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_Below we address all the comments by the reviewers. However, the figures that were used in our response are unfortunately not displayed in this format. _

Reviewer #1

Evidence, reproducibility and clarity

Thanks to the development of Ribo-Seq, translational buffering has been reported in the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. Although the authors' report provides a step forward in our understanding of translational buffering, this reviewer found a series of concerns in this paper. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

Major comments: 1. This paper heavily relies on the reference 18. However, this paper was not properly stated (no page or journal number); the study in Bioinformatics is nowhere to be found on the website, despite being out in 2024 apparently. Either title is wrong (yet a biorxiv can be found). This reviewer guessed that the reference 18 may be accepted. However, without a proper reference, this paper could not be judged since nearly all the parts of this work have been based on the reference 18. Also, the Ribobase data used in this manuscript comes from this reference, so it had better be well defined, especially when another Ribobase data set seems to be available online: http://www.bioinf.uni-freiburg.de/~ribobase/index.html

We apologize for the citation issue. This citation by Liu et al , 2024 (18) was a preprint from BioRxiv. This manuscript is now published in Nature Biotechnology. The reference has been updated in the revised version of the manuscript. The reference number in revised manuscript is Liu et al, 2025 (23).

In the Discussion, the authors mentioned "TE is based on a compositional regression model (18) rather than the commonly applied approach of using a logarithmic ratio of ribosome occupancy to mRNA abundance." This important information should be mentioned in the early section of the manuscript. Related to this, there are other published methods for exploring change in translation efficiency (e.g., 10.1093/bioinformatics/btw585; 10.1093/nar/gkz223) that could also be suitable in this context. It is not entirely clear if their approach is better than before. Again, the improper reference to 18 made our assessment of this work difficult.

We apologize and acknowledge the impact of the citation issue on this point. In Liu et al (2025), we have provided a comparison between our approach and the log-ratio strategy. We also agree that additional context was needed within the current study. Hence, we have now included more detailed information about the TE calculations in the initial results section (line 94).

As noted by the reviewer, several other methods have been developed previously for measuring changes in translation efficiency. These methods are designed to be used in cases of paired designs where there is a treatment or manipulation that is assayed along with controls. While these methods are highly valuable in assessing differential TE, they are unable to accommodate the type of meta-analyses described in our study. In particular, we do not report changes/differential TE with respect to a control sample but instead focus on the coordinated patterns of TE across experiments. We now note this important distinction in the manuscript in the discussion section (line 494).

The paper mainly relies on detecting a set of buffered genes using mRNA-TE correlation and MAD ratios (Ribo-Seq/RNA-Seq). While the concept seems sound, the authors should ensure that this method is reliable. Several controls could be used to confirm this. First, if any studies in humans or mice have described a set of genes as buffered, it would be worth checking for overlap between the authors' set of 'TB high' genes and the previously established list. Furthermore, the authors could use packages explicitly developed for translational buffering detection, such as annota2seq (https://academic.oup.com/nar/article/47/12/e70/5423604?login=true). Not all of the data used by the authors may be suitable for such packages, but the authors could at least partially use them on some of their datasets and see whether the buffered genes reported by these packages match their predictions.

We thank the reviewer for this constructive suggestion. To the best of our knowledge, no prior study in humans or mice has systematically analyzed translational buffering across a wide range of conditions. As a result, defining a gold-standard set for benchmarking is currently not feasible.

While packages such as anota2seq have proven highly valuable for identifying buffering effects in controlled experimental designs (e.g., comparing a treatment to a matched control), they are not readily applicable to the type of large-scale meta-analysis we present here.Our study integrates ribosome profiling and RNA-seq data across diverse datasets and conditions, which lies outside the design scope of such tools.

The most relevant point of comparison to our work is Wang et al. 2020 Nature, which examined a related but distinct form of translational buffering across species for a given tissue. We now present the overlap of genes identified as buffered in our study vs Wang et al. 2020. The details are presented in the reviewer's comment 5-2.

The threshold of 'TB high' or 'TB low' (top and bottom 250) is somewhat arbitrary. Why not top 100 or 500? The authors should provide a rationale for this choice. Also, they could include a numeric measure of buffering (the sum of the two rankings is probably suitable for this purpose). Several of the authors' explorations are suitable for numerical quantification (GO enrichment can be turned into GSEA, and the boxplot can be shown as correlations)

Thanks for these suggestions. We agree that the threshold used to define TB high and low are somewhat subjective. We ensure that changing this cutoff as suggested is easily achievable with the provided R script. These can be used to reproduce all of the reported analyses of translational buffering with different cutoffs.

To further assess whether our conclusions are robust to the selection of these thresholds, we tested several different values to define the TB high and TB low groups. As an example, we show here that the effect on protein variation and association of intrinsic features like the UTR lengths with the buffering potential of genes for different thresholds (i.e. if the TB high = top 100 or TB high = top 200) remain similar to the current cutoff of 250. However, if we increase the cutoff of TB high to 2000 and TB low to top 2000-4000 , the difference between the various features is diminished (Figure A& B). Further, protein variation (human cancer cell line and tissue) also becomes more similar across the three categories, possibly indicating a reduced regulatory potential of genes as their rank increases (Figure C& D).Our analyses reveal that highly ranked genes show associations with particular features, indicating an underlying hierarchy in translational buffering potential. This point is now discussed in the manuscript (line 177).

Legend: Effect of different thresholds on . A. Length features B. Median RNA expression C. Protein variation in human cancer cell line and D. on Primary human tissues

In response to the reviewer's suggestion of presenting data using numerical quantitation, we incorporated several additional inclusions in the manuscript.

1. We now report association of CDS / UTR length with translational buffering as a function of their translational buffering rank with highly ranked genes showing associations with particular features, indicating an underlying hierarchy in translational buffering potential (Sup Fig 3 A-B) Ii. We now include scatter plots which show that highly ranked genes have lower variation at the protein level in both cancer cell line and primary tissues (Sup Fig. 6 A-C).

Iii. We have now carried out modified GO enrichment analyses. Specifically, Gene Ontology enrichment analysis was performed for the TB high genes in humans and mouse using the clusterProfiler R package. Lists of TB high genes in human or mouse were analyzed against the Gene Ontology (GO) database using the enrichGO() function, with the organism-specific annotation database (org.Hs.eg.db for human or org.Mm.eg.db for mouse) as reference. Gene identifiers were supplied as gene symbols, and all genes in the current study were used as the background universe. Enrichment was carried out for the Biological Process (BP) ontology, with significance assessed by the hypergeometric test. P-values were adjusted for multiple testing using the Benjamini–Hochberg method, and terms with an adjusted p-value Legend: Gene Ontology (GO) enrichment analysis of the TB high gene set, performed with the clusterProfiler R package. Enriched GO Biological Process terms are shown after redundancy reduction using clusterProfiler::simplify. Each dot represents a GO term, with dot size indicating the number of genes associated with the term and color reflecting the adjusted p-value (Benjamini–Hochberg correction). Only the top non-redundant terms are displayed.

• *

Additionally, we performed Gene set enrichment analysis using the list of genes ordered according to their RNA-TE correlation. Hence lower ranks have lower RNA-TE correlations. The GSEA plots show significantly enriched Gene Ontology Biological Process (GO:BP) terms at the lower ranks of the ordered gene list. Together, these analyses further emphasize the observation that genes involved in macromolecular complexes are translationally buffered.

• *

Legend: Curves represent the enrichment score (ES) across the ranked gene list, with vertical bars indicating the positions of pathway-associated genes. The enrichment was identified using the gseGO() function from clusterProfiler.

Several of the statements of the authors in the Introduction or Discussion sections are not entirely true regarding the literature on the topics, or lack major papers on the topic, and therefore, they are a bit misleading. Among others, here are some:

We thank the reviewer for the suggestions and now have been incorporated in the revised manuscript, accordingly.

5-1 "In addition, genetic differences arising from aneuploidy, cell type differences or variability observed in the natural population can further determine the amplitude of variation (4-7). The effect of mRNA variation under these conditions is mostly reflected at the protein levels (2, 4-8).". Several recent or more ancient papers suggest that mRNA variation coming from aneuploidy, natural genetic variation, or CNV is buffered or not well reflected at the protein level: DOI: 10.1038/s41586-024-07442-9 DOI: 10.1073/pnas.2319211121 DOI: 10.1016/j.cels.2017.08.013 DOI: 10.15252/msb.20177548

We agree that mRNA variation coming from aneuploidy, natural genetic variation, or CNV is buffered or not well reflected at the protein level for some genes. This point has now been revised in the introduction. We have incorporated all the suggested literature into the revised manuscript (line 38).

5-2: The authors should also consider mentioning these studies and softening their initial statement. "Similarly, translational buffering of certain genes have been reported in mammalian cells, specifically under estrogen receptor alpha (ERα) depletion conditions (16).". Translational buffering has been deeply explored in mammalian tissues and even across several mammalian species in this study (DOI: 10.1038/s41586-020-2899-z). In this, the authors also provide a nice exploration of the gene characteristics that are associated with translational buffering. The authors should mention it and compare the study's findings to theirs ultimately.

We thank the reviewer for this suggestion. We have now cited the recommended study in the revised manuscript (line 65). Here, we provide a comparison of its findings with ours. While this related work offers important insights into translational buffering, its focus is on buffering across species within a given tissue, whereas our study emphasizes buffering across conditions, cell types, and treatments within a species. Despite this difference in focus, the comparison is highly informative, and we now highlight both the similarities and distinctions between the two studies in the relevant section of the revised manuscript.

Wang et al. calculate the variation at the transcriptome level vs at the translatome level and is represented as delta ∆ value for each gene. A lower value represents lower variation at the ribosome occupancy level than at the mRNA levels across various species. We classified the genes in the Wang et al study as TB high, TB low genes or others as identified in the current study while indicating the calculated delta ∆ from Wang et al. Many of the genes with a lower delta value (are delta ∆ Legend: A. Dot plot to highlight the delta value of all genes in the Wang et al study (also present in RiboBase) which are further grouped as TB high, low or others in (A) brain and (B) liver.

5-3: "Differences in species evaluated and statistical methods have resulted in conflicting interpretations (13, 28).". These conflicting results have been previously discussed in reviews on the topic that would be worth mentioning: DOI: 10.1016/j.cell.2016.03.014 DOI: 10.1038/s41576-020-0258-4

We have added these reviews at the appropriate location of the manuscript.

1. In addition to the p-values stated in the main text, the authors should annotate their plots when they find significant differences between groups to greatly facilitate the visual interpretation of the graphs.

We have now annotated many of the relevant graphs with p-values to facilitate visual interpretation, adding them where space and figure design allow.

Based on the data of Figure 4D, apparently, ribosome occupancy was not buffered even in high TB sets. The authors may argue that translational buffering may not cope with such a strong mRNA reduction. In that case, how big a difference in mRNA level does the buffering system adjust in protein synthesis? The authors should test gradual gene knockdown and/or overexpression and conduct Ribo-Seq/RNA-Seq to survey the buffering range.

We appreciate the reviewer’s suggestion regarding the experiment to determine the buffering range.To understand this for multiple genes, we attempted a series of knockdowns using CRISPR/gRNA approach using a MutiCas12a approach. We targeted 8 buffered and 2 non-buffered genes using a 10-plex crRNA along with 10-plex gRNA serving as a negative control (Figure below). The fold change at the mRNA level of the targeted gene was within the variation range observed in replicates for other non-targeted genes. The challenge in performing a gradual knockdown is the subtle changes in RNA expression falls within the margin of error of estimation, making it difficult to understand the clear implications of the mRNA levels on buffering. Hence, the precise experimental manipulation of mRNA expression levels that would be conducive to translational buffering remains highly technically challenging. As noted in our manuscript (Figure 4D), the conventional approaches for manipulation of transcript abundance lead to larger changes than typically observed as a result of natural variation.

*Legend: Validation of translational buffering by targeted knockdown of genes. A. The scatter plot shows the coefficient of variation of mRNA and ribosome occupancy between HEK293T cells targeted with sgRNA of different efficiencies. The genes indicated in blue are buffered and those in green are non buffered genes. B. The plot shows the fold change in mRNA abundance and ribosome occupancy as compared to cells that were infected with non-targeting crRNA array control (ratio of cpm in test vs control). Each color represents a gene and each point of a gene represents cells targeted by one of the four CRISPR arrays. *

"differential transcript accessibility model" could not be functional if mRNA is reduced beyond the accessible pool (i.e., less than the threshold, all the mRNAs are translated without buffering). The authors should carefully reconsider this model and the effective range of mRNAs.

We agree with the reviewer that according to the 'differential transcript accessibility model,' transcripts with abundances below a certain threshold should be completely accessible to the translational pool. Further, this could also be true for the other model, wherein initiation rate cannot increase beyond a particular threshold for transcripts of very low abundance. However, our observation from our haploinsufficiency analysis (Figure 4 B& C) and siRNA knockdown analysis from RiboBase (Figure 4 D) suggests that buffering might be possible within a given range of transcript abundance. Testing the buffering range by serial knockdowns might help in determining the threshold at which transcripts exhibit buffering. However, due to the challenges of serial knockdown as discussed above, makes this analysis difficult with Ribosome profiling and matched RNA-seq approach. An alternative approach could involve imaging translating and non-translating mRNA of buffered genes in different cells, which may help distinguish the two models. However, this falls outside the scope of the manuscript.

Minor comments:

1. Some figures are of poor quality as they seem to have points outside of the panel representations... Like Figure 3C, one point is out of the square, same for Figure 4E. Similarly, on figure 5F, some outliers seem to be clearly cut from the figure (maybe not, but then the author should put a larger space between the end of the figure and the max y points). Same for panel S2D and S6D, this does not sound so rigorous.

We agree and apologize for this issue. The axes of the figures have been annotated appropriately to indicate the presence of outliers in the figures.

1. There are several typos or weird sentences. Here are some (but maybe not all): 2-1: [...]with lower sums corresponding to higher final ranks. "two rankings". Based on these final ranks[...] 2-2: For each dataset, median absolute deviation (MAD) "i" protein abundance was calculated across samples 2-3: [...]neighbor method implemented in the MatchIT package (38) Differences in protein[...] a point is missing here. 2-4: Additionally a second dataset providing predictions of haploinsufficiency (pHaplo score) and triplosensitivity (pTriplo score) for all autosomal genes (25) was used to asses the distribution of these score"S" across buffered and non-buffered gene sets . There is a missing "s" at "score" and there is a space between the last word and the final point.

The necessary corrections have been incorporated in the revised version of the manuscript.

1. In the "Lymphoblastoid cell line data analysis:" section, this reviewer wonders why the authors used a different method to calculate buffering compared to before.

The main reason is the limited sample of the lymphoblastoid cell line data. In our larger analyses, we could use median absolute deviation as a robust metric of dispersion across heterogeneous samples. However, given the smaller dataset in that study we decided CV would be a better indicator of dispersion. To evaluate the potential for translational buffering of genes from RiboBase, we used two metrics. The first was the negative correlation between translation efficiency and RNA abundance across samples. The second metric relied on the ratio of variation in ribosome occupancy to variation in RNA levels. Given the limited sample size of the lymphoblastoid cell line dataset, we used the coefficient of variation (CV) instead of the median absolute deviation (MAD), as the data in this study were normalized using counts per million (CPM) rather than the centered log-ratio (clr) normalization used in RiboBase. This CV ratio allowed us to assess the effect of natural variation in RNA abundance on ribosome occupancy.

1. "Samples which had R2 less than 0.2 were removed as the residuals calculated for these samples could be unreliable". These samples for which the correspondence between RNA-Seq and Ribo-Seq is low wouldn't be the ones most impacted by translational buffering? Is it sure that the authors are not missing something here?

We agree with the reviewer that genes that show translational buffering may not conform to linear relationships between the two parameters. However, the proportion of genes exhibiting this buffering effect is not expected to significantly influence the overall regression fit. Instead, we hypothesized that low quality samples or truly different relationships between the two parameters can make this relationship nonlinear, rendering it unsuitable for linear regression analysis for calculation of TE.

To address these possibilities, we first analysed a commonly used proxy for data quality. Given the characteristic movement of ribosomes across mRNAs, periodicity of sequencing reads is a useful metric to assess whether reads are randomly fragmented, as in RNA-seq, or specifically represent ribosome-protected footprints. For this, we compared two groups: samples that were removed (~30) and those retained for analysis. We plotted the distribution of periodicity scores for all samples in both groups. For the calculation of periodicity scores, first the percentage of reads mapped to the dominant frame position across the dynamic ribosome footprint read length range was calculated for each sample. The periodicity score was calculated by taking the weighted sum of these dominant percentages, with weights based on the total read counts at each length.

The results indicate that the removed samples did not have lower periodicity scores, suggesting that their quality in terms of periodicity was comparable to the retained samples.

        To assess the second possibility, we checked if the study involved major perturbations, which may skew the relationship towards non linearity. The 30 samples that were removed came from 14 unique studies, 18 of which involved perturbation which possibly affected either of the two parameters. In addition to the genetic/pharmacological perturbations specific to the study, the overall conditions of the cells during an experiment could influence this relationship. Another point to note is that many of the filtered-out samples are HeLa and HEK293T cells, which show a normal relationship between ribosome occupancy and RNA abundance for the majority of cases.

        These considerations suggest that removing these samples is most appropriate, as their inclusion could bias the TE calculations.

For Figure 4B and 4C, the authors should provide statistical tests and p-values to confirm the observed trends.

The haploinsufficiency and triplosensitivity analyses are now supported by a chi-squared test. The details of the statistical test are now mentioned in the text and the p-values have been noted on the respective figures.

In Figure 2A, the "all genes" color doesn't correspond to the point color.

The color in the figure has been modified in the revised version of the manuscript.

1. "To understand if codon usage patterns are[...]". This comes slightly out of the blue. The authors could maybe explain why codon usage should be explored for translational buffering. The authors should cite recent key works in the fields: DOI: 10.1016/j.celrep.2023.113413 DOI: 10.1101/2023.11.27.568910

We would like to thank the reviewer for their suggestion. The references have been incorporated in the revised version of the manuscript. We have now explained why codon usage could be a contributor in determining the translational buffering potential (line 190).

"The change in each metric was calculated by subtracting the mean value in the control samples from that in the knockdown samples. This yielded the differential mRNA abundance and ribosome occupancy resulting from gene knockdown.". This looks statistically weak. The authors should consider using more robust methods like DESeq.

We thank the reviewer for the suggestion. We reanalyzed the selected studies using edgeR and the modified figure is included in the revised version of the manuscript (Figure 4D). The conclusion after this analysis remains essentially the same. In particular, translational buffering is ineffective when mRNA abundance is perturbed drastically. Additionally, the limited number of experiments with direct perturbation of buffered genes limit the generalizability of this observation. This limitation is included in the result section (line 342).

Legend: Scatter plot represents log2 fold change in RNA abundance and ribosome occupancy. Each point represents a gene and the fold change in its RNA and ribosome occupancy with respect to their controls. The line represents the line of equivalence. Buffered genes do not show less change in ribosome occupancy upon reduction in their RNA levels than other genes.

1. "Genes in the buffered gene set had a higher codon adaptation index than the non-buffered set, indicating that candidates in the buffered gene set are relatively well expressed due to the presence of a higher proportion of the codons observed in highly expressed genes". What do the authors mean by "relatively well expressed"? Abundantly expressed? This sentence and the causality under it is unclear and should be modified or better explained.

We thank the reviewer for pointing out the lack of clarity in the sentence. We have now quantitatively measured the CAI in the three categories and modified the sentence to better explain the rationale in the revised version (line 183). “To understand if codon usage patterns are associated with translational buffering, we next analyzed codon properties across buffered and non-buffered human gene sets. The codon adaptation index quantifies how closely a gene’s codon usage aligns with that of highly expressed genes. Genes in the buffered gene set had a higher codon adaptation index than the non-buffered set. Specifically, 28.4% of TB high genes, 14% of TB low genes and 9.3% of genes in the other category fall within the top decile (>90th percentile) of codon adaptation index.”

The panel 4D is unclear. Is one point associated with one gene? Or is it the average of several genes? If it's one point for one gene, it is important to clearly state it because the number of cases is therefore quite low, especially for the TB high and low.

Each point and line are associated with a single gene. This is now clarified in the legend of the figure (line 364). The number of genes in this analysis is limited to the available ribosome profiling data with gene knockdown experiments.

1. In Figure 2J, GGU (Gly), AAG (Lys), and ACU (Arg) provide negative effects on prediction, although these were enriched in the high TB set (Figure 2E). This contradiction should be explained.

While this appears to be a seeming contradiction, it is in line with what we expected. In particular, the objective of Figure 2J is to illustrate the features that predict the mRNA–TE correlation of genes, as identified using a LGBM model. The Spearman correlation shown reflects the relationship between each feature and the mRNA–TE correlation values. A negative correlation for codons such as GGU (Gly), AAG (Lys), and ACU (Thr) suggests that enrichment of these codons is associated with lower mRNA–TE correlation. This is in agreement with our observation in Figure 2E which suggests that high TB genes are enriched in these codons. In contrast, transcript size exhibits a positive correlation, indicating that shorter transcripts tend to have lower mRNA–TE correlation values.

Given that the choice of colors is a potential source of confusion, we have revised the text (line 230) and the figure (& legend) to try to clarify this relationship.

The subtitle of "Translationally buffered genes exhibit variable association kinetics with the translational machinery in response to mRNA variation" sounds unfair to this reviewer. Since the authors did not work on kinetics directly, the use of this word is misleading.

We agree and revised the subtitle to “The association of translationally buffered genes with the translational machinery varies in response to changes in mRNA abundance"

1. The explanation of Figure 5A "We next explored the potential mechanisms that may give rise to translational buffering. Specifically, we considered two non-mutually exclusive models by which mRNA abundance might be decoupled from ribosome occupancy. In the first, the "differential transcript accessibility model", mRNA abundance determines the fraction of transcripts that are accessible to the translational pool. In this scenario, an increase in mRNA abundance would be accompanied by a proportionally smaller increase in the fraction of transcripts entering the translating pool for buffered genes, compared to non-buffered genes. In the second, the "initiation rate model", the rate of translation initiation per transcript scales inversely with mRNA abundance. Under this model, the proportion of mRNA entering the translational pool would be comparable across buffered and non-buffered genes (Fig 5A)." is hard to understand. The authors should rewrite for a better understanding of the readers.

This section has been rewritten in the revised version of the manuscript. The text now reads as

“We next explored the potential mechanisms that may give rise to translational buffering. Specifically, we considered two non-mutually exclusive models by which mRNA abundance might be decoupled from ribosome occupancy. In the first, the “differential transcript accessibility model”, mRNA abundance determines the fraction of transcripts that are accessible to the translational pool. In this scenario, an increase in mRNA abundance would be accompanied by a proportionally smaller increase in the fraction of transcripts entering the translating pool for buffered genes, compared to non-buffered genes. In the second, the “initiation rate model”, the rate of translation initiation per transcript scales inversely with mRNA abundance. Under this model, as mRNA abundance increases, translation initiation on each transcript is reduced, thereby lowering the number of ribosomes per transcript. However, this mechanism allows a proportional increase in transcripts entering the translational pool for buffered genes, similar to non-buffered genes”

Significance

Thanks to the development of Ribo-Seq, translational buffering has been reported in various works. However, the systematic investigation has remained challenging. Employing the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. A group of mRNAs whose expression variance is buffered at the translation level was comprehensively surveyed in humans and mice. The authors found a series of features in the translationally buffered genes, including high GC contents in the 5′ UTR, optimal codon usage, and mRNA length. The depletion or increase of one allele of the genes in the group may be particularly detrimental to cells. The authors' report provides a step forward in our understanding of translational buffering, appealing to the broad scientific community in basic and applied biology. However, this reviewer found a series of concerns in this paper, including clarity in the methods, experimental validation, referring the earlier works, etc. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

We thank the reviewer for noting the significance of the work and for their constructive feedback.

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

In this manuscript, Rao and colleagues present a comprehensive analysis of translational buffering in human and mouse by mining 1515 matched ribosome profiling and RNAseq datasets from diverse tissues and cell lines. They define translational buffering as genes whose TE is negatively correlated with mRNA abundance across conditions, and further identify candidates by comparing median absolute deviations of ribosome occupancy versus mRNA levels. The authors find a conserved set of buffered genes enriched for components of multiprotein complexes, demonstrate that buffered genes exhibit lower protein variability and greater dosage sensitivity, and propose two non-mutually exclusive mechanistic models (differential accessibility and initiation rate modulation). Finally, they perform complementary fractionation experiments in HEK293T cells to support these models.

These findings propose a novel, conserved mechanism of translational buffering that tunes gene expression in mouse and human, showing how intrinsic sequence features and cellular context cooperate to stabilize protein output across diverse conditions. However, further evidence is required to fully support the authors conclusions, particularly direct validation of the proposed models of buffering.

We thank the reviewer for their positive assessment and thoughtful suggestions that we address below.

Below are my main concerns:

1. The choice of the top 250 genes by spearman correlation and MAD ratio as "TB high" seems arbitrary. The authors should justify these cut offs (via permutation analysis or FDR control) and show that conclusions are robust to different thresholds.

We agree that the threshold used to define TB high and TB low is somewhat subjective, and we now clearly acknowledge this in the discussion section (line 485). We now provide an R script that reproduces all analyses of translational buffering, where changing this cutoff to higher or lower values is straightforward.

To ensure the robustness of our conclusions, we evaluated several thresholds for defining TB high and TB low. We observed that the conclusions hold within a reasonable range of values (100-250). For example, the effects on protein variation and the association of intrinsic features such as UTR lengths with buffering potential remain consistent when TB high is defined as the top 100 or the top 200 genes, compared with the current cutoff of 250. In contrast, when we define TB high as the top 2000 and TB low as ranks 2000–4000, the difference between the various features is diminished (Figure A& B). Further, protein variation (human cancer cell line and tissue) also becomes more similar across the three categories, possibly indicating a reduced regulatory potential of genes as their rank increases (Figure C& D). Our results show that highly ranked genes consistently associate with specific features, suggesting an underlying hierarchy in translational buffering potential.

Legend: Effect of different thresholds on . A. Length features B. Median RNA expression C. Protein variation in human cancer cell line and D. on Primary human tissues

The modified compositional regression approach for TE and imputation of missing values are central to the study, but details are relegated to supplemental methods. The manuscript would benefit from a clear comparison of this method against standard log-ratio TE estimates, including sensitivity analyses to missing-data imputation strategies

We thank the reviewer for the feedback. We have now added further description of the modified compositional regression and the imputation strategy in the results section (line 94). Comparison to standard log-ratio TE estimates and their limitations has already been detailed in Liu et al. 2025, Nature Biotechnology. Therefore, in the current manuscript we specifically focus on the effect of the imputation strategy.

        Specifically, the modified imputation slightly improved concordance between the set of genes that are identified to be translationally buffered using the negative RNA-TE relationship or using RNA -Ribosome occupancy correlation (0.91 to 0.94). Further, we assessed the correlation between TE and protein abundance as measured by mass spectrometry from seven human cell lines (A549, HEK293, HeLa, HepG2, K562, MCF7 and U2OS). The protein measurements were obtained from PaxDb. The new imputation strategy slightly increased mean correlation between the TE and proteome abundance as compared to naive strategy. It specifically showed improved correlation for HepG2, A549 and HeLa cell lines. 3507 genes were used for this analysis that were common between PaxDb, Liu et al., 2005 and the current study.

Legend: Proteomics vs TE correlation of cell types without or with imputation strategy. Spearman correlation between compositional TE calculated as calculated by Liu et al., 2025 from 68 samples from 11 studies (HEK293), 86 samples from 10 studies (HeLa), 58 samples from four studies (U2OS), 29 samples from five studies (A549), five samples from two studies (MCF7), seven samples from two studies (K562) and 10 samples from two studies (HepG2) or from the current study. 57 samples from 10 studies (HEK293), 82 samples from 9 studies (HeLa), 58 samples from four studies (U2OS), 29 samples from five studies (A549), 5 samples from two studies (MCF7), one samples from one studies (K562) and 9 samples from two studies (HepG2) . 3507 genes were used for this analysis that were common between Paxdb, Liu et al., 2005 and the current study.

Human data are derived mainly from immortalized cell lines, whereas mouse data are from primary tissues. Pooling these heterogeneous sources may conflate cell type-specific regulation with intrinsic buffering. The authors should either stratify analyses by context or demonstrate buffering signatures remain consistent within more homogeneous subsets

We thank the reviewer for the suggestion and agree that heterogeneity could potentially mask cell type-specific buffering effects. The TB-high genes we report are those that show consistent and robust expression across diverse contexts. However, unlike RNA-seq datasets, the current number of ribosome profiling samples per cell type is still limited, and a more comprehensive assessment of context-specific buffering will require larger datasets that will accumulate over time.

Nonetheless, we have stratified the analysis by cellular context. Specifically, we grouped samples of the same cell-type and repeated the buffering analysis. We provide a new table listing TB-ranks of genes for the five cell types with the largest sample sizes as a table in github.

https://github.com/CenikLab/Translational-buffering/blob/Translational-Buffering/combined_tables.xlsx

As an additional control, we compared buffering patterns between related and unrelated cell lines. For example, the correlation of TB ranks between related cell lines HEK293T (n = 98) and HEK293 (n = 57) is higher (0.46) than between either and an unrelated cell line, HeLa (n = 82). Similarly, the correlation between two liver cell lines, Huh7 (n = 39) and HepG2 (n = 9), is higher (0.20) than between Huh7 and a similarly sampled but unrelated lymphoblastoid cell line (LCL, n = 9; correlation = 0.05). While these analyses suggest that cell type-specific patterns may exist, their exploration is currently limited by sample size, as detecting buffering requires substantial variability in mRNA expression. We now highlight this as a limitation in the Discussion section (line 573).

*Legend: Spearman correlation between TB ranks of different pairs of cell lines. The first set indicates comparison with HEK293T. The second set indicates comparison between liver cells (HepG2 and Huh 7). *

The HEK293T fractionation experiments offer preliminary support for both the "accessibility" and "initiation" models, but only slope analyses are shown. To validate these models, the authors should perform targeted reporter assays (dual luciferase constructs with 5′UTR swaps) or manipulations of initiation factors (eIF4E knockdown) to directly test how transcript abundance alters initiation rates versus pool entry

We thank the reviewer for suggesting experiments to validate the proposed models. In the luciferase reporter experiments, constructs bearing the endogenous UTRs from non-buffered genes would be expected to result in expression that is proportional to transcript abundance. In contrast, swapping a 5’ UTR from buffered genes would mitigate this effect of translation buffering via “initiation rate model” depending on the 5 UTR sequence of transcript. However, as outlined below, this experiment has important caveats:

1. Role of coding sequence: Such assays primarily test the contribution of the 5′UTR and do not address potential cooperative effects between the 5′UTR and the coding sequence (CDS). Thus, if 5′UTRs fails to recapitulate translational buffering, it would be unclear whether the buffering requires coordinated action of the 5′UTR and CDS or whether the gene in question simply does not conform to the initiation-rate model.
2. Sensitivity of measurements: Reporter-based measurements often rely on RT-qPCR to quantify expression changes. While suitable for large fold-changes, small shifts may fall within the assay’s technical margin of error, limiting the interpretability of the results. iii. Gene-to-gene variability: Buffered and non-buffered transcripts likely span a wide range of intrinsic initiation rates. Selecting only a few “representative” transcripts for 5′UTR swapping could yield results that are not broadly generalizable.

Similarly, knockdown of general initiation factors will likely impact on both buffered and non-buffered genes, which could limit the ability to distinguish the effect of transcript abundance on translational buffering via either of the proposed models. We envision an alternative future approach that would involve single molecule imaging translating and non-translating mRNAs of buffered and non-buffered genes under varying abundance conditions in a physiological context. Such experiments are likely the most suitable for disentangling the contributions of accessibility versus initiation. While we find this an exciting direction for future work, it lies beyond the scope of the present manuscript.

The conclusion that buffering reduces protein variability relies on mass-spec comparisons, but ribosome occupancy does not always reflect functional protein output (due to elongation stalling or co-translational degradation). Incorporating orthogonal measures, such as pulse-labeling or western blots for key buffered versus non-buffered genes, would strengthen the link between buffering and proteome stability

We agree with the reviewer’s concern and have been acknowledged as a limitation in the discussion section. To address this with orthogonal approaches, we carried out several additional experiments. Specifically, we identified a study from RiboBase (GSE132703) that exhibited significant variation in FUS transcript (a translationally buffered gene) abundance across conditions—namely HEK293T wild type, LARP1A single knockout (SKO), and LARP1A/B double knockout (DKO) using their RNA-seq data. We reached out to the authors of the study and obtained these knockout cell lines. We reanalyzed RNA abundance under the different conditions by RT-qPCR and assessed protein levels by Western blot. Despite observing differences in RNA abundance, FUS protein levels did not exhibit corresponding change at the protein level.

We also selected a non-buffered gene; DNAJC6, that also showed RNA-level differences. However, the change in RNA expression was not consistent at the protein level. Some caveats of Western blot is its limited sensitivity which may prevent detection of subtle changes and that the measurements are steady-state protein levels which cannot resolve whether differences arise from altered synthesis or degradation.

*Legend : Validation of buffering gene by western blot: A. Plot showing the RNA abundance and ribosome occupancy of buffered gene ; FUS and non buffered genes; DNAJC6 with variation in HEK293T-wild type, LARP1A single knockout and LARP1A/B double knockout. B. Validation of the RNA seq data by qPCR. C. Western Blot showing the FUS, DNAJC6 and Actin in wild type and different mutants. D. Bar plot showing the quantification of western blot. *

        In addition to this targeted analysis , we performed quantitative mass spectrometry to evaluate the effect of mRNA variation at the protein level at global scale.

LC MS/MS analysis was performed on the above samples in triplicates at the Proteomics facility of the University of Texas. A total of 4,048 proteins were identified using a peptide confidence threshold of 95% and a protein confidence threshold of 99%, with a minimum of two peptides required for identification. Total precursor intensities for all peptides of a protein was summed and was used for protein quantification using DEP (Differential Enrichment of Proteomics Analysis) Package, in Bioconductor, R (https://rdrr.io/bioc/DEP/man/DEP.html). DEP was used for variance normalization and statistical testing of differentially expressed proteins. As expected LARP1 protein was identified in the control cells but not in the single or double knockouts.

We then plotted the fold change in RNA as determined by edgeR analysis of RNA-seq from (Philippe et al. 2020) and the fold change in protein abundance from our mass spectrometry data. We observed that genes in the TB high group show reduced changes at the protein level compared to TB low or others as determined by the linear regression analysis in both single and double LARP1 KO mutants. This finding is consistent with our findings that buffered genes show lower variation in the protein abundance in response to change in mRNA expression.

Legend: Scatter plot showing the log2fold change in the RNA and protein levels as determined by RNA seq from (Philippe et al. 2020) or mass spectroscopy. Differential analysis of RNA was done using the edgeR package and the DEP (Differential Enrichment of Proteomics Analysis) Package *was used for mass spectrometry analysis. Only genes with an FDR We have not included this data in the manuscript given the deviation of the approach from our original analysis, but we are happy to reconsider the inclusion of this data to supplement our proteomic analysis.

While the LGBM modeling shows modest predictive power of sequence features alone, the manuscript stops short of exploring what cellular factors might drive context dependence. Integrating public datasets on RNA-binding protein expression or mTOR pathway activity across samples could illuminate trans-acting determinants of buffering and move beyond correlative sequence analyses,

We thank the reviewer for this suggestion. To investigate potential trans-acting determinants of buffering, we focused on 1,394 human RBPs as classified by Hentze et al. (2018), reasoning that some of these factors may facilitate translational buffering. Specifically, we examined correlations between the RNA expression of each RBP and the TE of all other genes across samples. p-values were corrected using the Bonferroni procedure. For each RBP, we then performed a Fisher’s exact test to assess whether the number of significant correlations was enriched among buffered versus non-buffered genes.

This analysis revealed that the expression levels of many RBPs are significantly enriched for either positive or negative correlations with the TE of buffered genes. In particular, we note that RNA expression of many buffered RBPs is enriched for negative correlations with the TE of other buffered transcripts. These results suggest that, rather than considering translational buffering in isolation for each transcript, buffering effects may be coordinated at the translational level and influenced by shared trans-acting factors such as RBPs. Network-based approaches have been valuable for RNA co-expression and are only now being applied to TE covariation. However, the correlative nature of these analyses limits causal inference. For example, although many ribosomal proteins appear to influence the buffering of other ribosomal proteins, they themselves may be regulated by a non-ribosomal RBP—so the apparent effects could reflect upstream regulatory influences. This analysis is now included as a supplementary figure (Sup. Fig. 5) of the revised manuscript.

Legend: A scatter plot of odds ratio log₂ of number of significant correlations (RNA abundance of RBPs ::TE of genes) and the p value from fisher test. The vertical dashed line represents the threshold odds ratio, above which RBPs exhibit a higher number of significant correlations with buffered genes. P values were corrected using Bonferroni procedure* and the horizontal dashed line represents the adjusted p value cutoff. *

Reviewer #2 (Significance (Required)):

Overall, this manuscript leverages an unprecedented compendium of matched ribosome profiling and RNAseq datasets across human cell lines and mouse tissues, combined with improved TE estimation, to robustly catalog genes exhibiting translational buffering, a clear methodological and conceptual strength. The main limitations stem from heterogeneous sample sources, largely correlative analyses, and a lack of targeted mechanistic validation. Compared to prior yeast focused studies, it fills a key gap by demonstrating conservation of buffering in mammals and linking it to dosage sensitivity and protein stability, representing a conceptual advance in understanding post-transcriptional homeostasis and a methodological step forward in TE analysis. This work will interest researchers in RNA biology, gene expression regulation, systems biology, and cancer proteomics, as well as those studying dosage-sensitive pathways and translational control. My expertise is on translational control in cancer.

We thank the reviewer for noting the broader significance of the work and for their constructive feedback.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Rao and colleagues present a comprehensive analysis of translational buffering in human and mouse by mining 1515 matched ribosome profiling and RNAseq datasets from diverse tissues and cell lines. They define translational buffering as genes whose TE is negatively correlated with mRNA abundance across conditions, and further identify candidates by comparing median absolute deviations of ribosome occupancy versus mRNA levels. The authors find a conserved set of buffered genes enriched for components of multiprotein complexes, demonstrate that buffered genes exhibit lower protein variability and greater dosage sensitivity, and propose two non-mutually exclusive mechanistic models (differential accessibility and initiation rate modulation). Finally, they perform complementary fractionation experiments in HEK293T cells to support these models.

These findings propose a novel, conserved mechanism of translational buffering that tunes gene expression in mouse and human, showing how intrinsic sequence features and cellular context cooperate to stabilize protein output across diverse conditions. However, further evidence is required to fully support the authors conclusions, particularly direct validation of the proposed models of buffering. Below are my main concerns:

1. The choice of the top 250 genes by spearman correlation and MAD ratio as "TB high" seems arbitrary. The authors should justify these cut offs (via permutation analysis or FDR control) and show that conclusions are robust to different thresholds
2. The modified compositional regression approach for TE and imputation of missing values are central to the study, but details are relegated to supplemental methods. The manuscript would benefit from a clear comparison of this method against standard log-ratio TE estimates, including sensitivity analyses to missing-data imputation strategies
3. Human data are derived mainly from immortalized cell lines, whereas mouse data are from primary tissues. Pooling these heterogeneous sources may conflate cell type-specific regulation with intrinsic buffering. The authors should either stratify analyses by context or demonstrate buffering signatures remain consistent within more homogeneous subsets
4. The HEK293T fractionation experiments offer preliminary support for both the "accessibility" and "initiation" models, but only slope analyses are shown. To validate these models, the authors should perform targeted reporter assays (dual luciferase constructs with 5′UTR swaps) or manipulations of initiation factors (eIF4E knockdown) to directly test how transcript abundance alters initiation rates versus pool entry
5. The conclusion that buffering reduces protein variability relies on mass-spec comparisons, but ribosome occupancy does not always reflect functional protein output (due to elongation stalling or co-translational degradation). Incorporating orthogonal measures, such as pulse-labeling or western blots for key buffered versus non-buffered genes, would strengthen the link between buffering and proteome stability
6. While the LGBM modeling shows modest predictive power of sequence features alone, the manuscript stops short of exploring what cellular factors might drive context dependence. Integrating public datasets on RNA-binding protein expression or mTOR pathway activity across samples could illuminate trans-acting determinants of buffering and move beyond correlative sequence analyses

Significance

Overall, this manuscript leverages an unprecedented compendium of matched ribosome profiling and RNAseq datasets across human cell lines and mouse tissues, combined with improved TE estimation, to robustly catalog genes exhibiting translational buffering, a clear methodological and conceptual strength. The main limitations stem from heterogeneous sample sources, largely correlative analyses, and a lack of targeted mechanistic validation. Compared to prior yeast focused studies, it fills a key gap by demonstrating conservation of buffering in mammals and linking it to dosage sensitivity and protein stability, representing a conceptual advance in understanding post-transcriptional homeostasis and a methodological step forward in TE analysis. This work will interest researchers in RNA biology, gene expression regulation, systems biology, and cancer proteomics, as well as those studying dosage-sensitive pathways and translational control. My expertise is on translational control in cancer.

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Referee #1

Evidence, reproducibility and clarity

Thanks to the development of Ribo-Seq, translational buffering has been reported in various works. However, the systematic investigation has remained challenging. Employing the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. Although the authors' report provides a step forward in our understanding of translational buffering, this reviewer found a series of concerns in this paper. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

Major comments:

1. This paper heavily relies on the reference 18. However, this paper was not properly stated (no page or journal number); the study in Bioinformatics is nowhere to be found on the website, despite being out in 2024 apparently. Either title is wrong (yet a biorxiv can be found). This reviewer guessed that the reference 18 may be accepted. However, without a proper reference, this paper could not be judged since nearly all the parts of this work have been based on the reference 18. Also, the Ribobase data used in this manuscript comes from this reference, so it had better be well defined, especially when another Ribobase data set seems to be available online: http://www.bioinf.uni-freiburg.de/~ribobase/index.html
2. In the Discussion, the authors mentioned "TE is based on a compositional regression model (18) rather than the commonly applied approach of using a logarithmic ratio of ribosome occupancy to mRNA abundance." This important information should be mentioned early section of the manuscript. Related to this, there are other published methods for exploring change in translation efficiency (e.g., 10.1093/bioinformatics/btw585; 10.1093/nar/gkz223) that could also be suitable in this context. It is not entirely clear if their approach is better than before. Again, the improper reference to 18 made our assessment of this work difficult.
3. The paper mainly relies on detecting a set of buffered genes using mRNA-TE correlation and MAD ratios (Ribo-Seq/RNA-Seq). While the concept seems sound, the authors should ensure that this method is reliable. Several controls could be used to confirm this. First, if any studies in humans or mice have described a set of genes as buffered, it would be worth checking for overlap between the authors' set of 'TB high' genes and the previously established list. Furthermore, the authors could use packages explicitly developed for translational buffering detection, such as annota2seq (https://academic.oup.com/nar/article/47/12/e70/5423604?login=true). Not all of the data used by the authors may be suitable for such packages, but the authors could at least partially use them on some of their datasets and see whether the buffered genes reported by these packages match their predictions.
4. The threshold of 'TB high' or 'TB low' (top and bottom 250) is somewhat arbitrary. Why not top 100 or 500? The authors should provide a rationale for this choice. Also, they could include a numeric measure of buffering (the sum of the two rankings is probably suitable for this purpose). Several of the authors' explorations are suitable for numerical quantification (GO enrichment can be turned into GSEA, and the boxplot can be shown as correlations)
5. Several of the statements of the authors in the Introduction or Discussion sections are not entirely true regarding the literature on the topics, or lack major papers on the topic, and therefore, they are a bit misleading. Among others, here are some:

5-1 "In addition, genetic differences arising from aneuploidy, cell type differences or variability observed in the natural population can further determine the amplitude of variation (4-7). The effect of mRNA variation under these conditions is mostly reflected at the protein levels (2, 4-8).". Several recent or more ancient papers suggest that mRNA variation coming from aneuploidy, natural genetic variation, or CNV is buffered or not well reflected at the protein level:

DOI: 10.1038/s41586-024-07442-9 DOI: 10.1073/pnas.2319211121 DOI: 10.1016/j.cels.2017.08.013 DOI: 10.15252/msb.20177548

5-2: The authors should also consider mentioning these studies and softening their initial statement. "Similarly, translational buffering of certain genes have been reported in mammalian cells, specifically under estrogen receptor alpha (ERα) depletion conditions (16).". Translational buffering has been deeply explored in mammalian tissues and even across several mammalian species in this study (DOI: 10.1038/s41586-020-2899-z). In this, the authors also provide a nice exploration of the gene characteristics that are associated with translational buffering. The authors should mention it and compare the study's findings to theirs ultimately.

5-3: "Differences in species evaluated and statistical methods have resulted in conflicting interpretations (13, 28).". These conflicting results have been previously discussed in reviews on the topic that would be worth mentioning: DOI: 10.1016/j.cell.2016.03.014 DOI: 10.1038/s41576-020-0258-4 6. In addition to the p-values stated in the main text, the authors should annotate their plots when they find significant differences between groups to greatly facilitate the visual interpretation of the graphs. 7. Based on the data of Figure 4D, apparently, ribosome occupancy was not buffered even in high TB sets. The authors may argue that translational buffering may not cope with such a strong mRNA reduction. In that case, how big a difference in mRNA level does the buffering system adjust in protein synthesis? The authors should test gradual gene knockdown and/or overexpression and conduct Ribo-Seq/RNA-Seq to survey the buffering range. 8. "differential transcript accessibility model" could not be functional if mRNA is reduced beyond the accessible pool (i.e., less than the threshold, all the mRNAs are translated without buffering). The authors should carefully reconsider this model and the effective range of mRNAs.

Minor comments:

1. Some figures are of poor quality as they seem to have points outside of the panel representations... Like Figure 3C, one point is out of the square, same for Figure 4E. Similarly, on figure 5F, some outliers seem to be clearly cut from the figure (maybe not, but then the author should put a larger space between the end of the figure and the max y points). Same for panel S2D and S6D, this does not sound so rigorous.
2. There are several typos or weird sentences. Here are some (but maybe not all):

2-1: [...]with lower sums corresponding to higher final ranks. "two rankings". Based on these final ranks[...]

2-2: For each dataset, median absolute deviation (MAD) "i" protein abundance was calculated across samples

2-3: [...]neighbor method implemented in the MatchIT package (38) Differences in protein[...] a point is missing here.

2-4: Additionally a second dataset providing predictions of haploinsufficiency (pHaplo score) and triplosensitivity (pTriplo score) for all autosomal genes (25) was used to asses the distribution of these score"S" across buffered and non-buffered gene sets . There is a missing "s" at "score" and there is a space between the last word and the final point. 3. In the "Lymphoblastoid cell line data analysis:" section, this reviewer wonders why the authors used a different method to calculate buffering compared to before. 4. "Samples which had R2 less than 0.2 were removed as the residuals calculated for these samples could be unreliable". These samples for which the correspondence between RNA-Seq and Ribo-Seq is low wouldn't be the ones most impacted by translational buffering? Is it sure that the authors are not missing something here? 5. For Figure 4B and 4C, the authors should provide statistical tests and p-values to confirm the observed trends. 6. In Figure 2A, the "all genes" color doesn't correspond to the point color. 7. "To understand if codon usage patterns are[...]". This comes slightly out of the blue. The authors could maybe explain why codon usage should be explored for translational buffering. The authors should cite recent key works in the fields: DOI: 10.1016/j.celrep.2023.113413 DOI: 10.1101/2023.11.27.568910 8. "The change in each metric was calculated by subtracting the mean value in the control samples from that in the knockdown samples. This yielded the differential mRNA abundance and ribosome occupancy resulting from gene knockdown.". This looks statistically weak. The authors should consider using more robust methods like DESeq. 9. "Genes in the buffered gene set had a higher codon adaptation index than the non-buffered set, indicating that candidates in the buffered gene set are relatively well expressed due to the presence of a higher proportion of the codons observed in highly expressed genes". What do the authors mean by "relatively well expressed"? Abundantly expressed? This sentence and the causality under it is unclear and should be modified or better explained. 10. The panel 4D is unclear. Is one point associated with one gene? Or is it the average of several genes? If it's one point for one gene, it is important to clearly state it because the number of cases is therefore quite low, especially for the TB high and low. 11. In Figure 2J, GGU (Gly), AAG (Lys), and ACU (Arg) provide negative effects on prediction, although these were enriched in the high TB set (Figure 2E). This contradiction should be explained. 12. The subtitle of "Translationally buffered genes exhibit variable association kinetics with the translational machinery in response to mRNA variation" sounds unfair to this reviewer. Since the authors did not work on kinetics directly, the use of this word is misleading. 13. The explanation of Figure 5A "We next explored the potential mechanisms that may give rise to translational buffering. Specifically, we considered two non-mutually exclusive models by which mRNA abundance might be decoupled from ribosome occupancy. In the first, the "differential transcript accessibility model", mRNA abundance determines the fraction of transcripts that are accessible to the translational pool. In this scenario, an increase in mRNA abundance would be accompanied by a proportionally smaller increase in the fraction of transcripts entering the translating pool for buffered genes, compared to non-buffered genes. In the second, the "initiation rate model", the rate of translation initiation per transcript scales inversely with mRNA abundance. Under this model, the proportion of mRNA entering the translational pool would be comparable across buffered and non-buffered genes (Fig 5A)." is hard to understand. The authors should rewrite for a better understanding of the readers.

Significance

Thanks to the development of Ribo-Seq, translational buffering has been reported in various works. However, the systematic investigation has remained challenging. Employing the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. A group of mRNAs whose expression variance is buffered at the translation level was comprehensively surveyed in humans and mice. The authors found a series of features in the translationally buffered genes, including high GC contents in the 5′ UTR, optimal codon usage, and mRNA length. The depletion or increase of one allele of the genes in the group may be particularly detrimental to cells. The authors' report provides a step forward in our understanding of translational buffering, appealing to the broad scientific community in basic and applied biology. However, this reviewer found a series of concerns in this paper, including clarity in the methods, experimental validation, referring the earlier works, etc. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

SECTION A - Evidence, Reproducibility, and Clarity Summary The study investigates the neurodevelopmental impact of trisomy 21 on human cortical excitatory neurons derived from induced pluripotent stem cells (hiPSCs). Key findings include a modest reduction in spontaneous firing, a marked deficit in synchronized bursting, decreased neuronal connectivity, and altered ion channel expression-particularly a downregulation of voltage‐gated potassium channels and HCN1. These conclusions are supported by a combination of in vitro calcium imaging, electrophysiological recordings, viral monosynaptic tracing, RNA sequencing, and in vivo transplantation with two‐photon imaging.

Major Comments • Convincing Nature of Key Conclusions: The study's conclusions are generally well supported by a diverse set of experimental approaches. However, certain claims regarding the intrinsic properties of the excitatory network would benefit from further qualification. In particular, the assertion that reduced synchronization is solely attributable to altered ion channel expression might be considered somewhat preliminary without additional corroborative experiments.

1.1) We agree with the reviewer and now write in the abstract: 'Together, these findings demonstrate long-lasting impairments in human cortical excitatory neuron network function associated with Trisomy 21 .' And in the Introduction: 'Collectively, the observed changes in ion channel expression, neuronal connectivity, and network activity synchronization may contribute to functional differences relevant to the cognitive and intellectual features associated with Down syndrome.'

• One major limitation of the current experimental design is the reliance on predominantly excitatory neuronal cultures derived from hiPSCs. Although the authors convincingly demonstrate differences in network synchronization and connectivity between trisomic (TS21) and control neurons, the almost exclusive focus on excitatory cells limits the physiological relevance of the in vitro network. In the developing cortex, interneurons and astrocytes play crucial roles in modulating network excitability, synaptogenesis, and plasticity. Therefore, incorporating these cell types-either through co-culture systems or through directed differentiation protocols that yield a more heterogeneous neuronal population-could help to determine whether the observed deficits are intrinsic to excitatory neurons or are compounded by a lack of proper inhibitory regulation and glial support. 1.2) Thank you for this thoughtful comment. We agree that interneurons and astrocytes are crucial for network function. To clarify, astrocytes are generated in this culture system, as we previously reported in our characterisation of the timecourse of network development using this approach (Kirwan et al., Development 2025). However, our primary goal was to first isolate and define the cell-autonomous defects intrinsic to TS21 excitatory neurons, minimizing the complexity introduced by additional neuronal types. This focused approach was chosen also because engineering a stable co-culture system with reproducible excitatory/inhibitory (E/I) proportions is a significant undertaking that extends beyond the scope of this initial investigation, and has proven challenging to date for the field. By establishing this foundational phenotype, our work complements prior studies on interneuron and glial contributions. Future studies building on this work will be essential to dissect the more complex, non-cell-autonomous effects within a heterogeneous network. Importantly, since our initial submission, two highly relevant preprints have emerged-including a notable study from the Geschwind laboratory at UCLA (Vuong et al., bioRxiv, 2025; Risgaard et al., bioRxiv, 2025), as well as our own complementary study Lattke et al, under revision, that highlight widespread transcriptional changes in excitatory cells of the human fetal DS cortex, providing strong validation for our central findings. This convergence of results from multiple groups underscores the timeliness and importance of our work.

• Furthermore, the assessment of neuronal connectivity via pseudotyped rabies virus tracing, while innovative, has inherent limitations. The quantification of connectivity as a ratio of red-to-green fluorescence pixels may be influenced by differential viral infection efficiencies, variations in the expression levels of the TVA receptor, or even by the lower basal activity levels observed in TS21 cultures. Complementary approaches-such as electron microscopy for synaptic density analysis or functional connectivity measurements using multi-electrode arrays (MEAs)-could provide additional structural and functional insights that would validate the rabies tracing data. 1.3) Thank you for this constructive feedback. While we cannot formally exclude that TS21 cells might express the TVA receptor at lower levels due to generalized gene dysregulation, we infected all WT and TS21 cultures in parallel using identical virus preparations and titers to minimize technical variability. Crucially, we also addressed the potential confound of differential basal activity by performing the rabies tracing under TTX incubation (see Suppl. Fig. 7), which blocks network activity and ensures that viral spread reflects structural connectivity alone.

While complementary methods like EM or MEA could provide additional insight, they fall outside the scope of the current study. We are confident that our rigorous controls validate our use of the rabies tracing method to assess structural connectivity.

• Qualification of Claims: Some conclusions, particularly those linking specific ion channel dysregulation (e.g., HCN1 loss) directly to network deficits, might be better presented as preliminary. The authors could temper their language to indicate that while the evidence is suggestive, the mechanistic link remains to be fully established. 1.4) We have revised the text to more clearly indicate that the link between HCN1 dysregulation and network deficits is correlative and remains to be fully established. While our ex vivo recordings suggest altered Ih-like currents consistent with reduced HCN1 expression, we now present these findings as preliminary and hypothesis-generating, pending further functional validation. We write in the discussion: However, further targeted functional validation will be needed to confirm a causal link.

• Need for Additional Experiments: Additional experiments that could further consolidate the current findings include: o Inclusion of Inhibitory Neurons or Co-culture Systems: Incorporating interneurons or astrocytes would help determine whether the observed deficits are solely intrinsic to excitatory neurons. See 1.2 o Alternative Connectivity Assessments: Complementing the rabies virus tracing with electron microscopy or multi-electrode array (MEA) recordings would add structural and functional validation of the connectivity differences. See 1.3 o Extended Temporal Profiling: Monitoring network activity over a longer developmental window would clarify whether the observed deficits represent a delay or a permanent alteration in network maturation. 1.5) In vivo we were able to track the cells for up to five months post-transplantation supporting the interpretation of a permanent alteration.

• Reproducibility and Statistical Rigor: The methods and data presentation are largely clear, with adequate replication and appropriate statistical analyses. Nonetheless, a more detailed description of the experimental replicates, particularly regarding the viral tracing and in vivo transplantation studies, would enhance reproducibility. The availability of raw data and scripts for calcium imaging analysis would also further support independent verification. We thank the reviewer for these suggestions and we now provide a more detailed description of replicates. We also add the raw data.

Minor Comments • Experimental Details: Minor revisions could include clarifying the infection efficiency and expression levels of the viral constructs used in connectivity assays to rule out technical variability.

See 1.3

• Literature Context: The authors reference prior studies appropriately; however, integrating a brief discussion comparing their findings with alternative DS models (e.g., organoids or other hiPSC-derived systems) would improve contextual clarity. We thank the reviewer for this helpful suggestion. We have now added a brief discussion comparing our findings with those reported in alternative Down syndrome models, including brain organoids and other hiPSC-derived systems. This addition helps to contextualize our results within the broader field and highlights the unique strengths and limitations of our in vitro and in vivo xenograft approach. We write: 'Our findings align with and extend previous studies using alternative Down syndrome models, such as brain organoids and other hiPSC-derived systems. Organoid models have provided valuable insights into early neurodevelopmental phenotypes in DS, including altered interneuron proportions (Xu et al Cell Stem Cell 2019) but also suggest that variability across isogenic lines can overshadow subtle trisomy 21 neurodevelopmental phenotypes (Czerminski et al Front in Neurosci 2023). However, these systems often lack the structural complexity, vascularization, and long-term maturation achievable in vivo. By using a xenotransplantation model, we were able to assess the maturation and functional properties of human neurons within a physiologically relevant environment over extended time frames, offering complementary insights into DS-associated circuit dysfunction (Huo et al Stem Cell Reports 2018; Real et al., 2018).

• Presentation and Clarity: Figures are generally clear,.But the manuscript contains a minor labeling error. On page 13, the figure is erroneously labeled as "Fig6A", whereas, based on the context and corresponding data, it should be "Fig5A". I recommend that the authors correct this mistake to ensure consistency and avoid potential confusion for readers. Thank you for pointing this out. This has been corrected in the revised manuscript.

Reviewer #1 (Significance (Required)):

SECTION B - Significance • Nature and Significance of the Advance: The work offers a substantial conceptual advance by providing a mechanistic link between trisomy 21 and impaired neuronal network synchronization. Technically, the study integrates state-of-the-art imaging, electrophysiology, and transcriptomic profiling, thereby offering a multifaceted view of DS-related neural dysfunction. Clinically, the findings have the potential to inform future therapeutic strategies targeting network connectivity and ion channel function in Down syndrome.

We thank the reviewer for this very supportive comment.

• Context in the Existing Literature: The study builds on previous observations of altered network activity in DS patients and DS mouse models (e.g., altered EEG synchronization and reduced synaptic connectivity). It extends these findings to human-derived neuronal models, thus bridging a gap between clinical observations and molecular/cellular mechanisms. Relevant literature includes studies on DS neurodevelopment and the role of ion channels in synaptic maturation. • Target Audience: The reported findings will be of interest to researchers in neurodevelopmental disorders, Down syndrome, and ion channel physiology. Additionally, the study may attract the attention of those working on hiPSC-derived models of neurological diseases, as well as clinicians interested in the pathophysiology of DS. • Keywords and Field Contextualization: Keywords: Down syndrome, trisomy 21, neuronal connectivity, synchronized network activity, hiPSC-derived cortical neurons, ion channel dysregulation.

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

Summary The manuscript by Peter et al., reports on the neuronal activity and connectivity of iPSC-derived human cortical neurons from Down syndrome (DS) that is caused by caused by trisomy of the human chromosome 21 (TS21). Major points: Although the manuscript is potentially interesting, the results appear somehow preliminary and need to be corroborated by control experiments and quantifications of effects to fully sustain the conclusions. (1) The authors have not assessed the percentage of WT and TS21 cells that acquire a neuronal or glia identity in their cultures. Indeed, the origin of alterations in network activity and connectivity observed in TS21 neurons could simply derive from reduced number of neurons arising from TS21 iPSC. Alternatively, the same alteration in network activity and connectivity could derive from a multitude of other factors including deficits in neuronal development, neurite extension, or intrinsic electrophysiological properties. In the current version of the manuscript, none of these has been investigated. 2.1) We thank the reviewer for this thoughtful comment. In response, we included an in vivo characterization of cell-type proportions at the same time points where we observed network activity defects using in vivo calcium imaging (see Supplementary Fig. 6).

Previous work has identified several cellular and molecular phenotypes in human cells, postmortem tissue, and mouse models-including those mentioned by the reviewer. In this study, our focus was on investigating neural network activity, intrinsic electrophysiological properties both in vitro and in vivo, and preliminary bulk RNA sequencing. We have also independently measured cell proportions in the human fetal cortex and conducted a more extensive transcriptomic analysis of Ts21 versus control cells in a separate study (Lattke et al., under revision). We observed a reduction of RORB/FOXP1-expressing Layer 4 neurons in the human fetal cortex at midgestation, as well as increased GFAP+ cells, reduced progenitors and a non significant reduction of Cux2+ cells in late stage DS human cell transplants, along with a gene network dysregulation specifically affecting excitatory neurons (Lattke et al., under revision). Here, we provide complementary findings, demonstrating reduced excitatory neuron network connectivity in vitro and decreased neural network synchronised activity in both in vitro and in vivo models (see also 2.8). We agree with the reviewer that this could be for a number of reasons, both cell autonomous (channel expression and/or function) or non-autonomous (connectivity and/or network composition - as reflected in differences in proportions of SATB2+ neurons generated in TS21 cortical differentiations).

(2) Electrophysiological properties of TS21 and WT neurons at day 53/54 in vitro indicate an extremely immature stage of development (i.e. RMP between -36 and -27 mV with most of the cells firing a single action potential after current injection) in the utilized culture conditions: This is far from ideal for in vitro neuronal-network studies. Finally, reduced activity of HCN1 channels should be confirmed by specific recordings isolating or blocking the related current.

2.2) Thank you for this thoughtful comment. We have also conducted ex vivo electrophysiological recordings and found that the neurons exhibit relatively immature properties, consistent with the known slow developmental trajectory of human neuron cultures. In light of this and the absence of direct confirmatory evidence, we now refer to the observed reduction in HCN1 as preliminary.

Main points highlighting the preliminary character of the study. 1) In Figure 1 immunofluorescence images of the neuronal differentiation markers (Tbr1, Ctip2 and Tuj1) are showed. However, no quantification of the percentage of cells expressing these markers for WT and TS21 neurons is reported. On the other hand, simple inspection of the representative images clearly seams to indicate a difference between the two genotypes, with TS21 cultures showing lower number of cells expressing neuronal markers. This quantification should be corroborated by a similar staining for an astrocyte marker (GFAP, but not S100b since is triplicated in DS). This is an extremely important point since it is obvious that any change in the percentage of neurons (or the neuron/astrocyte ratio) in the cultures will strongly affect the resulting network activity (shown in Figure 2) and the connectivity (showed in Figure 4). Possibly, the quantification should be done at the same time points of the calcium imaging experiments.

2.3) See 2.1. We included an in vivo characterization of cell-type proportions at the same time points where we observed network activity defects using in vivo calcium imaging. (see Supplementary Fig. 6).

2) In Figure 2 the authors show some calcium imaging traces of WT and TS21 cultures at different time points. However, they again do not show any quantification of neuronal activity. A power spectra analysis is shown in Supplementary Figure 2, but only for WT cultures, while in Supplementary Figure 3 a comparison between WT and Ts21 power spectra is done, but only at the 50 day time point, while difference in synchrony are assessed at 60 days. At minimum, the author should include in main Figure 2 the quantification of the mean calcium event rate and mean event amplitude at the different time points and the power spectra analysis for both WT and TS21 cultures at the same timepoints.

2.4) We thank the reviewer for this comment. We now add the power spectra analysis in the main Figure 2 and quantification of the mean calcium burst rate and mean event amplitude in SuppFig. 4.

Of note, the synchronized neuronal activity is present in WT cultures at day 60, but totally lost at subsequent time-points (70 and 80 days). The results of this later time points are different from previous data from the same lab (Kirwan et al., 2015). How might these data be explained? It would be important to rule out any potential issues with the health of the culture that could explain the loss of neuronal activity.It would be beneficial to check cell viability at the different time points to exclude possible confounding factors ? A propidium staining or a MTT assay would strongly improve the soundness of the calcium data.

2.5) We thank the reviewer for this important observation. The difference from the findings reported in Kirwan et al., 2015 is due to the use of a different neuronal differentiation medium in the current study (BrainPhys versus N2B27). BrainPhys medium supports robust early network activity compared to N2B27 (onset before day 60 in BrainPhys, post-day 60 in N2B27), resulting in an earlier decline in synchrony at later stages (day 70-80 in BrainPhys, compared with day 90-100 in N2B27). Importantly, in our in vivo xenograft model, burst activity is sustained up to at least 5 months post-transplantation (mpt), indicating that the neurons retain the capacity for network activity over extended periods in a more physiological environment. We adapted the text accordingly.

3) In Figure 3 there is no quantification of the number and/or density of transplanted neurons for WT and TS21, but only representative images. As above, inspection of the representative images seems to show a decrease in cells labeled by the Tbr1 neuronal marker for TS21 cells. Moreover, the in vivo calcium imaging of transplanted WT and TS21 cells lacks most of the quantification normally done in calcium imaging experiments. Are the event rate and event amplitude different between WT and TS21 neurons ? The measure of neuronal synchrony by mean pixel correlation is not well explained, but it looks somehow simplistic. Neuronal synchrony can be more precisely measured by cross-correlation analysis or spike time tiling coefficients on the traces from single-neuron ROI rather than on all pixels in the field of view, as apparently was done here.

2.6) We thank the reviewer for these valuable points. We now include quantification of the number and density of transplanted neurons for both WT and Ts21 grafts in Extended Data Figure 5 (see 2.1).

Regarding the in vivo calcium imaging, we appreciate the reviewer's suggestion to include additional standard metrics. We have quantified the event rate in Real et al 2018. These analyses reveal that Ts21 neurons show a reduction in event rate.

We agree that our initial description of the synchrony analysis using mean pixel correlation was not sufficiently detailed. We have now clarified this in the Methods and Results, and we acknowledge its limitations. Importantly, we note that the reduced synchronisation is a highly consistent phenotype, observed across at least six independent donor pairs, different differentiation protocols, and both in vitro (and in two independent labs) and in vivo settings. As suggested, future studies using ROI-based approaches-such as cross-correlation or spike-time tiling coefficients-would provide a more refined characterization of synchrony at the single-neuron level (Sintes et al, in preparation). We now include this point in the discussion.

4) The results on reduced neuronal connectivity in Figure 3 look very striking. However, these results should be accompanied by control experiments to verify the number of neuronal cells and neurite extension in WT and Ts21 cultures. These two parameters could indeed strongly influence the results. As the cultures appear to grow in clusters, bright-field images and TuJ1 staining of the cultures will also greatly help to understand the degree of morphological interconnection between the clusters.

We now add Tuj1 staining in Supplementary figure 10.

5) The authors performed RNA-seq experiments on day 50 cultures. Why the authors do not show the complete differential gene expression analysis, but only a small subset of genes? A comprehensive volcano plot and the complete list of identified genes with logFC and FDR values would be helpful. If possible, comparison of the present data (particularly on KCN and HCN expression changes) with published and publicly available expression datasets of other human or human Down syndrome iPSC-derived neurons or human Down syndrome brains will greatly increase the soundness of the present findings. In addition, the gene ontology (GO) results are mentioned in the text, but are not presented. Showing the complete GO analysis for both up and downregulated genes will help the reader to better understand the RNA-seq results. Notably, the results shown in Supplementary Figure on GRIN2A and GRIN2B expression (with values of 300-700 counts versus 2000-4000 counts, respectively) clearly indicate that in both WT and TS21 cultures the NMDA developmental switch has not occurred yet at the 50 days timepoint.

We now show volcano plots in Supplementary Fig. 11.

6) The measure of hyperpolarization-activated currents shown in Figure 5 lack proper control experiments. First, the hyperpolarizing current in TS21 cells do not reach a steady-state as the controls. The two curves are therefore hard to compare. To exclude possible difference in kinetic activation, the authors should have prolonged the current injection period (1-2 seconds). Second, to ultimately prove that such currents are mediated by HCN channels in WT cells the authors should perform some control experiments with a specific HCN blocker. A good example of a suitable protocol, with also current blockers to exclude all other possible current contributions, is the one reported in Matt et al Cell. Mol. Life Sci. 68, 125-137 (2011).

2.7) We thank the reviewer for this detailed and helpful comment. We agree that to definitively identify the recorded currents as Ih, it would be necessary to isolate them pharmacologically using specific HCN channel blockers and appropriate controls, such as those described in Matt et al., Cell. Mol. Life Sci. Unfortunately, due to current constraints, we no longer have access to the animals used in this study and cannot allocate the necessary time or resources, we are unable to perform the additional experiments at this stage.

However, our goal here was to use electrophysiological recordings as an indication of altered HCN channel activity, which we then support with molecular evidence. We now emphasize this point more clearly in the revised manuscript.

7) The manuscript lacks information on the statistical analysis used. Also, the numerosity of samples is not clear. Were the dots shown in some graph technical replicates from a single neuronal induction or were all independent neuronal inductions or a mix of the two ? Please clarify.

We now clarify the numbers in the Figure legend.

8) The method section lacks important information to guarantee reproducibility. Just a few examples: • Only electrophysiology methods for slice are reported, but not for in vitro culture.

We now clarify these details in the methods.

• Details on Laminin coating is lacking. What concentration was used ? Was poly-ornithine or poly-lysine used before Laminin coating ? We now clarify these details in the methods.

• How long cells were switched to BrainPhys medium before calcium imaging ? We now clarify these details in the methods.

Minor point/typos etc.

Introduction • Page 4 line 6: in the line "Trisomy 21 in humans commonly results in a range in developmental and morphological changes in the forebrain ..." "in" could be replaced by "of". We have fixed this. • Page 5 line 2: please remove "an" before the word "another". We have fixed this. • Page 5 line 2: please replace "ecitatory" with "excitatory". We have fixed this typo.

Results • Page 10 line 25: The concept of "pixel-wise" appears for the first time in this section and could be better introduced to facilitate the understanding of the experiment. • In the "results" section, page 11 line 1 and 4, references are made to "Figure 4D" and "4F," but these figures do not appear to be present in the figure section. Upon reviewing the rest of the section, the data seem to refer to "Figure 3D" and "3E." We have fixed this. Discussion • Page 15 line 20: please replace "synchronised" with "synchronized". We have fixed this typo. • Page 16 line 11: please replace "T21" with "TS21". We have fixed this typo. Methods • Page 19 line 12: "Pens/Strep" has to be replaced by Pen/Strep. We have fixed this typo. • Page 20 line 20: "Tocris Biocience" has to be replaced by "Tocris Bioscience". We have fixed this typo. • Page 21 line 2: "Addegene" has to be replaced by "Addgene". We have fixed this typo. Figures • Figure 3: the schematic experimental design (Fig. 3A) could be enlarged to match the width of the images/graphs below. We have fixed this. • Figure 5: the reviewer suggests resizing/repositioning the graphs in Fig. 1A so that they match the width of those below. We have fixed this. • Figure S1D: In all the figures of the paper, the respective controls for the TS21 1 and TS21 2 lines are labelled as "WT1/WT2," while in these graphs, they are called "Ctrl1" and "Ctrl2." To ensure consistency throughout the paper, it is suggested to change the names in these graphs. We have fixed this. • Figure S4L: The graph is not very clear, especially regarding the significance reported at -50 pA, please modify the graphical visualization and/or add a legend in the caption. We have fixed this.

Reviewer #2 (Significance (Required)):

Nature and significance of the advance for the field. The results presented in the manuscript are potentially interesting and useful, but not completely novel (currents deregulation has already been highlighted in mouse models of Down Syndrome).

2.8) We thank the reviewer for this comment. While we agree that current deregulation has been observed in mouse models of Down syndrome, the novelty and significance of our study lie in demonstrating these alterations directly in human neurons using both in vitro and in vivo xenograft models.

This is a critical advance because the human cortex has distinct developmental and functional properties not fully recapitulated in mice. In fact, three recent studies have already highlighted significant defects mainly in excitatory neurons within the fetal human DS cortex (Vuong et al., bioRxiv, 2025; Risgaard et al., bioRxiv, 2025; Lattke et al, under revision). Our work builds directly on these observations by providing, for the first time, an electrophysiological and network-level characterization of these human-specific deficits.

Our findings thus provide translationally relevant insight that is not merely confirmatory but extends previous work by grounding it in a human cellular context.

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Referee #2

Evidence, reproducibility and clarity

Summary

The manuscript by Peter et al., reports on the neuronal activity and connectivity of iPSC-derived human cortical neurons from Down syndrome (DS) that is caused by caused by trisomy of the human chromosome 21 (TS21).

Major points:

Although the manuscript is potentially interesting, the results appear somehow preliminary and need to be corroborated by control experiments and quantifications of effects to fully sustain the conclusions.

(1) The authors have not assessed the percentage of WT and TS21 cells that acquire a neuronal or glia identity in their cultures. Indeed, the origin of alterations in network activity and connectivity observed in TS21 neurons could simply derive from reduced number of neurons arising from TS21 iPSC. Alternatively, the same alteration in network activity and connectivity could derive from a multitude of other factors including deficits in neuronal development, neurite extension, or intrinsic electrophysiological properties. In the current version of the manuscript, none of these has been investigated.

(2) Electrophysiological properties of TS21 and WT neurons at day 53/54 in vitro indicate an extremely immature stage of development (i.e. RMP between -36 and -27 mV with most of the cells firing a single action potential after current injection) in the utilized culture conditions: This is far from ideal for in vitro neuronal-network studies. Finally, reduced activity of HCN1 channels should be confirmed by specific recordings isolating or blocking the related current.

Main points highlighting the preliminary character of the study.

1) In Figure 1 immunofluorescence images of the neuronal differentiation markers (Tbr1, Ctip2 and Tuj1) are showed. However, no quantification of the percentage of cells expressing these markers for WT and TS21 neurons is reported. On the other hand, simple inspection of the representative images clearly seams to indicate a difference between the two genotypes, with TS21 cultures showing lower number of cells expressing neuronal markers. This quantification should be corroborated by a similar staining for an astrocyte marker (GFAP, but not S100b since is triplicated in DS). This is an extremely important point since it is obvious that any change in the percentage of neurons (or the neuron/astrocyte ratio) in the cultures will strongly affect the resulting network activity (shown in Figure 2) and the connectivity (showed in Figure 4). Possibly, the quantification should be done at the same time points of the calcium imaging experiments.

2) In Figure 2 the authors show some calcium imaging traces of WT and TS21 cultures at different time points. However, they again do not show any quantification of neuronal activity. A power spectra analysis is shown in Supplementary Figure 2, but only for WT cultures, while in Supplementary Figure 3 a comparison between WT and Ts21 power spectra is done, but only at the 50 day time point, while difference in synchrony are assessed at 60 days. At minimum, the author should include in main Figure 2 the quantification of the mean calcium event rate and mean event amplitude at the different time points and the power spectra analysis for both WT and TS21 cultures at the same timepoints.

Of note, the synchronized neuronal activity is present in WT cultures at day 60, but totally lost at subsequent time-points (70 and 80 days). The results of this later time points are different from previous data from the same lab (Kirwan et al., 2015). How might these data be explained? It would be important to rule out any potential issues with the health of the culture that could explain the loss of neuronal activity.It would be beneficial to check cell viability at the different time points to exclude possible confounding factors ? A propidium staining or a MTT assay would strongly improve the soundness of the calcium data.

3) In Figure 3 there is no quantification of the number and/or density of transplanted neurons for WT and TS21, but only representative images. As above, inspection of the representative images seems to show a decrease in cells labeled by the Tbr1 neuronal marker for TS21 cells. Moreover, the in vivo calcium imaging of transplanted WT and TS21 cells lacks most of the quantification normally done in calcium imaging experiments. Are the event rate and event amplitude different between WT and TS21 neurons ? The measure of neuronal synchrony by mean pixel correlation is not well explained, but it looks somehow simplistic. Neuronal synchrony can be more precisely measured by cross-correlation analysis or spike time tiling coefficients on the traces from single-neuron ROI rather than on all pixels in the field of view, as apparently was done here.

4) The results on reduced neuronal connectivity in Figure 3 look very striking. However, these results should be accompanied by control experiments to verify the number of neuronal cells and neurite extension in WT and Ts21 cultures. These two parameters could indeed strongly influence the results. As the cultures appear to grow in clusters, bright-field images and TuJ1 staining of the cultures will also greatly help to understand the degree of morphological interconnection between the clusters.

5) The authors performed RNA-seq experiments on day 50 cultures. Why the authors do not show the complete differential gene expression analysis, but only a small subset of genes? A comprehensive volcano plot and the complete list of identified genes with logFC and FDR values would be helpful. If possible, comparison of the present data (particularly on KCN and HCN expression changes) with published and publicly available expression datasets of other human or human Down syndrome iPSC-derived neurons or human Down syndrome brains will greatly increase the soundness of the present findings. In addition, the gene ontology (GO) results are mentioned in the text, but are not presented. Showing the complete GO analysis for both up and downregulated genes will help the reader to better understand the RNA-seq results. Notably, the results shown in Supplementary Figure on GRIN2A and GRIN2B expression (with values of 300-700 counts versus 2000-4000 counts, respectively) clearly indicate that in both WT and TS21 cultures the NMDA developmental switch has not occurred yet at the 50 days timepoint.

6) The measure of hyperpolarization-activated currents shown in Figure 5 lack proper control experiments. First, the hyperpolarizing current in TS21 cells do not reach a steady-state as the controls. The two curves are therefore hard to compare. To exclude possible difference in kinetic activation, the authors should have prolonged the current injection period (1-2 seconds). Second, to ultimately prove that such currents are mediated by HCN channels in WT cells the authors should perform some control experiments with a specific HCN blocker. A good example of a suitable protocol, with also current blockers to exclude all other possible current contributions, is the one reported in Matt et al Cell. Mol. Life Sci. 68, 125-137 (2011).

7) The manuscript lacks information on the statistical analysis used. Also, the numerosity of samples is not clear. Were the dots shown in some graph technical replicates from a single neuronal induction or were all independent neuronal inductions or a mix of the two ? Please clarify.

8) The method section lacks important information to guarantee reproducibility. Just a few examples: - Only electrophysiology methods for slice are reported, but not for in vitro culture. - Details on Laminin coating is lacking. What concentration was used ? Was poly-ornithine or poly-lysine used before Laminin coating ? - How long cells were switched to BrainPhys medium before calcium imaging ?

Minor point/typos etc.

Introduction

• Page 4 line 6: in the line "Trisomy 21 in humans commonly results in a range in developmental and morphological changes in the forebrain ..." "in" could be replaced by "of".
• Page 5 line 2: please remove "an" before the word "another".
• Page 5 line 2: please replace "ecitatory" with "excitatory"

Results

• Page 10 line 25: The concept of "pixel-wise" appears for the first time in this section and could be better introduced to facilitate the understanding of the experiment.
• In the "results" section, page 11 line 1 and 4, references are made to "Figure 4D" and "4F," but these figures do not appear to be present in the figure section. Upon reviewing the rest of the section, the data seem to refer to "Figure 3D" and "3E."

Discussion

• Page 15 line 20: please replace "synchronised" with "synchronized".
• Page 16 line 11: please replace "T21" with "TS21".

Methods

• Page 19 line 12: "Pens/Strep" has to be replaced by Pen/Strep.
• Page 20 line 20: "Tocris Biocience" has to be replaced by "Tocris Bioscience".
• Page 21 line 2: "Addegene" has to be replaced by "Addgene".

Figures

• Figure 3: the schematic experimental design (Fig. 3A) could be enlarged to match the width of the images/graphs below.
• Figure 5: the reviewer suggests resizing/repositioning the graphs in Fig. 1A so that they match the width of those below.
• Figure S1D: In all the figures of the paper, the respective controls for the TS21 1 and TS21 2 lines are labelled as "WT1/WT2," while in these graphs, they are called "Ctrl1" and "Ctrl2." To ensure consistency throughout the paper, it is suggested to change the names in these graphs.
• Figure S4L: The graph is not very clear, especially regarding the significance reported at -50 pA, please modify the graphical visualization and/or add a legend in the caption.

Significance

Nature and significance of the advance for the field. The results presented in the manuscript are potentially interesting and useful, but not completely novel (currents deregulation has already been highlighted in mouse models of Down Syndrome).

Work in the context of the existing literature. This work follows the line of evidence that characterizes Down Syndrome in human neurons (Huo, H.-Q. et al. Stem Cell Rep. 10, 1251-1266 (2018); Briggs, J. A. et al. Etiology. Stem Cells 31, 467-478 (2013)), both in vitro and in xenotransplanted mice, by corrborating some important findings already found in animal models (Stern, S., Segal, M. & Moses, E. EBioMedicine 2, 1048-1062 (2015); Cramer, N. P., Xu, X., F. Haydar, T. & Galdzicki, Z. Physiol. Rep. 3, e12655 (2015); Stern, S., Keren, R., Kim, Y. & Moses, E. http://biorxiv.org/lookup/doi/10.1101/467522 (2018) doi:10.1101/467522.

Audience. Scientists in the field of pre-clinical biomedical research, especially those working on neurodevelopmental disorders and iPSC-based non-animal models.

Field of expertise. In vitro electrophysiology, Neurodevelopmental disorders, Down Syndrome, ips cells.

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Referee #1

Evidence, reproducibility and clarity

Summary

The study investigates the neurodevelopmental impact of trisomy 21 on human cortical excitatory neurons derived from induced pluripotent stem cells (hiPSCs). Key findings include a modest reduction in spontaneous firing, a marked deficit in synchronized bursting, decreased neuronal connectivity, and altered ion channel expression-particularly a downregulation of voltage‐gated potassium channels and HCN1. These conclusions are supported by a combination of in vitro calcium imaging, electrophysiological recordings, viral monosynaptic tracing, RNA sequencing, and in vivo transplantation with two‐photon imaging.

Major Comments

• Convincing Nature of Key Conclusions: The study's conclusions are generally well supported by a diverse set of experimental approaches. However, certain claims regarding the intrinsic properties of the excitatory network would benefit from further qualification. In particular, the assertion that reduced synchronization is solely attributable to altered ion channel expression might be considered somewhat preliminary without additional corroborative experiments.
• One major limitation of the current experimental design is the reliance on predominantly excitatory neuronal cultures derived from hiPSCs. Although the authors convincingly demonstrate differences in network synchronization and connectivity between trisomic (TS21) and control neurons, the almost exclusive focus on excitatory cells limits the physiological relevance of the in vitro network. In the developing cortex, interneurons and astrocytes play crucial roles in modulating network excitability, synaptogenesis, and plasticity. Therefore, incorporating these cell types-either through co-culture systems or through directed differentiation protocols that yield a more heterogeneous neuronal population-could help to determine whether the observed deficits are intrinsic to excitatory neurons or are compounded by a lack of proper inhibitory regulation and glial support.
• Furthermore, the assessment of neuronal connectivity via pseudotyped rabies virus tracing, while innovative, has inherent limitations. The quantification of connectivity as a ratio of red-to-green fluorescence pixels may be influenced by differential viral infection efficiencies, variations in the expression levels of the TVA receptor, or even by the lower basal activity levels observed in TS21 cultures. Complementary approaches-such as electron microscopy for synaptic density analysis or functional connectivity measurements using multi-electrode arrays (MEAs)-could provide additional structural and functional insights that would validate the rabies tracing data.
• Qualification of Claims: Some conclusions, particularly those linking specific ion channel dysregulation (e.g., HCN1 loss) directly to network deficits, might be better presented as preliminary. The authors could temper their language to indicate that while the evidence is suggestive, the mechanistic link remains to be fully established.
• Need for Additional Experiments: Additional experiments that could further consolidate the current findings include:
  • Inclusion of Inhibitory Neurons or Co-culture Systems: Incorporating interneurons or astrocytes would help determine whether the observed deficits are solely intrinsic to excitatory neurons.
  • Alternative Connectivity Assessments: Complementing the rabies virus tracing with electron microscopy or multi-electrode array (MEA) recordings would add structural and functional validation of the connectivity differences.
  • Extended Temporal Profiling: Monitoring network activity over a longer developmental window would clarify whether the observed deficits represent a delay or a permanent alteration in network maturation.
• Reproducibility and Statistical Rigor: The methods and data presentation are largely clear, with adequate replication and appropriate statistical analyses. Nonetheless, a more detailed description of the experimental replicates, particularly regarding the viral tracing and in vivo transplantation studies, would enhance reproducibility. The availability of raw data and scripts for calcium imaging analysis would also further support independent verification.

Minor Comments

• Experimental Details:

Minor revisions could include clarifying the infection efficiency and expression levels of the viral constructs used in connectivity assays to rule out technical variability. - Literature Context:

The authors reference prior studies appropriately; however, integrating a brief discussion comparing their findings with alternative DS models (e.g., organoids or other hiPSC-derived systems) would improve contextual clarity. - Presentation and Clarity:

Figures are generally clear,.But the manuscript contains a minor labeling error. On page 13, the figure is erroneously labeled as "Fig6A", whereas, based on the context and corresponding data, it should be "Fig5A". I recommend that the authors correct this mistake to ensure consistency and avoid potential confusion for readers.

Significance

• Nature and Significance of the Advance:

The work offers a substantial conceptual advance by providing a mechanistic link between trisomy 21 and impaired neuronal network synchronization. Technically, the study integrates state-of-the-art imaging, electrophysiology, and transcriptomic profiling, thereby offering a multifaceted view of DS-related neural dysfunction. Clinically, the findings have the potential to inform future therapeutic strategies targeting network connectivity and ion channel function in Down syndrome. - Context in the Existing Literature:

The study builds on previous observations of altered network activity in DS patients and DS mouse models (e.g., altered EEG synchronization and reduced synaptic connectivity). It extends these findings to human-derived neuronal models, thus bridging a gap between clinical observations and molecular/cellular mechanisms. Relevant literature includes studies on DS neurodevelopment and the role of ion channels in synaptic maturation. - Target Audience:

The reported findings will be of interest to researchers in neurodevelopmental disorders, Down syndrome, and ion channel physiology. Additionally, the study may attract the attention of those working on hiPSC-derived models of neurological diseases, as well as clinicians interested in the pathophysiology of DS. - Keywords and Field Contextualization:

Keywords: Down syndrome, trisomy 21, neuronal connectivity, synchronized network activity, hiPSC-derived cortical neurons, ion channel dysregulation.

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Reply to the reviewers

We thank the referees for taking time to review our manuscript. These reviews are positive, highlighting the novelty of our findings. The majority of comments are cosmetic, and we have added data in response to some technical points. We feel that some of the additional experiments proposed would not add significant methodological depth, and cross-commenting suggests that our referees agree. At present we are attempting antibody staining to quantify Tk peptide retention in the midgut, as per suggestion by reviewer #2.

We enclose our point-by-point response to each referee's points, below.

__Reviewer #1 __

• Can the authors state in the figure legends the numbers of flies used for each lifespan and whether replicates have been done?

• We have incorporated the requested information into legends for lifespan experiments.

• Do the interventions shorten lifespan relative to the axenic cohort? Or do they prevent lifespan extension by axenic conditions? Both statements are valid, and the authors need to be consistent in which one they use to avoid confusing the reader.

• We read these statements differently. The only experiment in which a genetic intervention prevented lifespan extension by axenic conditions is neuronal TkR86C knockdown (Figure 6B-C). Otherwise, microbiota shortened lifespan relative to axenic conditions, and genetic knockdowns extend blocked this effect (e.g. see lines 131-133). We have ensured that the framing is consistent throughout, with text edited at lines 198-199, 298-299, 311-312, 345-347, 408-409, 424-425, 450, 497-503.

• TkRNAi consistently reduces lipid levels in axenic flies (Figs 2E, 3D), essentially phenocopying the loss of lipid stores seen in control conventionally reared (CR) flies relative to control axenic. This suggests that the previously reported role of Tk in lipid storage - demonstrated through increased lipid levels in TkRNAi flies (Song et al (2014) Cell Rep 9(1): 40) - is dependent on the microbiota. In the absence of the microbiota TkRNAi reduces lipid levels. The lack of acknowledgement of this in the text is confusing

• We have added text at lines 219-222 to address this point. We agree that this effect is hard to interpret biologically, since expressing RNAi in axenics has no additional effect on Tk expression (Figure S7). Consequently we can only interpret this unexpected effect as a possible off-target effect of RU feeding on TAG, specific to axenic flies. However, this possibility does not void our conclusion, because an off-target dimunition of TAG cannot explain why CR flies accumulate TAG following TkRNAi We hope that our added text clarifies.

• *I have struggled to follow the authors logic in ablating the IPCs and feel a clear statement on what they expected the outcome to be would help the reader. *

• We have added the requested statement at lines 423-424, explaining that we expected the IPC ablation to render flies constitutively long-lived and non-responsive to A pomorum.

• *Can the authors clarify their logic in concluding a role for insulin signalling, and qualify this conclusion with appropriate consideration of alternative hypotheses? *

• We have added our logic at lines 449-454. In brief, we conclude involvement for insulin signalling because FoxO mutant lifespan does not respond to TkRNAi, and diminishes the lifespan-shortening effect of * pomorum*. However, we cannot state that the effects are direct because we do not have data that mechanistically connects Tk/TkR99D signalling directly in insulin-producing cells. The current evidence is most consistent with insulin signalling priming responses to microbiota/Tk/TkR99D, as per the newly-added text.

• Typographical errors

• We have remedied the highlighted errors, at lines 128-140.

• I'd encourage the authors to provide lifespan plots that enable comparison between all conditions

• We have plotted our figures in faceted boxes, because the number of survival curves that would need to be presented on the same axis (e.g. 16 for Figure 5) would not be intellegible. However we have ensured that axes on faceted plots are equivalent and with grid lines for comparison. Moreover, our approach using statistical coefficients (EMMs) enables direct quantitative comparison of the differences among conditions.

Reviewer #2

• Not…essential for publication…is it possible to look at Tk protein levels?

• We have acquired a small amount of anti-TK antibody and we will attempt to immunostain guts associated with * pomorum and L. brevis*. We are also attempting the equivalent experiment in mouse colon reared with/without a defined microbiota. These experiments are ongoing, but we note that the referee feels that the manuscript is a publishable unit whether these stainings succeed or not.

• it would be good to show that the bacterial levels are not impacted [by TkRNAi]

• We have quantified CFUs in CR flies upon ubiquitous TkRNAi (Figure S5), finding that the RNAi does not affect bacterial load. New text at lines 138-139 articulates this point.

• The effect of Tk RNAi on TAG is opposite in CR and Ax or CR and Ap flies, and the knockdown shows an effect in either case (Figure 2E, Figure 3D). Why is this?

• As per response to Reviewer #1, we have added text at lines 219-222 to address this point.

• Is it possible to perform at least one lifespan repeat with the other Tk RNAi line mentioned?

• We have added another experiment showing longevity upon knockdown in conventional flies, using an independent TkRNAi line (Figure S3).

• Is it possible that this driver is simply not resulting in an efficient KD of the receptor? I would be inclined to check this

• This comment relates to Figure 7G. We do see an effect of the knockdown in this experiment, so we believe that the knockdown is effective. However the direction of response is not consistent with our hypothesis so the experiment is not informative about the role of these cells. We therefore feel there is little to be gained by testing efficacy of knockdown, which would also be technically challenging because the cells are a small population in a larger tissue which expresses the same transcripts elsewhere (i.e. necessitating FISH).

• Would it be possible to use antibodies for acetylated histones?

• The comment relates to Figure 4C-E. The proposed studies would be a significant amount of work because, to our knowledge, the specific histone marks which drive activation in TK+ cells remain unknown. On the other hand, we do not see how this information would enrich the present story, rather such experiments would appear to be the beginning of something new. We therefore agree with Reviewer #1 (in cross-commenting) that this additional work is not justified.

Reviewer #3

• *In Line243, the manuscript states that the reporter activity was not increased in the posterior midgut. However, based on the presented results in Fig4E, there is seemingly not apparent regional specificity. A more detailed explanation is necessary. *

• We thank the reviewer sincerely for their keen eye, which has highlighted an error in the previous version of the figure. In revisiting this figure we have noticed, to our dismay, that the figures for GFP quantification were actually re-plots of the figures for (ac)K quantification. This error led to the discrepancy between statistics and graphics, which thankfully the reviewer noticed. We have revised the figure to remedy our error, and the statistics now match the boxplots and results text.

• Fig1C uses Adh for normalization. Given the high variability of the result, the authors should (1) check whether Adh expression levels changed via bacterial association

• We selected Adh on the basis of our RNAseq analysis, which showed it was not different between AX and CV guts, whereas many commonly-used “housekeeping” genes were. We have now added a plot to demonstrate (Figure S2).

• The statement in Line 82 that EEs express 14 peptide hormones should be supported with an appropriate reference

• We have added the requested reference (Hung et al, 2020) at line 86.

• Tk+ EEC activity should be assessed directly, rather than relying solely on transcript levels. Approaches such as CaLexA or GCaMP could be used.

• We agree with reviewers 1-2 (in cross-commenting) that this proposal is non-trivial and not justified by the additional insight that would be gained. As described above, we are attempting to immunostain Tk, which if successful will provide a third line of evidence for regulation of Tk+ cells. However we note that we already have the strongest possible evidence for a role of these cells via genetic analysis (Figure 5).

• While the difficulty of maintaining lifelong axenic conditions is understandable, it may still be feasible to assess the induction of Tk (ie. Tk transcription or EE activity upregulation) by the microbiome on males.

• As the reviewer recognises, maintaining axenic experiments for months on end is not trivial. Given the tendency for males either to simply mirror female responses to lifespan-extending interventions, or to not respond at all, we made the decision in our work to only study females. We have instead emphasised in the manuscript that results are from female flies.

• TkR86C, in addition to TkR99D, may be involved in the A. pomorum-lifespan interaction. Consider revising the title to refer more generally to the "tachykinin receptor" rather than only TkR99D.

• We disagree with this interpretation: the results do not show that TkR86C-RNAi recapitulates the effect of enteric Tk-RNAi. A potentially interesting interaction is apparent, but the data do not support a causal role for TkR86C. A causal role is supported only for TkR99D, knockdown of which recapitulates the longevity of axenic flies and TkRNAi flies. Therefore we feel that our current title is therefore justified by the data, and a more generic version would misrepresent our findings.

• The difference between "aging" and "lifespan" should also be addressed.

• The smurf phenotype is a well-established metric of healthspan. Moreover, lifespan is the leading aggregate measure of ageing. We therefore feel that the use of “ageing” in the title is appropriate.

• If feasible, assessing foxo activation would add mechanistic depth. This could be done by monitoring foxo nuclear localization or measuring the expression levels of downstream target genes.

• Foxo nuclear localisation has already been shown in axenic flies (Shin et al, 2011). We have added text and citation at lines 402-403.

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Referee #3

Evidence, reproducibility and clarity

Summary

Marcu et al. demonstrate a gut-neuron axis that is required for the lifespan-shortening effects mediated by gut bacteria. They show that the presence of commensal bacteria-particularly Acetobacter pomorum-promotes Tk expression in the gut, which then binds to neuronal tachykinin receptors to shorten lifespan. Tk has also recently been reported to extend lifespan via adipokinetic hormone (Akh) signaling (Ahrentløv et al., Nat Metab 7, 2025), but the mechanism here appears distinct. The lifespan shortening by Ap via Tk seems to be partially dependent on foxo and independent of both insulin signaling and Akh-mediated lipid mobilization. Although the detailed mechanistic link to lifespan is not fully resolved, the experiment and its results clearly shows the involvement of the molecules tested. This work adds a valuable dimension to our growing understanding of how gut bacteria influence host longevity. However, there are some points that should be addressed.

1. Tk+ EEC activity should be assessed directly, rather than relying solely on transcript levels. Approaches such as CaLexA or GCaMP could be used.
2. In Line243, the manuscript states that the reporter activity was not increased in the posterior midgut. However, based on the presented results in Fig4E, there is seemingly not apparent regional specificity. A more detailed explanation is necessary.
3. If feasible, assessing foxo activation would add mechanistic depth. This could be done by monitoring foxo nuclear localization or measuring the expression levels of downstream target genes.
4. Fig1C uses Adh for normalization. Given the high variability of the result, the authors should (1) check whether Adh expression levels changed via bacterial association and/or (2) compare the results using different genes as internal standard.
5. While the difficulty of maintaining lifelong axenic conditions is understandable, it may still be feasible to assess the induction of Tk (ie. Tk transcription or EE activity upregulation) by the microbiome on males.
6. We also had some concerns regarding the wording of the title. Fig6B and C suggests that TkR86C, in addition to TkR99D, may be involved in the A. pomorum-lifespan interaction. Consider revising the title to refer more generally to the "tachykinin receptor" rather than only TkR99D. The difference between "aging" and "lifespan" should also be addressed. While the study shows a role for Tk in lifespan, assessment of aging phenotypes (eg. Climbing assay, ISC proliferation) beyond the smurf assay is required to make conclusions about aging.
7. The statement in Line 82 that EEs express 14 peptide hormones should be supported with an appropriate reference, if available.

Referees cross-commenting

I agree with the other reviewers that the study has been done very well and hence additional experiments are not mandatory to be published such as calcium imaging. However, I still believe that testing Tk's elevation by the Ap in males should greatly increase the generality of the finding, no matter what the outcome would be. Too many studies use only females.

Significance

General assessment

The main strength of this study is the careful and extensive lifespan analyses, which convincingly demonstrate the role of gut microbiota in regulating longevity. The authors clarify an important aspect of how microbial factors contribute to lifespan control. The main limitation is that the study primarily confirms the involvement of previously reported signaling pathways, without identifying novel molecular players or previously unrecognized mechanisms of lifespan regulation.

Advance

The lifespan-shortening effect of Acetobacter pomorum (Ap) has been reported previously, as has the lifespan-shortening effect of Tachykinin (Tk). However, this study is the first to link these two factors mechanistically, which represents a significant and original contribution to the field. The advance is primarily mechanistic, providing new insight into how microbial cues converge on host signaling pathways to influence ageing.

Audience

This work will be of particular interest to a specialized audience of basic researchers in ageing biology. It will also attract interest from microbiome researchers who are investigating host-microbe interactions and their physiological consequences. The findings will be useful as a conceptual framework for future mechanistic studies in this area.

Field of expertise

Drosophila ageing, lifespan, microbiome, metabolism

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Referee #2

Evidence, reproducibility and clarity

The main finding of this work is that microbiota impacts lifespan though regulating the expression of a gut hormone (Tk) which in turn acts on its receptor expressed on neurons. This conclusion is robust and based on a number of experimental observation, carefully using techniques in fly genetics and physiology: 1) microbiota regulates Tk expression, 2) lifespan reduction by microbiota is absent when Tk is knocked down in gut (specifically in the EEs), 3) Tk knockdown extends lifespan and this is recapitulated by knockdown of a Tk receptor in neurons. These key conclusions are very convincing. Additional data are presented detailing the relationship between Tk and insulin/IGF signalling and Akh in this context. These are two other important endocrine signalling pathways in flies. The presentation and analysis of the data are excellent.

There are only a few experiments or edits that I would suggest as important to confirm or refine the conclusions of this manuscript. These are:

1. When comparing the effects of microbiota (or single bacterial species) in different genetic backgrounds or experimental conditions, I think it would be good to show that the bacterial levels are not impacted by the other intervention(s). For example, the lifespan results observed in Figure 2A are consistent with Tk acting downstream of the microbes but also with Tk RNAi having an impact on the microbiota itself. I think this simple, additional control could be done for a few key experiments. Similarly, the authors could compare the two bacterial species to see if the differences in their effects come from different ability to colonise the flies.
2. The effect of Tk RNAi on TAG is opposite in CR and Ax or CR and Ap flies, and the knockdown shows an effect in either case (Figure 2E, Figure 3D). Why is this? Better clarification is required.
3. With respect to insulin signalling, all the experiments bar one indicate that insulin is mediating the effects of Tk. The one experiment that does not is using dilpGS to knock down TkR99D. Is it possible that this driver is simply not resulting in an efficient KD of the receptor? I would be inclined to check this, but as a minimum I would be a bit more cautious with the interpretation of these data.
4. Is it possible to perform at least one lifespan repeat with the other Tk RNAi line mentioned? This would further clarify that there are no off-target effects that can account for the phenotypes.

There are a few other experiments that I could suggest as I think they could enrich the current manuscript, but I do not believe they are essential for publication: 5. The manuscript could be extended with a little more biochemical/cell biology analysis. For example, is it possible to look at Tk protein levels, Tk levels in circulation, or even TkR receptor activation or activation of its downstream signalling pathways? Comparing Ax and CR or Ap and CR one would expect to find differences consistent with the model proposed. This would add depth to the genetic analysis already conducted. Similarly, for insulin signalling - would it be possible to use some readout of the pathway activity and compare between Ax and CR or Ap and CR? 6. The authors use a pan-acetyl-K antibody but are specifically interested in acetylated histones. Would it be possible to use antibodies for acetylated histones? This would have the added benefit that one can confirm the changes are not in the levels of histones themselves. 7. I think the presentation of the results could be tightened a bit, with fewer sections and one figure per section.

Referees cross-commenting

Reviewer 1

I generally agree with this reviewer but for

"I'm convinced by the data showing that FOXO is required for TkRNAi to prevent lifespan shortening by Ap, but FOXO doesn't only respond to insulin signalling and can't be taken by itself to indicate a role for insulin signalling which the authors appear to do here."

To the best of my knowledge, Foxo has only been shown to be required for lifespan extension/modulation by a reduction in insulin-like signalling. I.e. it does respond to other pathways but this is the only one where Foxo activity is known to modulate lifespan.

Reviewer 3

I agree with reviewer 1 that point raised under (1) does not appear strictly required for the conclusions of the manuscript.

Both reviewers 1 and 3:

I have a different take on the results of experiments where IPCs are manipulated. To me, Figure 7D and E show that ablating the IPCs removes the difference between Ax and Ap i.e. the IPCs are involved and insulin-like signalling is likely involved. The fact that RNAi against the TKR99D receptor does not have the same effect, does not matter (the sensing could happen in different neurons). Similarly, dilp expression is only a minor readout of what is happening with insulin-like signalling - dilps are controlled at the level of secretion.

However, I would be happy for the authors to present different arguments and make a reasonable conclusion, which may differ from mine. But I think the arguments I present above should be taken into account.

Significance

The main contribution of this manuscript is the identification of a mechanism that links the microbiota to lifespan. This is very exciting and topical for several reasons:

1) The microbiota is very important for overall health but it is still unclear how. Studying the interaction between microbiota and health is an emerging, growing field, and one that has attracted a lot of interest, but one that is often lacking in mechanistic insight. Identifying mechanisms provides opportunities for therapies. The main impact of this study comes from using the fruit fly to identify a mechanism.

2) It is very interesting that the authors focus on an endocrine mechanism, especially with the clear clinical relevance of gut hormones to human health recently demonstrated with new, effective therapies (e.g. Wegovy).

3) Tk is emerging as an important fly hormone and this study adds a new and interesting dimension by placing TK between microbiota and lifespan.

I think the manuscript will be of great interest to researchers in ageing, human and animal physiology and in gut endocrinology and gut function.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study the authors use a Drosophila model to demonstrate that Tachykinin (Tk) expression is regulated by the microbiota. In Drosophila conventionally reared (CR) flies are typically shorter lived than those raised without a microbiota (axenic). Here, knockdown of Tk expression is found to prevent lifespan shortening by the microbiota and the reduction of lipid stores typically seen in CR flies when compared to axenic counterparts. It does so without reducing food intake or fecundity which are often seen as necessary trade-offs for lifespan extension. Further, the strength of the interaction between Tk and the microbiota is found to be bacteria specific and is stronger in Acetobacter pomorum (Ap) monoassociated flies compared to Levilactobacillus brevis (Lb) monoassociation. The impact on lipid storage was also only apparent in Ap-flies. Building on these findings the authors show that gut specific knockdown is largely sufficient to explain these phenotypes. Knockdown of the Tk receptor, TkR99D, in neurons recapitulates the lifespan phenotype of intestinal Tk knockdown supporting a model whereby Tk from the gut signals to TkR99D expressing neurons to regulate lifespan. In addition, the authors show that FOXO may have a role in lifespan regulation by the Tk-microbiota interaction. However, they rule out a role for insulin producing cells or Akh-producing cells suggesting the microbiota-Tk interaction regulates lifespan through other, yet unidentified, mechanisms.

Major comments:

Overall, I find the key conclusions of the paper convincing. The authors present an extensive amount of experimental work, and their conclusions are well founded in the data. In particular, the impact of TkRNAi on lifespan and lipid levels, the central finding in this study, has been demonstrated multiple times in different experiments and using different genetic tools. As a result, I don't feel that additional experimental work is necessary to support the current conclusions. However, I find it hard to assess the robustness of the lifespan data from the other manipulations used (TkR99DRNAi, TkRNAi in dFoxo mutants etc.) because information on the population size and whether these experiments have been replicated is lacking. Can the authors state in the figure legends the numbers of flies used for each lifespan and whether replicates have been done? For all other data it is clear how many replicates have been done, and the methods give enough detail for all experiments to be reproduced.

Minor comments:

While I feel the conclusions of this study are well supported by the data I found this to be a complex read and in places hard to follow. I feel some work is necessary in the writing to help the reader follow the authors logic. Below I describe some of the issues that confused me and provide some suggestions that I hope the authors will find helpful.

Survival curves The authors state that the lifespan difference between CR and axenic flies disappears with TkRNAi because TkRNAi CR flies are longer lived, rather than because TkRNAi axenic flies are shorter lived. Is this consistent in every TkRNAi experiment? It's hard for the reader to assess this because the relevant lifespan curves are presented on separate plots. I'd encourage the authors to provide lifespan plots that enable comparison between all conditions. For example, in figures 2 and 6 the reader wants to directly compare between RU- and RU+ but can't easily do so. Additional plots could be made available in the supplementary figures showing the comparisons that are not easy to make on the main figures.

Consistent framing of the data Do the interventions shorten lifespan relative to the axenic cohort? Or do they prevent lifespan extension by axenic conditions? Both statements are valid, and the authors need to be consistent in which one they use to avoid confusing the reader. For example, line 325 says TkR86CRNAi prevents lifespan extension in axenic flies. Given the framing in the previous sections, it might be clearer to say that TkR86CRNAi shortens the lifespan of axenic flies to that of CR flies in contrast to TkRNAi and TkR99DRNAi which don't.

The impact of TkRNAi on lipid levels in axenic flies TkRNAi consistently reduces lipid levels in axenic flies (Figs 2E, 3D), essentially phenocopying the loss of lipid stores seen in control conventionally reared (CR) flies relative to control axenic. This suggests that the previously reported role of Tk in lipid storage - demonstrated through increased lipid levels in TkRNAi flies (Song et al (2014) Cell Rep 9(1): 40) - is dependent on the microbiota. In the absence of the microbiota TkRNAi reduces lipid levels. The lack of acknowledgement of this in the text is confusing for the reader because it is inconsistent with the microbiota driving both higher Tk expression and higher lipid storage. If the microbiota increases Tk expression and this results in reduced lipid storage, why does reduced Tk expression also result in reduced lipid storage in axenic flies? This could further highlight the unique impact that the interaction between TkRNAi and the microbiota has on lipid storage, given it reverses both the impact of the microbiota alone and TkRNAi alone. I feel this aspect of the data should be given more attention in the text both for clarity and because it may be telling us something important about the function of Tk. The current framing around pleiotropic effects is valid, and the impact of Tk on lipid storage is clearly independent of its impact on lifespan and so is not central to this study. However, I feel a short additional paragraph to acknowledge this nuance of the data is needed. It can be made clear in the text that further exploration is beyond the scope of the current study.

Role of insulin signalling and insulin producing cells I'm convinced by the data showing that FOXO is required for TkRNAi to prevent lifespan shortening by Ap, but FOXO doesn't only respond to insulin signalling and can't be taken by itself to indicate a role for insulin signalling which the authors appear to do here.

I would expect ablation of IPCs to have the opposite effect to foxo mutation and to increase FOXO activity throughout the organism due to a reduction in Dilp levels and so reduced insulin signalling. So, I have struggled to follow the authors logic in ablating the IPCs and feel a clear statement on what they expected the outcome to be would help the reader. They find that TkRNAi still prevents lifespan shortening by Ap when IPCs are ablated and that TkR99DRNAi in IPCs also doesn't block lifespan shortening by Ap despite reducing the expression of dilp3 and dilp5. To me these data rule out a role for insulin signalling despite the requirement for FOXO and yet the authors conclude that insulin signalling is involved in the response to Ap and TkRNAi, although not obligately (lines 420 - 422 and 511 - 512). Can the authors clarify their logic in concluding a role for insulin signalling, and qualify this conclusion with appropriate consideration of alternative hypotheses? The potential involvement of other signalling inputs to FOXO activity, e.g. immune signalling and JNK, should be acknowledged and warrants some discussion.

Typographical errors:

Incomplete sentence line 121 to 122 - starting "Cox proportional hazards.... and posthoc tests (Fig 2b).

Line 123 "EMMs" - define abbreviation on first use

References to Fig 2b (first given on line 122), should be capitalised to Fig 2B for consistency.

Lines 231 and 317 - the phrase "steady state (microbiota independent) expression" in reference to flyATLAS 2 data could be misleading. The term "microbiota independent" could suggest that expression levels have been shown not to be regulated by the microbiota and this is not the case. The authors should change this to simply state they are referring to steady state expression in conventionally reared flies.

Referees cross-commenting

Below are brief comments on the revision suggestions that reviewers 2 and 3 have requested.

Reviewer 2

1. I agree that confirmation that TkRNAi doesn't impact microbial levels could be helpful and would be straightforward for the authors to do. However, I don't feel it's essential to support the central claims of the paper.
2. I agree.
3. I don't feel that any of these experiments supports a role for insulin signalling, so I don't feel that this additional control is needed.
4. It would be a good addition to have lifespan data from a separate knockdown line for corroboration. However, this has already been done in several different genetic backgrounds through crosses with different driver lines in multiple tissues, so I feel it's unnecessary given the time and resources that lifespan experiments take. There's also the caveat that different RNAi lines can knockdown to different extents so that would have to be assessed as well and if there's a difference it may mean that ultimately not much can be concluded from this additional experiment.
5. A good suggestion, but not straightforward and depends on the availability of the necessary tools, or possibly the generation of new tools. One for a follow up study.
6. I feel this is not important enough to the central findings of the study to warrant the extra work.
7. I agree.

Reviewer 3 1. Imaging calcium signalling is not straightforward unless a lab already has the tools available and optimised. If Tk+ EEs show changes in calcium signalling I'm not convinced that this tells us anything specific to the Tk-microbiota interaction. The point is the role of Tk itself, not the broader activity of the cells that express it. 2. I agree this needs clarification. 3. I agree that this would add depth, if feasible, but feel it's not essential to support the current conclusions. 4. This is a minor point and given the RT-qPCR data and the RNAseq data corroborate each other I'm convinced that Tk levels are elevated. 5. I feel exploring this in males is opening an additional line of enquiry beyond the scope of the current study. Either the phenotypes are the same - in which case what is added? - or they are different but there's no scope to assess why. A good suggestion for a follow up study. 6. No comment. 7. Agreed.

One final comment. It's true that FOXO has only been shown to regulate lifespan in the context of insulin signalling. However, as far as I'm aware it hasn't been shown not to regulate lifespan downstream of it's other activators, this simply hasn't been explored due to the historical focus on insulin signalling in this field. In the context of host-microbiota interactions considering other pathways the activate FOXO, such as immune and JNK signals, would make sense.

Reviewed by Dr Rebecca Clark, Department of Biosciences, Durham University

Significance

Overall, I find the key conclusions of the paper convincing. The authors present an extensive amount of experimental work, and their conclusions are well founded in the data. We have known that the microbiota influence lifespan for some time but the mechanisms by which they do so have remained elusive. This study identifies one such mechanism and as a result opens several avenues for further research. The Tk-microbiota interaction is shown to be important for both lifespan and lipid homeostasis, although it's clear these are independent phenotypes. The fact that the outcome of the Tk-microbiota interaction depends on the bacterial species is of particular interest because it supports the idea that manipulation of the microbiota, or specific aspects of the host-microbiota interaction, may have therapeutic potential.<br /> These findings will be of interest to a broad readership spanning host-microbiota interactions and their influence on host health. They move forward the study of microbial regulation of host longevity and have relevance to our understanding of microbial regulation of host lipid homeostasis. They will also be of significant interest to those studying the mechanisms of action and physiological roles of Tachykinins.

Field of expertise: Drosophila, gut, ageing, microbiota, innate immunity

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Reply to the reviewers

1. General Statements

We thank the reviewers for providing thoughtful and constructive feedback, which will help us improve the clarity and rigor of the paper. On balance, the reviews were positive. Reviewer 1 mentioned that “This is a strong manuscript with few problems and all important findings well justified, indeed this is a nicely polished…..high-quality manuscript,” and that “this paper makes a major breakthrough, showing that cell autonomous defects in hTSCs are very likely at the heart of the pathology observed in GIN-prone murine mutants.” Reviewer 3 stated that “The study is well designed, and the manuscript is very well written. The conclusions are supported by the evidence presented.” Reviewer 2 was less enthusiastic, with main concerns being that “The paper is mostly descriptive and often quite confusing leaving one not much closer to understanding the mechanistic basis for the interesting sex-biased semi-lethal phenotype.” and felt that figure titles/section headers overstated the results, and finally recommended to improve some technical aspects and tempering conclusions. The proposed edits we think address most issues raised by the reviewers either with re-writing or adding data as described below.

In response to reviewer #1 comments:

Major comments:

• I am confused as to the basis of the sex-skewing phenomenon? Is the problem that lack of maternally loaded WT Mcm4 worsens the phenotype, or is the issue that Mcm4C3/C3 dams are less able to retain pregnancies, perhaps being a more inflammatory environment? Also, while there quite consistent evidence for reduced viability of Mcm4C3/C3McmGt/+ progeny, especially for female progeny, how confident can we be that the genotype of the dam vs. sire is important? Notably on a Ddx58 background, the progeny of the Mcm4C3/C3 sire included seven live male Mcm4C3/C3McmGt/+ but no female.

Regarding the first point (sex skewing only when female is C3/C3), we also suspected either: 1) the maternal uterine environment, or 2) reduced oocyte quality. Although not reported in this manuscript, we tested #1 by performing embryo transfer experiments. Transferring 2-cell stage embryos from sex-skewing mating to WT females did not rescue the sex-bias. We then examined oocytes from C3/C3 females. We found evidence for compromised mitochondria and transcriptome disruption. However, we are not sure why this happens (poor follicle support? Oocyte intrinsic phenomenon?). We are reserving these results and additional experiments for another paper, especially since this one mainly deals with GIN and placenta development. If the reviewers feel strongly that the embryo transfer data is crucial, we can include it.

Regarding how confident we are that the genotype of the dam vs. sire is important, this stems from our previous paper by McNairn et al 2019 (the percentage of female C3/C3 M2/+ from sex-skewing mating is 20% compared to 60% from the reciprocal mating), which was quite dramatic. Consistent with this, MCM levels were significantly reduced in the placentae only when the dam was C3/C3 and the sire C3/+ M2/+, but not in the reciprocal cross. The reviewer makes a good observation about the Ddx58 cross; we can only hypothesize that the mutation somehow sensitizes females in this scenario and will make mention of it in the revision. We also realize that we neglected to write in Methods that the Ddx58 allele was coisogenic in the C3H background.

• I'm not sure what Supplementary Figure 6 is showing (faster differentiation of C3 but less TGC?). Regardless, it's hard to draw too much conclusion from one not-very-pretty Western blot. This figure requires both additional replicates and a better explanation of how it fits with the other conclusions of the paper..

We hypothesized that the JZ defect observed in the semi-lethal genotype placentas could arise either from impaired maintenance of the progenitor pool or from reduced capacity of mutant trophoblast progenitors to differentiate into the JZ lineage. The blot in Supplementary Figure 6 was intended as a qualitative demonstration that mutant trophoblast stem cells can differentiate into JZ lineages. We recognize that the figure is not definitive and will revise the text to clarify its purpose. A replicate(s) of the Western will be performed as suggested.

• Supplementary Figure 7F-G is puzzling. Half of the mESCs have gamma-H2AX at all times, including most in S or G2 phase? In Figure S7E, do the quadrants correspond to being negative or positive for gamma-H2AX? At very least, IF images showing clear gamma-H2AX foci would be much more convincing.

The gates for γH2AX FACS analysis were established using negative controls lacking primary antibody. As reported previously, embryonic stem cells display high basal levels of γH2AX staining (Chuykin et al., Cell Cycle 2008; Turinetto et al., Stem Cells 2012; Ahuja et al., Nat Comm 2016), which likely explains the broad signal observed across cell cycle phases. Regardless, we will provide immunofluorescence staining of γH2Ax and foci count in our revision.

• The methods section is well detailed, but it would be ideal to clarify how many replicates each Western Blot or flow cytometry experiment is representative of.

Thanks for the suggestion. We will update this for Fig4 and Fig5.

Minor comments:

• Is it possible that cGAS-STING and RIG pathways act redundantly to cause inflammation and lethality, or that other innate immune components are involved? I don't expect the authors to make compound mutants to test this but at least this possibility should be discussed textually.

We appreciate the reviewer’s point, and had the same suspicion. Supporting this, we will add new RNA-seq analysis of Tmem173 KO placentas revealed elevated inflammatory gene expression compared to C3/C3 M2/+ controls, consistent with potential redundancy or feedback regulation. We will update in supplementary figures to reflect this.

In response to reviewer #2 comments:

Major comments:

A major concern throughout the paper is that conclusions are often overstating their data. The title of figure 2 is "placentae with replication stress have smaller junctional and labyrinth zones". However, there is no measure of replication stress in this figure, just a histological evaluation of the placentae from the different mutants. The title of figure 3 is "Impact of GIN on LZ is less than JZ," but there is no measure of GIN, but instead measurement of number of cells in cell cycle and some bulk RNA-seq analysis. Title of figure 4 is "TSCs with increased genomic instability exhibit abnormal phenotypes." Again there is no measure of GIN, but instead staining of derived TSCs for proliferation, cell death, and a TSC marker. Title of figure 5 is "DNA damage responses and G2/M checkpoint activation drive premature TSC differentiation." However, there does not appear to be a difference in gH2AX between the two mutant genotypes. Checkpoint proteins might be up, but need quantification and reproduction. > 4C is the only marker of differentiation. Importantly, all the analyses here are associations, not connections, so cannot use the word "drive". Similar issues can be raised with a number of the supplementary figures.

The Chaos3 (chromosome aberrations occurring spontaneously 3) model is a well-established system of intrinsic chronic replication stress and GIN. It is characterized by ~20 fold elevation of blood micronuclei (Shima et al., Nature 2007), a hallmark of GIN (Soxena et al., Mol Cell 2022); a destabilized MCM2-7 helicase prone to replication fork collapse (Bai et al., PLoS Genet 2016); and increased mitotic chromosome abnormalities and decreased dormant origins (Kawabata et al., Mol Cell 2011; Chuang et al., Nucleic Acid Res 2012) that are known to cause GIN and replication stress (Ibarra et al., PNAS 2008 ). Also, in our previous work (McNairn et al Nature 2019), we showed that placentae from C3/C3 dams exhibit significantly elevated γH2Ax as well as reduced MCM2 and MCM4 protein levels. In our current study, we also observe elevated γH2Ax in mutant TSCs (C3/C3 and C3/C3 M2/+), consistent with genomic instability. Nevertheless, we acknowledge that in TSCs, we did not formally demonstrate replications stress(RS), so where appropriate, we will advise figure titles, for example to say that “cells/placentae with a GIN or RS genotype.”

We acknowledge the reviewers concern regarding western blots. We will provide quantification and statistics in our revision.

1) A deeper analysis of the cell lines is likely to be the most fruitful path to reveal interesting mechanisms. It is very surprising that there is no phenotype in ESCs. Authors should check for increased apoptosis. Maybe the phenotypic cells are lost. Or do ESCs use different MCMs/mechanisms of DNA replication or are they better able to handle replication stress and GIN? How many passages were the TSCs and ESCs cultured for? Does GIN (i.e. aneuploidy, CNVs) develop in TSCs and ESCs with passaging? How do the MCM mutations impact the molecular identity of the ESC and TSC cells including their heterogeneity in the population.

We assessed apoptosis using cleaved caspase 3 flow cytometry in mutant ESCs and observed no difference compared to controls (we will add this data as Supplementary Fig. 7).

We believe there are intrinsic differences in TSCs and ESCs in their ability to respond to and counteract replication stress and DNA damage. ESCs are known to license more replication origins than somatic cells at a higher rate, which protects them from short G1-induced replication stress (Ahuja et al., Nat Comm 2016; Ge et al., Stem Cell Rep 2015; Matson et al., eLife 2017). Human placental cells physiologically exhibit high levels of mutation rate and chromosomal instability in vivo (Coorens et al., Nature 2021). Supporting this, Wang, D., et al (Nat Comm 2025) reported that several cell cycle and DDR regulators are differentially expressed in human TSCs vs human pluripotent stem cells. Whether such transcriptional differences directly contribute to functional outcomes remains to be determined.

All experiments in this study were conducted using early-passage ESCs and TSCs (i.e. Finally, we showed that close to 90% mutant ESCs are KLF4+ (a naive pluripotency marker) whereas EOMES+ cells were significantly reduced in TSCs carrying the GIN genotype (Fig. 4E–F and Supplementary Fig. 7), highlighting lineage-specific differences.

Minor Comments:

1) There is a lack of quantification and repeats for all Westerns. At minimum there should be three repeats for each experiment, quantification including normalization to a reference protein, and stats confirming any proposed differences between conditions.

We will update our revision with quantification and statistics for western blots.

2) I would recommend moving the results in supp table 1 to figure 1. While negative, they are the newer results. The results shown in current figure 1 are essentially a reproduction of their previous work.

The placental observations presented in Fig.1 are new. In particular, the placental and embryonic weight measurements graphed in Fig1B and C have not been published by our group. Fig1A reproduces our previous observation on embryo viability in GIN mutants (McNairn et al., Nature 2019), while the schematic was provided for better flow and readability given the complex mating schemes. We are agnostic on the Suppl Table 1. It could be changed to a new Table 1 in the main section depending on the journal.

In response to reviewer #3 comments:

Major Comments

While the inclusion of bulk RNAseq data of whole placental tissue is appreciated, the interpretation of the results is somewhat problematic, as it is acknowledged that the cell type composition of the placentas is drastically different between groups. Making conclusions based upon GSEA analysis of two different groups with drastically different cell type composition is somewhat misleading, as based on the results, it is a direct reflection of the cell types present. It would be more helpful to perform cell type deconvolution of the RNAseq data to estimate the proportion of each cell type within the bulk samples and compare that to what is seen histologically and not dive too deeply into the pathways since the results could just be a reflection of the cell types e.g. angiogenesis pathways from more endothelial cells. Additionally, the RNAseq data can be leveraged to look at expression of inflammatory genes by sex, which may show interesting patterns based on the other results.

We agree that the representation of cell types in the placenta is problematic especially for underrepresented genes. We propose to use the BayesPrism tool (Chu et al., Nat Cancer 2022) to deconvolute bulk RNA-seq for better representation of transcriptional changes in the placenta.

Section: GIN impairs trophoblast stem cell establishment and maintenance. To support the assertion in the first paragraph, beyond measuring apoptosis, it would be helpful at this stage to look at RNA expression levels indicative of the activation of DNA damage checkpoint genes

We have performed RNA-seq on mutant ESC and TSCs and are in the process of data analysis. We will update these results in the revision.

Please include additional methodological details in the methods section on the statistical analysis done for differential expression analysis. Specifically, what type of normalization was used, if lowly expressed genes were filtered out and at what cutoff, what statistical model was used (did you include covariates?), what comparisons were made? Did you stratify by sex? What cutoff was used for statistical significance? Did you perform multiple testing correction?

We will update RNA-Seq data analysis methods in our full revision.

2. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer #1 comments:

• Supplementary Table 1. would be enhanced greatly showing comparable tables for Mcm4C3/C3 x Mcm4C3/+McmGt/+ in mice without the Tmem173 or Ddx58 mutations. It is fine to recycle data from McNairn 2019 here, as long as the source is indicated, but a comparison is needed.

Thanks for pointing this out. We have updated this suggestion in Supp table 1.

• In Figure S3E-F, is the box above each graph supposed to show the genotype of the dam?

Yes. Thanks for pointing this out. We have added a description in the figure legend to make it clear.

• "Indeed, the placenta and embryo weights of E13.5 Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ animals were significantly improved vs. Mcm4C3/C3 Mcm2Gt/+ animals, rendering them similar to Mcm4C3/C3 littermates (Fig. 6A-C). The JZ (but not LZ) area in Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ placentae also increased to the level of Mcm4C3/C3 littermates (Fig. 6D-H)." There are two problems here. First, the figure calls are wrong. Second, the description of the data is not quite right, it looks like the C3/C3 and C3/C3 M2/+ M3/+ LZs are a similar size to each and are statistically indistinguishable.

Thanks for catching this. We have updated these in the main text.

*Reviewer #2 comments: *

Minor comment

• Need to review citations to figures. For example, no citations are made to figure 4a and 4c.

Thanks for catching this. We have updated the text.

Reviewer #3 comments:

Define the first use of >4C DNA content to help readers understand this potentially unfamiliar term.

We have edited this part to indicate cells with more than 4C DNA content for better clarity.

iDEP tool - please include citation to manuscript instead of link

We have updated this citation.

Check citations. Some citations to BioRxiv that are now published e.g. 13.

We have updated this citation.

3. Description of analyses that authors prefer not to carry out

Reviewer 2

2) Along similar lines, most of the in vivo phenotypic analyses are performed at E13.5, long after defects are likely beginning to express themselves especially given that they see phenotypes in the TSCs, which represent the polar TE of a E4.5. To understand the primary defects of the in vivo phenotype, they should be looking much earlier. Supplemental figure 5 is a start but represents a rather superficial analysis.

The peri-implantation period, namely E4.5, represents a “black box” of embryonic development given that this is a critical stage for implantation. Aside from being an extremely difficult stage to analyze technically, we don’t think it is essential to the conclusions (or doable in a timely manner), especially given the use of TSCs. If we complete EdU studies on E6.5 embryos, we will include them.

3) Fig. 6 would benefit from evidence that MCM3 mutant is rescuing MCM4 levels in the chromatin fraction of cells and the DNA damage phenotype.

The genetic evidence presented is strong, and although we didn’t do the suggested experiment, we feel that our previous studies (McNairn et al., Nature 2019 and Chuang et al., PLoS Genet 2010) on the effects of MCM3 as a nuclear export factor (as it is in yeast (Liku et al., Mol Biol Cell 2005)) are a reasonable basis for not repeating such experiments. Furthermore, we are no longer maintaining the Mcm3 line and it would take over a year to reconstitute and rebreed triple mutants.

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Referee #3

Evidence, reproducibility and clarity

This manuscript examines chronic replication stress-mediated genomic instability in placental development and concludes that it disrupts placental development in mice. The study is well designed and the manuscript is very well written. The conclusions are supported by the evidence presented. The manuscript would be improved by addressing the comments below.

Major Comments:

• While the inclusion of bulk RNAseq data of whole placental tissue is appreciated, the interpretation of the results is somewhat problematic, as it is acknowledged that the cell type composition of the placentas is drastically different between groups. Making conclusions based upon GSEA analysis of two different groups with drastically different cell type composition is somewhat misleading, as based on the results, it is a direct reflection of the cell types present. It would be more helpful to perform cell type deconvolution of the RNAseq data to estimate the proportion of each cell type within the bulk samples and compare that to what is seen histologically and not dive too deeply into the pathways since the results could just be a reflection of the cell types e.g. angiogenesis pathways from more endothelial cells. Additionally, the RNAseq data can be leveraged to look at expression of inflammatory genes by sex, which may show interesting patterns based on the other results.

• Section: GIN impairs trophoblast stem cell establishment and maintenance. To support the assertion in the first paragraph, beyond measuring apoptosis, it would be helpful at this stage to look at RNA expression levels indicative of the activation of DNA damage checkpoint genes

Minor Comments:

• Define the first use of >4C DNA content to help readers understand this potentially unfamiliar term.

• Please include additional methodological details in the methods section on the statistical analysis done for differential expression analysis. Specifically, what type of normalization was used, if lowly expressed genes were filtered out and at what cutoff, what statistical model was used (did you include covariates?), what comparisons were made? Did you stratify by sex? What cutoff was used for statistical significance? Did you perform multiple testing correction?

• iDEP tool - please include citation to manuscript instead of link

• Check citations. Some citations to BioRxiv that are now published e.g. 13.

Significance

The manuscript concludes that replication-stress induced genomic instability impairs placental development in mice. This is a significant advance in the field, as it mechanistically links genomic instability to placental development with further study needed in human trophoblast to establish clinical relevance. Strengths of this manuscript include solid study design, interpretation and presentation (both writing and figures). Weakness of the manuscript reside primarily in the RNAseq analysis results, methods and interpretation. The manuscript is of interest to audiences with interests in genome maintenance, development and placental biology. To contextualize this reviewer's point of view, this review is based on expertise in genomics, computational biology and placental biology.

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Referee #2

Evidence, reproducibility and clarity

The manuscript, "Chronic replication stress-mediated genomic instability disrupts placenta development in mice" by Munisha et al follows up a 2019 paper in Nature by the same group where they show that mutations to the MCM genes lead to a sex-skewed semi-lethal phenotype starting after embryonic day 9.5 and extending to birth. In the paper, they hypothesized that the semi-lethality is secondary to genomic instability (GIN) driven inflammation due to activation of the innate immune pathways sensing cytoplasmic DNA. In this paper, they start by disproving that hypothesis and then go on to present data arguing lethality is due to a placental development defect rather than inflammation. The paper is mostly descriptive and often quite confusing leaving one not much closer to understanding the mechanistic basis for the interesting sex-biased semi-lethal phenotype that was described in their original paper. The most interesting aspect of the paper is the derivation of TSC and ESCs and initial analysis suggesting that the TSCs are more sensitive to the MCM mutations, but the analysis is rather shallow. Importantly it is unclear how the phenotype explains the sex-skewing of the phenotype. Are the TSC phenotypes sex-skewed and if so why? Also, why is the JZ and especially GlyTCs most effected?

A major concern throughout the paper is that conclusions are often overstating their data. The title of figure 2 is "placentae with replication stress have smaller junctional and labyrinth zones". However, there is no measure of replication stress in this figure, just a histological evaluation of the placentae from the different mutants. The title of figure 3 is "Impact of GIN on LZ is less than JZ," but there is no measure of GIN, but instead measurement of number of cells in cell cycle and some bulk RNA-seq analysis. Title of figure 4 is "TSCs with increased genomic instability exhibit abnormal phenotypes." Again there is no measure of GIN, but instead staining of derived TSCs for proliferation, cell death, and a TSC marker. Title of figure 5 is "DNA damage responses and G2/M checkpoint activation drive premature TSC differentiation." However, there does not appear to be a difference in gH2AX between the two mutant genotypes. Checkpoint proteins might be up, but need quantification and reproduction. > 4C is the only marker of differentiation. Importantly, all the analyses here are associations, not connections, so cannot use the word "drive". Similar issues can be raised with a number of the supplementary figures.

Major Comments:

1) A deeper analysis of the cell lines is likely to be the most fruitful path to reveal interesting mechanisms. It is very surprising that there is no phenotype in ESCs. Authors should check for increased apoptosis. Maybe the phenotypic cells are lost. Or do ESCs use different MCMs/mechanisms of DNA replication or are they better able to handle replication stress and GIN? How many passages were the TSCs and ESCs cultured for? Does GIN (i.e. aneuploidy, CNVs) develop in TSCs and ESCs with passaging? How do the MCM mutations impact the molecular identity of the ESC and TSC cells including their heterogeneity in the population.

2) Along similar lines, most of the in vivo phenotypic analyses are performed at E13.5, long after defects are likely beginning to express themselves especially given that they see phenotypes in the TSCs, which represent the polar TE of a E4.5. To understand the primary defects of the in vivo phenotype, they should be looking much earlier. Supplemental figure 5 is a start but represents a rather superficial analysis.

3) Fig. 6 would benefit from evidence that MCM3 mutant is rescuing MCM4 levels in the chromatin fraction of cells and the DNA damage phenotype.

Minor Comments:

1) There is a lack of quantification and repeats for all Westerns. At minimum there should be three repeats for each experiment, quantification including normalization to a reference protein, and stats confirming any proposed differences between conditions.

2) I would recommend moving the results in supp table 1 to figure 1. While negative, they are the newer results. The results shown in current figure 1 are essentially a reproduction of their previous work.

3) Need to review citations to figures. For example, no citations are made to figure 4a and 4c.

Significance

As is, the study does not provide much new insight or understanding of how the MCM mutants are driving the sex-skewed semi-lethal phenotype. It would likely take much effort (months) to reach such a goal. However, without such effort, it is unclear what the significance of the story is. It does make the observation that the placenta appears to be impacted more severely and earlier than then the embryo, and that within the placenta, certain zones and cell types are more vulnerable. The reasons for these differential impacts are unclear though.

If the authors choose not to dig deeper as suggested in the major comments, then at a minimum it would be important to soften their conclusions as raised in the summary and at least perform experiments/edits proposed in minor comments.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In a previous paper (McNairn et al. 2019 "Female-biased embryonic death from inflammation induced by genomic instability" Science), the Schimenti lab demonstrated that mouse embryos with hypomorphic mutations of the heterohexameric minichromosome maintenance complex, mutations that cause increased genomic instability (GIN), show reduced embryonic viability, with greater loss of female embryos and some parent-of-origin effect. Treatment with immunosuppressants, including ibuprofen and testosterone, partially rescued the observed lethality.

In this new manuscript, the Schimenti lab demonstrates that these GIN-prone mutants feature smaller placentas with fewer cells. Mutations that interfere with the ability of the innate immune system to respond to micronuclei (a consequence of GIN) have no protective effect. Munisha and colleagues then demonstrate that MCM-mutant TSCs are harder to derive and show elevated apoptosis and a greater propensity for differentiation. The mutant TSCs show CHK1 phosphorylation, P53 phosphorylation and higher P21 levels, all consistent with a response to DNA damage. Downstream of this, they also show loss and inhibition of CDK1, which is already established to cause G2/M arrest (generally) and endoreduplication (specifically in trophoblast). The authors advance a model in which GIN results in loss of the TSC pool by apoptosis, cell cycle arrest and premature differentiation, resulting in smaller placentas and particularly fewer junctional zone cells. How this causes inflammation is less clear, but inflammation appears to be a downstream effect rather than cause of poor placentation.

Major comments:

This is a strong manuscript with few problems and all important findings well justified, indeed this is a nicely polished manuscript for something just entering peer review. There are a few unclear points textually and a couple places in the supplementary figures where better data quality would help, but generally it is a high-quality manuscript.

• I am confused as to the basis of the sex-skewing phenomenon? Is the problem that lack of maternally loaded WT Mcm4 worsens the phenotype, or is the issue that Mcm4C3/C3 dams are less able to retain pregnancies, perhaps being a more inflammatory environment? Also, while there quite consistent evidence for reduced viability of Mcm4C3/C3McmGt/+ progeny, especially for female progeny, how confident can we be that the genotype of the dam vs. sire is important? Notably on a Ddx58 background, the progeny of the Mcm4C3/C3 sire included seven live male Mcm4C3/C3McmGt/+ but no female.

• I'm not sure what Supplementary Figure 6 is showing (faster differentiation of C3 but less TGC?). Regardless, it's hard to draw too much conclusion from one not-very-pretty Western blot. This figure requires both additional replicates and a better explanation of how it fits with the other conclusions of the paper..

• Supplementary Figure 7F-G is puzzling. Half of the mESCs have gamma-H2AX at all times, including most in S or G2 phase? In Figure S7E, do the quadrants correspond to being negative or positive for gamma-H2AX? At very least, IF images showing clear gamma-H2AX foci would be much more convincing.

• The methods section is well detailed, but it would be ideal to clarify how many replicates each Western Blot or flow cytometry experiment is representative of.

The required additional experiments re: Supplementary Figure 6 and 7 could be conducted in a couple of months.

Minor comments:

• Supplementary Table 1. would be enhanced greatly showing comparable tables for Mcm4C3/C3 x Mcm4C3/+McmGt/+ in mice without the Tmem173 or Ddx58 mutations. It is fine to recycle data from McNairn 2019 here, as long as the source is indicated, but a comparison is needed.

• Is it possible that cGAS-STING and RIG pathways act redundantly to cause inflammation and lethality, or that other innate immune components are involved? I don't expect the authors to make compound mutants to test this but at least this possibility should be discussed textually.

• In Figure S3E-F, is the box above each graph supposed to show the genotype of the dam?

• "Indeed, the placenta and embryo weights of E13.5 Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ animals were significantly improved vs. Mcm4C3/C3 Mcm2Gt/+ animals, rendering them similar to Mcm4C3/C3 littermates (Fig. 6A-C). The JZ (but not LZ) area in Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ placentae also increased to the level of Mcm4C3/C3 littermates (Fig. 6D-H)." There are two problems here. First, the figure calls are wrong. Second, the description of the data is not quite right, it looks like the C3/C3 and C3/C3 M2/+ M3/+ LZs are a similar size to each and are statistically indistinguishable.

Significance

I partially discussed the above in the summary, but this paper makes a major breakthrough, showing that cell autonomous defects in hTSCs are very likely at the heart of the pathology observed in GIN-prone murine mutants.

Some questions go unsolved. Why are TSCs more prone to die in response to GIN than mESCs, particularly in light of the general observation that karyotypic abnormality is more common in placental lineage? How does the placental abnormality give rise to inflammation? No manuscript can answer every question, and I think this is a mature manuscript that can be published in a good journal with limited modifications.

I am an expert on gene regulation in placental development, with somewhat less expertise in the DNA damage field. The placenta field will find this paper interesting, as will the DNA damage field. There are also ramifications for cancer research. The question of why some cells tolerate high levels of DNA damage and others die is very relevant to cancer.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

SUMMARY

In this study, Fernandes and colleagues addressed the question of the role of micro-RNAs in regulating the coupling between organ growth and developmental timing. Using Drosophila, they identified the conserved micro-RNA miR-184 as a regulator of the developmental transition between juvenile larval stages and metamorphosis. This transition is under the control of the steroid hormone Ecdysone, and has been shown to be modulated in case of abnormal tissue growth to adjust the duration of larval growth in response to developmental perturbations. The relaxin-like hormone Dilp8 has been identified as a key secreted factor involved in this coupling. Here, the authors show that miR-184 is involved in the regulation of Dilp8 expression both in physiological conditions and upon growth perturbation. They propose that this function is carried out in imaginal tissues, where miR-184 levels are modulated by tissue stress. While several factors have already been involved in triggering sharp dilp8 induction at the transcriptional level, this study adds another level of complexity to the regulation of Dilp8 by proposing that its expression is fine-tunned post-transcriptionally through repression by miR-184.

__MAJOR COMMENTS______

Overall, the manuscript is well organized, and the logics of the experimental plan well presented. The results are clear, and I appreciate the quality of the pupariation curves. However, I believe that two main conclusions of the paper are not fully supported by the results presented in the figures: the direct regulation of dilp8 3'UTR by miR-184, and the specificity of this regulation in imaginal discs. Here I develop in more details these two aspects.

Comment 1) The strategy of the 3'UTR sensor is not fully optimized. Indeed, in most experiments, qRT-PCR is used to assess dilp8 expression levels, although it reflects both transcriptional and post-transcriptional. Importantly, to show that post-transcriptional regulation is involved in the response to tissue damage, the levels of the 3'UTR sensor should be analyzed in discs expressing RAcs (showing at the same time that the response is cell-autonomous in the discs). The expected upregulation of the sensor should be prevented by simultaneous expression of miR-184. This approach would shed light on the relative contribution of transcriptional versus post-transcriptional regulation of dilp8 in response to growth perturbation.

Response: We thank the reviewer for this comment. We agree that qRT-PCRs do not distinguish between transcriptional and post-transcriptional changes of dilp8 levels, in response to changes in miR-184 levels and tissue damage. In addition to the qRT-PCR data we have looked at dilp8-3’UTR-GFP reporter in response to overexpression of miR-184 in the wingdisc using patched-Gal4 driver, which show downregulation of the GFP reporter in the ptc domain (Fig 4C-D’). This suggests that dilp8 mRNA is a direct target of miR-184 by post-transcriptional regulation through its 3’UTR. Further, to confirm the specificity of the effect of miR-184 on dilp8-3’UTR, we generated a dilp8-3’UTR mutant in which the single target site for miR-184 was mutated. We show that the mutated dilp8-3’UTR reporter doesn’t show any regulation in response to miR-184 overexpression in the ptc domain of the wingdisc (Fig. 4E, E’, F, F’). This experiment confirms the specificity of the dilp8-3’UTR regulation by miR-184.

As suggested by the reviewer we analysed dilp8-3’UTR-GFP reporter expression by overexpressing RicinA using ptcGAL4 driver in the wing imaginal disc (Fig. S6F-G’). We observed a slight but consistent increase in the dilp8-3’UTR-GFP reporter expression, indicating post-transcriptional regulation of dilp8 expression in response to tissue damage. However, the increase of reporter GFP levels observed in this experiment in response to tissue damage is mild (Fig. S6F-G’) than expected based on the qRT-PCR results (Fig S6A and B). We have added this new data to the manuscript (Fig. S6F-G’).

We propose the following reasons to explain this result:

a) both transcriptional and post-transcriptional regulation of dilp8 mRNA in response to developmental perturbations

b) the data on 3’UTR reporter GFP is specifically from the ptc domain expression of RicinA, whereas for dilp8 transcript levels we have expressed RicinA in all larval imaginal tissues, or in the entire wing imaginal disc, which could be one of the reasons for the stronger effect seen on dilp8 mRNA levels

c) we are not certain if the tubulin-promoter driven dilp8-3’UTR GFP reporter reflects post-transcriptional regulation of dilp8 by miR-184 efficiently in comparison to qRT-PCR. This is especially as the reporter-GFP-3’UTR will be expressed at very high levels due to the tubulin promoter, a majority of this reporter-GFP mRNA may not be relieved from degradation due to the moderate suppression of miR-184 in response to RicinA overexpression.

Thus, our experiments suggest that dilp8 levels are regulated post-transcriptionally by miR-184 which contributes to pupariation delays in response to tissue damage. In support of this, we could rescue pupariation delays and dilp8 induction caused by RicinA expression using overexpression of miR-184 (Figs 5B, C). Thus, we confirm that the effect of post-transcriptional regulation by miR-184 during developmental perturbations also contributes to dilp8 induction and pupariation delays. Unfortunately, due to experimental limitations we could not perform simultaneous expression of RicinA and miR-184 to evaluate the rescue of dilp8-3’UTR-GFP sensor expression. The levels of dilp8-3’UTR sensor GFP is reduced efficiently by miR-184 overexpression (Fig 4D), which prevented us from attempting the rescue of the moderate increase of dilp8-3’UTR GFP levels in response to RicinA.

Comment 2) In my opinion, the use of a 3'UTR sensor is not sufficient to conclude that the regulation by miR-184 is direct, as miR-184 could also regulate an intermediate factor that acts on dilp8 post-transcriptional regulation. To solve this issue, a common strategy is to generate a 3'UTR sensor with mutated binding sites that should abolish the regulation by miR-184. This mutated 3'UTR might also respond differently to tissue damage, which would strongly support the conclusions of the study.

Response: We couldn’t agree more with the reviewer, this comment is addressed in the response to comment 1. We have confirmed the specificity of regulation of dilp8-3’UTR by miR-184 using target site mutated dilp8-3’UTR (new figures added to the manuscript Fig. 4E, E’, F, F’). We tested if the changes in dilp8 mRNA levels in response to tissue damage is post-transcriptional mediated by miR-184. We observe that there is a slight, but consistent increase of dilp8-3’UTR GFP reporter levels in the ptc domain of wingdisc in response to RicinA expression, suggesting a role for miR-184 mediated post-translational regulation of dilp8. However, we have not yet tested the mutated dilp8-3’UTR GFP reporter in response to tissue damage.

Comment 3) Concerning the tissue-specific regulation of Dilp8 by miR-184, these results need to be strengthened. Indeed, this comes mostly from phenotypes observed with rn-GAL4. Although this is a classical tool for driving expression in imaginal discs, rn-GAL4 also drives strong expression in other tissues that could contribute to triggering a delay, such as the CNS and part of the gut (proventriculus). In our hands, some growth phenotypes in the wing obtained with rn-GAL4 could be fully reverted by blocking GAL4 in the CNS indicating that the phenotype was not wing-specific. Importantly, miR-184 seems to be highly expressed in the CNS according to FlyBase, reinforcing the possibility that it plays a role in this organ. Here I propose approaches to confirm that miR-184 mediated regulation of dilp8 and developmental timing indeed occur in the discs:

- Another driver with less secondary expression sites could be used (pdmR11F02-GAL4), or rn-GAL4 could be combined with an elav-GAL80 to prevent expression in most neurons. - The authors could identify the source of Dilp8 upregulation in miR-184 mutants using tissue-specific qRT-PCR instead of whole larvae expression like in Fig 4A-B. - This tissue-specific upregulation could be functionally tested using a rescue experiment, in which the delay observed in miR-184 mutants could be rescued by disc-specific downregulation of Dilp8 (using pdm2-GAL4 for instance).

Response: We are thankful to the reviewer, and agree that it is important to show that the effects that we see using rn-Gal4 are specific to imaginal discs, and not due to an effect in CNS. We tested this by expressing miR-184 sponge in the CNS. Though miR-184 is highly expressed in the larval CNS, downregulation of miR-184 specifically in the pan-neuronal background using elav-GAL4 led to no effects on pupariation timepoint. We have added this as supplementary data Figure S4. Therefore, we believe that the miR-184 downregulation phenotype in the rnGAL4 background can be mainly attributed to its role in the imaginal discs. In addition, as suggested by the reviewer we have also demonstrated that downregulation of miR-184 in the imaginal discs using rnGAL4 driver leads to an increase in dilp8 expression (Fig S5B). Thus confirming that dilp8 mRNA is enhanced in the imaginal discs by blocking miR-184.

OPTIONAL: Because it is known that dilp8 is strongly regulated at the transcriptional level, the relative input from post-transcriptional upregulation is an important question arising from this study. Although it might be a more long-term approach, I believe that generating a Dilp8 mutant lacking its 3'UTR or, even better, with mutated miR-184 binding sites, would shed light on the role of this regulation for the response to growth perturbation and/or developmental stability (fluctuating asymmetry).

Response: We thank the reviewer for the suggestion. This would have been an interesting experiment to carry out especially in the context of fluctuating asymmetry.

MINOR COMMENTS

1. __ I think that a number of results could be moved to SI as they are either controls, or reproduce published data without bringing novelty. For instance, results in Fig 5A-D are similar to data published by Sanchez et al, as stated in the text. Fig6A as well.__

__Response: __We thank the reviewer for this suggestion, Fig. 5A-D, and F has been moved to Fig. S6A-E. We have also moved data from Fig. 6 to Fig. 5, as a result Fig 6 A-D has become Fig. 5 B-D.

__ Fig 6D is quite mysterious, as it suggests that basal JNK activation regulates miR-184, which is different from a context of tissue damage. I think that this result could be removed. Alternatively, if the authors want to dig in that direction, more experiments should be provided, such as bskDN expression in an RAcs context and the effects on miR-184 levels and the 3'UTR sensor (since transcript levels are already published).__

Response: We would like to clarify that our experiments suggest that endogenous JNK signalling negatively regulates miR-184, as blocking basal JNK signalling using bskDN increased the levels of miR-184 (changed to Fig 5D). Enhanced JNK signalling has been reported to be involved in tissue damage responses, and we propose that RicinA mediated increase in JNK signalling leads to the reduction of miR-184 (changed to Fig 5A, S6D-E). However, we are not strongly implying this as we did not co-express RicinA and bskDN to show that JNK signalling is responsible for the drop in miR-184 levels in response to tissue damage. We thank the reviewer for seeking this explanation, we have rewritten the results section to improve clarity.

__ The references related to Dilp8 should be checked more in detail in the intro and discussion. About Dilp8 and developmental stability: remove the ref to Colombani et al 2012, instead put Boone et al 2016 and add Blanco-Obregon et al 2022 (in addition to Garelli et al 2012 who initially identified this phenotype. About Lgr3 as the receptor for Dilp8: add Colombani et al, Current Biology 2015, and cite here Vallejo et al 2015, Garelli et al 2015. Among the important transcriptional regulators of Dilp8, Xrp1 could be mentioned (Boulan et al 2019, Destefanis et al 2022) as it plays a complementary function to JNK depending on the type of tissue stress.__

__Response: __We are really sorry for the glaring errors in citing appropriate references. We thank the reviewer for correcting this for us. We have made necessary changes to the text.

Significance

GENERAL ASSESSMENT This study provides convincing data showing that the conserved microRNA miR-184 plays a role in regulating developmental timing in Drosophila through modulating the levels of Dilp8, a key factor in the coupling between tissue growth and developmental transitions. The results are convincing, but the general conclusions of the paper need to be strengthened regarding the direct regulation of dilp8 by miR-184 and the tissue-specificity of this interaction.

ADVANCE Dilp8 is a key factor that modulates growth and timing in response to developmental perturbations and contributes to developmental precision in physiological conditions. As such, its regulation has been studied by different groups in the last decade, leading to the identification of several inputs for its transcriptional regulation. Here, the authors uncover a post-transcriptional regulation by miR-184, adding another level of regulation of Dilp8 that contribute to ensuring proper regulation of developmental timing, and opening the possibility that miR-184 might play similar roles in other species.

AUDIENCE This study is of interest for researchers in the field of basic science, with a focus on developmental timing, tissue damage and biological function of microRNAs.

REVIEWER EXPERTISE Drosophila, growth control, developmental timing, Dilp8.

Reviewer #2

Evidence, reproducibility and clarity

Drosophila has helped to characterize the mechanisms that coordinate tissue growth with developmental timing. The insulin/relaxin-like peptide Dilp8 has been identified as a key factor that communicates the abnormal growth status of larval imaginal discs to neuroendocrine neurons responsible for regulating the timing of metamorphosis. Dilp8, derived from imaginal discs, targets four Lgr3-positive neurons in the central nervous system, activating cyclic-AMP signaling in an Lgr3-dependent manner. This signaling pathway reduces the production of the molting hormone, ecdysone, delaying the onset of metamorphosis. Simultaneously, the growth rates of healthy imaginal tissues slow down, enabling the development of proportionate individuals.

In this manuscript "miR-184 modulates dilp8 to control developmental timing during normal growth conditions and in response to developmental perturbations" by Dr. Varghese and colleagues, the authors identify a new post transcriptional regulator of Dilp8. The authors show that miR-184 plays a pivotal role in tissue damage responses by inducing dilp8 expression, which in turn delays pupariation to allow sufficient time for damage repair mechanisms to take effect.

Major points:

Comment 1) In most of the experiments for percentage of pupariation, the 50% pupariation in control is around 110 hours AED in figures 1, 2 and 3. In figures 5 and 6 using the UAS Ricin, the controls are more around 90 hours AED. Why this discrepancy?

Response: We thank the reviewer for asking for this clarification. The former experiments for Figs 1-3 were carried out at 25oC while the latter experiments with a cold sensitive version of RicinA (UAS-RAcs), Figs 5 and 6 (now changed to Figs. 5 and S6 as suggested by reviewer #1) were carried out at 29oC (permissive temperature). This difference in temperature has led to alterations in pupariation timing. We apologise for not having mentioned this in the text, now we have made necessary corrections to the methods section clearly indicating this.

Comment 2) What is the mechanism behind the expression of miR-184 in stress conditions? Is miR-184 also implicated in other conditions giving rise to a developmental delay (X-rays irradiation or animal bearing rasV12, scrib-/- tumors)?

Response: We thank the reviewer for these questions.

a) In response to developmental perturbations by RicinA, we believe that activation of JNK signalling controls miR-184 expression. We propose this as our experiments show that imaginal disc damage leads to enhancement of JNK signalling and increase in dilp8 mRNA levels (as reported earlier by Colombani et al 2012; Sánchez et al 2019), and a simultaneous reduction of miR-184 (Figs. S6A, D, E). We also have performed new experiments to show that in response to RicinA expression in the wingdisc there is moderate increase in the dilp8-3’UTR-GFP sensor expression (Figs. S6F-G’), indicating a post-transcriptional regulation of dilp8 expression in response to tissue stress. We also show that RicinA induced dilp8 expression and pupariation delay can be rescued by increasing miR-184 levels (Fig 5B and C), suggesting that the reduction of miR-184 in response to tissue damage contributes to the damage responses. In a separate experiment we show that blocking the endogenous JNK pathway by the expression of bskDN enhances miR-184 levels, suggesting that miR-184 is under the regulation of JNK signalling (Fig 5D). Hence, we speculate that during tissue stress, activation of JNK signalling leads to a reduction of miR-184 levels which contributes to regulating the levels of dilp8 post-transcriptionally and resulting in pupariation delays. The text has been modified to explain this better.

b) In a previous paper by Shu et al., 2017 (https://doi.org/10.18632/oncotarget.22226) decreased expression of miR-184 was observed in a lglRNAi; RasV12 tumor background. Apart from this various studies have shown that dilp8 levels increase in response to tumour, radiation stress, apoptosis, and tissue damage (Yeom et al 2021, Ray et al 2019, Demay et al 2014, Katsuyama et al 2015, Colombani et al 2012, Garelli et al 2012). Whether the regulation of dilp8 by miR-184, occurs in these backgrounds is yet to be tested. We have now discussed this possibility in the manuscript.

Comment 3) dilp8 mutant animals have also been shown to be more resistant to starvation or desiccation (https://doi.org/10.3389/fendo.2020.00461). Is miR-184 implicated in this answer?

Response: We thank the reviewer for this question. In our earlier experiments miR-184 has been demonstrated to be regulated by nutrition in the larval stages and lack of miR-184 led to enhanced larval death in response to diet restriction (Fernandes et al., 2022). miR-184 was also demonstrated to play a role in the insulin producing cells (IPCs) in regulating lifespan (Fernandes & Varghese., 2022). In the current work, we propose miR-184 to act upstream of dilp8 in response to stress stimuli. Hence, it is possible that miR-184 might be involved in responses to starvation and desiccation stress in the adult female flies, by regulating dilp8 levels post-transcriptionally. However, it has not been tested yet if the miR-184 regulation of dilp8 plays a role in resistance to starvation or desiccation in adult females, as this was not within the scope of the current study. We have now added this reference in the discussion section.

Comment 4) dilp8 expression has been also shown to be regulated by Xrp1 in response to ribosome stress (https://doi.org/10.1016/j.devcel.2019.03.016). This paper should be included in the manuscript. Is it possible that the expression levels of miR184 are regulated by Xrp1?

Response: We thank the reviewer for the suggestion and have incorporated the reference into the paper. During ribosome stress in the larval imaginal discs the stress-response transcription factor Xrp1 acts through dilp8 in regulating systemic growth. We agree with the reviewer, it is possible that expression of miR-184 is regulated by Xrp1. Currently we have not explored this possibility. We have now added this to the discussion section.

Minor points:

1. __ Does the overexpression of miR184 induce an increased fluctuating asymmetry?__

Response: We thank the reviewer for asking this question. The role of dilp8 in the fluctuation asymmetry is only observed in the dilp8 hypomorphic mutant background. To replicate this we would have to overexpress miR-184 in either the whole larvae or in the wing discs. Unfortunately overexpression of miR-184 in the wing discs (using rnGAL4) leads to pupal lethality while as overexpression of miR-184 in the whole larvae leads to embryonic lethality and therefore we were not be able to conclude from our experiments if miR-184 overexpression induces increased fluctuating asymmetry.

2. There are 2 references Colombani et al. (2012 for Dilp8 and 2015 for Lgr3). Can you double check that they are used accordingly

Response: We thank the reviewer for pointing these errors out and we have incorporated these changes into the paper.

Significance

Altogether, the paper present compiling lines of evidence supporting the proposed model. The experiments are well designed and are convincing. The papers is interesting and relevant for a broad audience.

__Reviewer #3 __

Evidence, reproducibility and clarity (Required):

This is an interesting study demonstrating an interaction between miR-184 and the Drosophila insulin-like peptide 8 (dilp8) in the tissue damage response. The authors show that Dilp8 activity is negatively regulated by miR-184, apparently through direct interaction between miR-184 and the dilp8-3'UTR, which leads to lower dilp8 mRNA transcript levels, via an undetermined mechanism, supposedly its degradation? Furthermore, the authors show that during aberrant tissue growth, miR-184 levels are very slightly downregulated (see comment below), and based on other experiments, imply causation of this with the increased dilp8 mRNA levels that occur in these tissues, again via an unclear mechanism: upregulation or stabilization of dilp8 mRNA. The authors present evidence that the JNK pathway, which had been known to be critical for dilp8 mRNA upregulation upon tissue damage, does so via miR-184.

Major Comments:

__Comment 1: The data showing the direct regulation of dilp8-3'UTR by miR-184 are not very strong and would require more controls to strengthen the claim, as described below. __

Response: We have performed new experiments to validate that dilp8-3’UTR is regulated by miR-184. Please see the detailed responses to comments 10-12 below.

__Comment 2: The miR-184 effects are also very small (less than 2-fold reduction with tissue damage; or less than 2-fold induction with JNK-pathway inhibition via bskDN). These two points are the weakest part of the manuscript and model. __

Response: We agree with the reviewers on this point. The reduction in miR-184 levels in response to RicinA expression is modest (25–30%), and the induction of miR-184 in response to bskDN expression is less than two-fold (Figs. 5A and D). In contrast, dilp8 transcript levels increase several-fold in response to RicinA expression (Fig. 5C, S6A and B). Since we measure dilp8 transcript levels by qPCR, we detect both transcriptional and post-transcriptional contributions to dilp8 regulation. In addition, we have performed a new experiment to check the post-transcriptional regulation of dilp8, in response to tissue damage. Though the change in the dilp8-3′UTR GFP reporter upon RicinA expression in the ptc domain of the wingdisc is mild (Figs. S6F-G’), this strongly suggests a post-transcriptional outcome of the reduction of miR-184 levels on dilp8. Hence, we propose that tissue damage induces strong transcriptional activation of dilp8, while the reduction of miR-184, despite its smaller magnitude, contributes to dilp8 upregulation via post-transcriptional regulation. In support of this, our experiments demonstrate direct regulation of the dilp8-3′UTR by miR-184 (Figs. 4C-F’), and show strong dilp8 mRNA upregulation in miR-184 deficient conditions (Fig. 4A and B), suggesting the role of miR-184 in maintaining dilp8 levels. We also show that RicinA induced effects on dilp8 and pupariation delay are reversed by co-expression of miR-184 (Fig. 5C). We do not claim that regulation by miR-184 is the sole mechanism for driving dilp8 induction during tissue damage, but suggest that miR-184-mediated post-transcriptional regulation acts in a complementary manner to transcriptional responses. Furthermore, we believe that the mild effect of JNK signaling on miR-184 (as shown by the bskDN experiment) is sufficient for the moderate reduction of miR-184 in response to tissue damage.

Comment 3: ____Regarding the expression levels, it does not help that the authors show bar graphs with standard errors of the mean instead of the actual data points to allow reliable appreciation of the data dispersion.

Response: We have modified our figures and have performed statistical analysis according to the suggestions of the reviewers, please see responses to comments 1-9, and 13-19.

Comment 4: It is difficult to understand how minute changes in miR-184 levels can lead to over an order of magnitude differences (in some cases) in dilp8 mRNA levels considering that it is a stoichiometric relationship. Maybe ?miR-184-Dicer1? complexes are highly stable and re-used for multiple dilp8 transcripts - the authors could discuss how they understand this occurring in their manuscript.

On the same line, discussion is also rather weak on what regards the mechanism of control of dilp8 mRNA levels by miR-184. Please discuss eg, the evidence for mRNA degradation induction by microRNAs with this UTR binding profile (imperfect UTR binding Fig S4) and-if appropriate-how other possible regulatory models (direct and indirect) could explain the findings.

Response: We accept the reviewers comment that 25-30% reduction of miR-184 is low in comparison to the many fold increase in dilp8 levels. We believe that both post-transcriptional and transcriptional changes are responsible for the induction of dilp8 in response to tissue damage. However, our experiments suggest the role of post-transcriptional regulation by miR-184, as pupariation delay is rescued by miR-184 overexpression (also please see the response to the previous comment). We are not ruling out the possibility of transcriptional regulation of dilp8 mRNA, rather we are suggesting the possibility that both transcriptional and post-transcriptional means are responsible for changes in dilp8. Moreover, we have not performed absolute measurement of miR-184 in the imaginal discs (what we show is a comparison between control and RicinA expression), hence we do not have an exact estimate of how many miR-184 molecules are reduced and if they would be greatly equal or more in comparison to the dilp8 mRNA molecules that are upregulated, as again while measuring dilp8 mRNA we are not checking how many molecules of dilp8 exactly are increased. As the reviewer suggests, it is possible that miR-184-RISC could be stable to handle multiple dilp8 molecules one after the other, hence it is not a 1:1 relationship between miR-184:dilp8. We have included this in the manuscript. It is also known that imperfect 3’UTR binding as seen in most animal microRNAs leads to translational repression and mRNA deadenylation, which eventually results in mRNA degradation.

Comment 5: ____We suggest the authors carefully revise their citations to cite appropriate work that supports the claims, and also to avoid missing the seminal studies that report the claims they cite.

Response: We are really apologetic for the errors citing the key references. We are grateful to the reviewers for correcting this for us. We have made changes to the text to include and correct the references.

We have the suggestions below which we hope will help the authors improve their manuscript. If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

Detailed Comments:

Comment 1. Results 1st paragraph: please describe the screen in more detail. As written, one only discovers it was a miRNA loss-of-function screen when reading the legend of Table S1. Please show the original data of the screen - with dispersion if possible.

Response: We thank the reviewers for these suggestions, we have now included the data from the screen with SEM, and p-values.

Comment 2. Results 1st paragraph, Fourth line, "While several miRNAs caused delays in pupariation by 12 hours or more..". Please correct, as actually loss of miRNAs caused delays.

Response: We thank the reviewer for pointing out this error, we have corrected the text accordingly.

Comment 3. ____Results (Figure 1) - It says that data from three independent experiments are shown. However there is no dispersion in the data. Could the authors please explain this? Are the results of the three experiments summed and presented as one? or is this one of the three?

Response: We thank the reviewers for these suggestions and have plotted data with the SEM values.

Comment 4. It is reported in the legend of Figure S2 that LogRank test was performed to determine statistical significance. However, no statistical data is presented. Please show the results.

__Response: __We thank the reviewers for these suggestions to improve the data presentation, we have incorporated the p-value as suggested.

Comment 5. Fig2A and B. Please show the data points in the bar graphs (as in Figure. 2C), or choose another data representation. ____Please consider redoing statistical analysis with a simple t-test. ____It is not clear to me why ANOVA was used to compare two samples. Please state that data are normalized also to control (tub-GAL4>UAS-scramble). Please ____state____ the h post-hatching from which the RNA samples were collected (as in Fig 2C for 20HE quantification).

__Response: __We thank the reviewers for these suggestions to improve the data presentation, we have incorporated all changes as suggested. Similar changes have been incorporated to the rest of the figures of the manuscript as well. Hours post-hatching information for each figure is now added to the figure legends. __ __

Comment 6. Fig2C. Fig legend states the bar graphs are "absolute values". Please specify if the bar represents the average, median or something else.

Response: We thank the reviewer for pointing this out, we have made the suggested changes.

Comment 7. Throughout the manuscript: please use GAL4 in capital letters or at least standardize it throughout the ms. Currently there are GAL4s and Gal4s.. eg compare Fig 2 and 3 legends.

Response: We thank the reviewer for pointing this out, we have incorporated all changes as recommended.

Comment 8. FigS3A and B. Please revise as Fig2A and B above. and apply the same criteria in the respective figure legend.

__Response: __We thank the reviewer for pointing this out, we have made the changes as recommended.

Comment 9. Fig. 4 - please indicate on the figures what is whole larvae and what is wing imaginal discs. This will facilitate understanding of the figure.

__Response: __We thank the reviewers for these suggestions and have included this information in all the figures.

Comment 10. Fig 4 - Data - Authors do not show that rn-GAL4>miR-184-sponge causes up regulation of dilp8 mRNA levels, hence the model is weakened. Doing this experiment would significantly strengthen the study whatever the result is.

Response: We thank the reviewer for pointing this out and we have included this in the manuscript (Fig S5B).

Comment 11. The dilp8-3'UTR experiment is weak especially because its generation is not sufficiently well described in the manuscript. "The dilp8 3'UTR-GFP reporter line was created as described in (Vargheese & Cohen, 2007)" is not sufficient. Please describe the construct generation in sufficient detail so that the experiments can be reproduced by others.

Response: We thank the reviewer for pointing this out and we have elaborated in the methods section on how we generated the dilp8 3'UTR-GFP reporter and dilp8 3'UTR mutant GFP reporter lines. The plasmid was originally created in Steve Cohen’s lab at EMBL, by modifying pCasper4 plasmid, by introducing a tubulin promoter, EGFP and a multiple cloning site, which allows one to clone 3’UTRs of target genes into this plasmid. Not1 and Xho1 sites were used to clone the dilp8-3’UTR and mut-3’UTR. We hope this explains our strategy sufficiently.

Comment 12. Making assumptions, if the construct is as described in Vargheese & Cohen, 2007 and contains all of the dilp8 3'UTR - it should be a Tubulin-driven GFP gene with a dilp8-3'UTR "Tub-GFP-(dilp8 3'UTR)". In this case the authors need to rule out the alternative interpretation of the result in Fig. 4D by showing that the expression of miR-184 does not down regulate Tub-GFP expression itself. The best scenario would be to have a mutated dilp8 3'UTR for the miR-184 recognition site. This experiment would significantly strengthen the study and model.

Response: We thank the reviewer for pointing this out. We agree with the reviewers that this experiment is needed to prove direct regulation of the dilp8-3’UTR by miR-184. We have mutated the sequences complementary to the seed region of miR-184 in the dilp8-3’UTR, and demonstrated that overexpression of miR-184 does not regulate the mutated tub-GFP-(dilp8 3'UTR) expression. This confirms that the dilp8 gene is a direct target of miR-184. This data is added to the manuscript as Figs 4E-F’.

Comment 13. Figure 4C-D please separate dilp8 from 3'UTR with a space or hyphen.

Response: We thank the reviewer for pointing this out and have separated dilp8 from 3’UTR with a hyphen.

Comment 14. Figure 4E. Please name the dilp8 allele as MI00727 as it is not a KO, but rather a hypomorphic mutation (fully WT dilp8 transcripts are still generated, albeit at a much lower level).

Response: We thank the reviewer for pointing this out and we have made the necessary changes.

Comment ____15. Figure 6D: please add UAS to bskDN/+. All figures have rn-GAL4 alone or with UAS-GFP as control. This finding would be strengthened with this other control, especially because the size effect is small.____ This being said a general comment for all experiments is that hemi-controls are generally missing for all figures. eg, in Fig 3. One would typically include controls such as A. Phm>+ and +>miR.184; B. aug21>+ and +>miR.184; C. ptth>+ and +>miR.184; D. rn>+ and +>miR.184

Response: We thank the reviewer for pointing this out. We have added UAS to bskDN, now Fig 5D and have also added the rnGAL4/+ control. We have also performed various hemi-control experiments as suggested by the reviewer to our best capabilities. We have added a separate graph with the hemicontrols in the as a Reviewer Response Figure 1.

Comment 16. Figure 7: Are IPCs necessary for the model? If not, I suggest removing them and placing the Lgr3 neuron cell bodies much more anterior in this scheme. Their cell bodies are as anterior and rostral as it gets, approximately where the IPCs are depicted in this type of view of the CNS.

Response: We thank the reviewer for pointing this out and have removed IPCs from the figure, this figure is now labelled as Fig. 6.

Comment ____17. Table S1- It would be preferable to see the data of these experiments, but if the authors prefer to show this data in a table, please at least add the dispersion analyses (eg standard deviation.. OR median+-quartiles OR Confidence intervals..), N of animals analysed, and statistics against controls.

Response: We thank the reviewer for pointing this out, we have added the number of larvae analysed, SEM values and statistics against the control condition.

Comment ____18. In all figures with pupariation time: please also indicate significant findings in the graphs (with an asterisk, for instance) and adjust figure legends accordingly. This could facilitate understanding the data.

__Response: __Thanks for the suggestion. We have incorporated this information into figure legends.

Comment ____19. Please revise Figure legends for punctuation.

__Response: __We have rectified all the errors in punctuation. We thank the reviewers for suggesting this.

__Comment ____20. __

a) Abstract:

Line 10: What is the evidence to call Dilp8 a "paracrine" factor?

Response: We thank the reviewer for pointing this out, we have changed the text to ‘secreted factor’.

b) Introduction:

4th paragraph, 3rd sentence " Dilp8... buffers developmental noise and delays pupariation..." Buffering of developmental noise was first shown in Garelli et al., Science 2012, so this publication should be cited. ____4th paragraph, 5th sentence: please include Jaszczak et al., Genetics 2016. This paper was published together with the 2015 papers, just a matter of timing that it got a 2016 date. Moreover, I do not think Katsuyama et al., 2015 is well cited to back up the statement in this sentence, hence I recommend removing that citation in this sentence.

Response: We thank the reviewer for pointing this out and have made necessary changes.

c) 6th paragraph: 5th line "targeting dilp8" : please specify if you mean the gene or the mRNA, or both. Same for line 7.

Response: We thank the reviewer for pointing this out and have made necessary changes.

d) Results Page 10, 1st paragraph, 1st sentence: the works cited are not the appropriate studies that demonstrated what is being stated. This was shown in Garelli et al., Science 2012 and Colombani et al., Science 2012. Results Page 10, 1st paragraph, line 11: Please also cite Colombani et al., Science 2012, who first showed that JNK is required for dilp8 regulation.

Response: We thank the reviewer for pointing this out and are extremely apologetic for this oversight. We have made necessary changes to the manuscript.

e) Discussion, 2nd paragraph, line 4: again, please indicate the rationale for using "paracrine" to describe Dilp8's activities. The current widely accepted model is that Dilp8 acts on interneurons in the brain ____(eg, reviewed in Juarez-Carreno et al., Cell Stress, 2018; Gontijo and Garelli, Mech Dev, 2018; Mirth and Shingleton, Front Cell Dev Biol, 2019; Texada et al., Genetics 2020; Boulan and Leopold, 2021).____ In order to reach the brain, Dilp8 has to be secreted from the discs and travel to the brain. This is as an endocrine mechanism as it gets for a small larva, considering that some discs can be on the opposite side of the larva (eg, genital discs). While this does not exclude that Dilp8 could also act paracrinally, the only evidence that I am aware of comes from other contexts such as during transdetermination (where Dilp8 has been proposed to work in an autocrine or paracrine fashion, via Drl in imaginal discs (Nemoto et al., Genes to Cells, 2023), however, this is not cited appropriately in this manuscript and is less related to the Lgr3-dependent pathway being studied here.

Response: We totally agree with the reviewer and appreciate clarifying this for us. We have made necessary changes to the text.

f) Discussion Page 13, 1st paragraph, This claim is supported by data presented in Garelli et al., Science 2012, not the other two papers. Garelli et al., 2015 shows that the Lgr3 receptor also participates in buffering developmental noise. Other studies have corroborated the Garelli et al., 2012 finding: eg, Colombani et al., Curr Biol 2015; Boone et al., Nat Commun 2016; Blanco-Obregon et al., Nat Commun 2022). Many other studies have shown that Dilp8 promotes developmental stability under tissue stress and challenges.

Discussion Page 12, 3rd paragraph, 2nd sentence: "The Lgr3 neurons directly interact with ... PTTH ...and insulin-producing neurons" Please cite Colombani et al., 2015 and Vallejo et al., Science 2015. Vallejo et al., propose that circuit with insulin-producing neurons. In the 3rd sentence, only Jaszczak et al., 2016 is cited, whereas this claim/model comes from many studies, such as Halme et al., Curr Biol, 2010; Hackney et al., PLoS One 2012; Garelli et al. Science 2012; Colombani et al., Science, 2012; and the Lgr3 papers from 2015). Jaszczak et al., actually propose that Lgr3 is also required in the ring gland in addition to neurons.

Discussion page 14 last paragraph,10 line, "In Aedes aegypti ....regulates ilp8 (Ling et al., 2017)". As far as I understand mosquitoes do not have a dilp8 orthologue (see for instance Gontijo and Gontijo, Mech Dev 2018; and Jan Veenstra's work). ilp nomenclature (numbering) does not follow that of Drosophila, so ilp8 is probably a typical Insulin/IGF-like peptide and is NOT an orthologue of Dilp8, a relaxin, so this citation needs to be removed or placed into the broader context of microRNA regulation of ilps.

Response: We are really sorry for the numerous glaring errors in the references. We thank the reviewers for correcting this for us. We have made necessary changes to the text.

Thank you for the opportunity to review your interesting work,

Alisson Gontijo and Rebeca Zanini

Reviewer #3 (Significance (Required)):

If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

__Author’s concluding response: __

We thank all the reviewers for the overall positive comments and suggestions that we believe have helped us to improve our manuscript. We have incorporated all the changes suggested, especially regarding errors in citing key references. We have performed most of the experimental suggestions. Also, we have modified the way in which graphs are presented, including statistical tests as suggested by the reviewers. Several controls have been performed to strengthen the manuscript further. We believe that this review process aided in significantly improving this manuscript.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

This is an interesting study demonstrating an interaction between miR-184 and the Drosophila insulin-like peptide 8 (dilp8) in the tissue damage response. The authors show that Dilp8 activity is negatively regulated by miR-184, apparently through direct interaction between miR-184 and the dilp8-3'UTR, which leads to lower dilp8 mRNA transcript levels, via an undetermined mechanism, supposedly its degradation? Furthermore, the authors show that during aberrant tissue growth, miR-184 levels are very slightly downregulated (see comment below), and based on other experiments, imply causation of this with the increased dilp8 mRNA levels that occur in these tissues, again via an unclear mechanism: upregulation or stabilization of dilp8 mRNA. The authors present evidence that the JNK pathway, which had been known to be critical for dilp8 mRNA upregulation upon tissue damage, does so via miR-184. The data showing the direct regulation of dilp8-3'UTR by miR-184 are not very strong and would require more controls to strengthen the claim, as described below. The miR-184 effects are also very small (less than 2-fold reduction with tissue damage; or less than 2-fold induction with JNK-pathway inhibition via bsk-DN). These two points are the weakest part of the manuscript and model. Regarding the expression levels, it does not help that the authors show bar graphs with standard errors of the mean instead of the actual datapoints to allow reliable appreciation of the data dispersion. It is difficult to understand how minute changes in miR-184 levels can lead to over an order of magnitude differences (in some cases) in dilp8 mRNA levels considering that it is a stoichiometric relationship. Maybe ?miR-184-Dicer1? complexes are highly stable and re-used for multiple dilp8 transcripts - the authors could discuss how they understand this occurring in their manuscript. On the same line, discussion is also rather weak on what regards the mechanism of control of dilp8 mRNA levels by miR-184. Please discuss eg, the evidence for mRNA degradation induction by microRNAs with this UTR binding profile (imperfect UTR binding Fig S4) and-if appropriate-how other possible regulatory models (direct and indirect) could explain the findings. We suggest the authors carefully revise their citations to cite appropriate work that supports the claims, and also to avoid missing the seminal studies that report the claims they cite. We have the suggestions below which we hope will help the authors improve their manuscript. If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

Comments:

Results 1st paragraph: please describe the screen in more detail. As written, one only discovers it was a miRNA loss-of-function screen when reading the legend of Table S1. Please show the original data of the screen - with dispersion if possible.

Results 1st paragraph, Fourth line, "While several miRNAs caused delays in pupariation by 12 hours or more..". Please correct, as actually loss of miRNAs caused delays.

Results (Figure 1) - It says that data from three independent experiments are shown. However there is no dispersion in the data. Could the authors please explain this? Are the results of the three experiments summed and presented as one? or is this one of the three?

It is reported in the legend of Figure S2 that LogRank test was performed to determine statistical significance. However, no statistical data is presented. Please show the results.

Fig2A and B. Please show the data points in the bar graphs (as in Figure. 2C), or choose another data representation. Please consider redoing statistical analysis with a simple t-test. It is not clear to me why ANOVA was used to compare two samples. Please state that data are normalized also to control (tub-GAL4>UAS-scramble). Please state the h post-hatching from which the RNA samples were collected (as in Fig 2C for 20HE quantification).

Fig2C. Fig legend states the bar graphs are "absolute values". Please specify if the bar represents the average, median or something else.

Throughout the manuscript: please use GAL4 in capital letters or at least standardize it throughout the ms. Currently there are GAL4s and Gal4s.. eg compare Fig 2 and 3 legends.

FigS3A and B. Please revise as Fig2A and B above. and apply the same criteria in the respective figure legend.

Fig. 4 - please indicate on the figures what is whole larvae and what is wing imaginal discs. This will facilitate understanding of the figure.

Fig 4 - Data - Authors do not show that rn-GAL4>miR-184-sponge causes up regulation of dilp8 mRNA levels, hence the model is weakened. Doing this experiment would significantly strengthen the study whatever the result is.

The dilp8-3'UTR experiment is weak especially because its generation is not sufficiently well described in the manuscript. "The dilp8 3'UTR-GFP reporter line was created as described in (Vargheese & Cohen, 2007)" is not sufficient. Please describe the construct generation in sufficient detail so that the experiments can be reproduced by others.

Making assumptions, if the construct is as described in Vargheese & Cohen, 2007 and contains all of the dilp8 3'UTR - it should be a Tubulin-driven GFP gene with a dilp8-3'UTR "Tub-GFP-(dilp8 3'UTR)". In this case the authors need to rule out the alternative interpretation of the result in Fig. 4D by showing that the expression of miR-184 does not down regulate Tub-GFP expression itself. The best scenario would be to have a mutated dilp8 3'UTR for the miR-184 recognition site. This experiment would significantly strengthen the study and model.

Figure 4C-D please separate dilp8 from 3'UTR with a space or hyphen.

Figure 4E. Please name the dilp8 allele as MI00727 as it is not a KO, but rather a hypomorphic mutation (fully WT dilp8 transcripts are still generated, albeit at a much lower level).

Figure 6D: please add UAS to bskDN/+. All figures have rn-GAL4 alone or with UAS-GFP as control. This finding would be strengthened with this other control, especially because the size effect is small. This being said a general comment for all experiments is that hemi-controls are generally missing for all figures. eg, in Fig 3. One would typically include controls such as A. Phm>+ and +>miR.184; B. aug21>+ and +>miR.184; C. ptth>+ and +>miR.184; D. rn>+ and +>miR.184

Figure 7: Are IPCs necessary for the model? If not, I suggest removing them and placing the Lgr3 neuron cell bodies much more anterior in this scheme. Their cell bodies are as anterior and rostral as it gets, approximately where the IPCs are depicted in this type of view of the CNS.

Table S1- It would be preferable to see the data of these experiments, but if the authors prefer to show this data in a table, please at least add the dispersion analyses (eg standard deviation.. OR median+-quartiles OR Confidence intervals..), N of animals analysed, and statistics against controls.

In all figures with pupariation time: please also indicate significant findings in the graphs (with an asterisk, for instance) and adjust figure legends accordingly. This could facilitate understanding the data.

Please revise Figure legends for punctuation.

Abstract: Line 10: What is the evidence to call Dilp8 a "paracrine" factor?

Introduction:

4th paragraph, 3rd sentence " Dilp8... buffers developmental noise and delays pupariation..." Buffering of developmental noise was first shown in Garelli et al., Science 2012, so this publication should be cited.

4th paragraph, 5th sentence: please include Jaszczak et al., Genetics 2016. This paper was published together with the 2015 papers, just a mater of timing that it got a 2016 date. Moreover, I do not think Katsuyama et al., 2015 is well cited to back up the statement in this sentence, hence I recommend removing that citation in this sentence.

6th paragraph: 5th line "targeting dilp8" : please specify if you mean the gene or the mRNA, or both. Same for line 7.

Results Page 10, 1st paragraph, 1st sentence: the works cited are not the appropriate studies that demonstrated what is being stated. This was shown in Garelli et al., Science 2012 and Colombani et al., Science 2012.

Results Page 10, 1st pagragraph, line 11: Please also cite Colombani et al., Science 2012, who first showed that JNK is required for dilp8 regulation.

Discussion, 2nd paragraph, line 4: again, please indicate the rationale for using "paracrine" to describe Dilp8's activities. The current widely accepted model is that Dilp8 acts on interneurons in the brain (eg, reviewed in Juarez-Carreno et al., Cell Stress, 2018; Gontijo and Garelli, Mech Dev, 2018; Mirth and Shingleton, Front Cell Dev Biol, 2019; Texada et al., Genetics 2020; Boulan and Leopold, 2021). In order to reach the brain, Dilp8 has to be secreted from the discs and travel to the brain. This is as an endocrine mechanism as it gets for a small larva, considering that some discs can be in the opposite side of the larva (eg, genital discs). While this does not exclude that Dilp8 could also act paracrinally, the only evidence that I am aware of comes from other contexts such as during transdetermination (where Dilp8 has been proposed to work in an autocrine or paracrine fashion, via Drl in imaginal discs (Nemoto et al., Genes to Cells, 2023), however, this is not cited appropriately in this manuscript and is less related to the Lgr3-dependent pathway being studied here.

Discussion Page 13, 1st paragraph, This claim is supported by data presented in Garelli et al., Science 2012, not the other two papers. Garelli et al., 2015 shows that the Lgr3 receptor also participates in buffering developmental noise. Other studies have corroborated the Garelli et al., 2012 finding: eg, Colombani et al., Curr Biol 2015; Boone et al., Nat Commun 2016; Blanco-Obregon et al., Nat Commun 2022). Many other studies have shown that Dilp8 promotes developmental stability under tissue stress and challenges.

Discussion Page 12, 3rd paragraph, 2nd sentence: "The Lgr3 neurons directly interact with ... PTTH ...and insulin-producing neurons" Please cite Colombani et al., 2015 and Vallejo et al., Science 2015. Vallejo et al., propose that circuit with insulin-producing neurons. In the 3rd sentence, only Jaszczak et al., 2016 is cited, whereas this claim/model comes from many studies, such as Halme et al., Curr Biol, 2010; Hackney et al., PLoS One 2012; Garelli et al. Science 2012; Colombani et al., Science, 2012; and the Lgr3 papers from 2015). Jaszczak et al., actually propose that Lgr3 is also required in the ring gland in addition to neurons.

Discussion page 14 last paragraph,10 line, "In Aedes aegypti ....regulates ilp8 (Ling et al., 2017)". As far as I understand mosquitoes do not have a dilp8 orthologue (see for instance Gontijo and Gontijo, Mech Dev 2018; and Jan Veenstra's work). ilp nomenclature (numbering) does not follow that of Drosophila, so ilp8 is probably a typical Insulin/IGF-like peptide and is NOT an orthologue of Dilp8, a relaxin, so this citation needs to be removed or placed into the broader context of microRNA regulation of ilps.

Thank you for the opportunity to review your interesting work, Alisson Gontijo and Rebeca Zanini

Significance

If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

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Referee #2

Evidence, reproducibility and clarity

Drosophila has helped to characterize the mechanisms that coordinate tissue growth with developmental timing. The insulin/relaxin-like peptide Dilp8 has been identified as a key factor that communicates the abnormal growth status of larval imaginal discs to neuroendocrine neurons responsible for regulating the timing of metamorphosis. Dilp8, derived from imaginal discs, targets four Lgr3-positive neurons in the central nervous system, activating cyclic-AMP signaling in an Lgr3-dependent manner. This signaling pathway reduces the production of the molting hormone, ecdysone, delaying the onset of metamorphosis. Simultaneously, the growth rates of healthy imaginal tissues slow down, enabling the development of proportionate individuals. In this manuscript "miR-184 modulates dilp8 to control developmental timing during normal growth conditions and in response to developmental perturbations" by Dr. Varghese and colleagues, the authors identify a new post transcriptional regulator of Dilp8. The authors show that miR-184 plays a pivotal role in tissue damage responses by inducing dilp8 expression, which in turn delays pupariation to allow sufficient time for damage repair mechanisms to take effect.

Major points:

• In most of the experiments for percentage of pupariation, the 50% pupariation in control is around 110 hours AED in figures 1, 2 and 3. In figures 5 and 6 using the UAS Ricin, the controls are more around 90 hours AED. Why this discrepancy?
• What is the mechanism behind the expression of miR-184 in stress conditions? Does miR-184 also implicated in other conditions giving rise to a developmental delay (X-rays irradiation or animal bearing rasV12, scrib-/- tumors)?
• dilp8 mutant animals have also been shown to be more resistant to starvation or desiccation (https://doi.org/10.3389/fendo.2020.00461 ). Is miR-184 implicated in this answer?
• dilp8 expression has been also shown to be regulated by Xrp1 in response to ribosome stress (https://doi.org/10.1016/j.devcel.2019.03.016). This paper should be included in the manuscript Is it possible that the expression levels of miR184 are regulated by Xrp1?

Minor points:

• Does the overexpression of miR184 induce an increased fluctuating asymmetry?
• There are 2 references Colombani et al. (2012 for Dilp8 and 2015 for Lgr3). Can you double check that they are used accordingly

Significance

Altogether, the paper present compiling lines of evidence supporting the proposed model. The experiments are well designed and are convincing. The papers is interesting and relevant for a broad audience.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this study, Fernandes and colleagues addressed the question of the role of micro-RNAs in regulating the coupling between organ growth and developmental timing. Using Drosophila, they identified the conserved micro-RNA miR-184 as a regulator of the developmental transition between juvenile larval stages and metamorphosis. This transition is under the control of the steroid hormone Ecdysone, and has been shown to be modulated in case of abnormal tissue growth to adjust the duration of larval growth in response to developmental perturbations. The relaxin-like hormone Dilp8 has been identified as a key secreted factor involved in this coupling. Here, the authors show that miR-184 is involved in the regulation of Dilp8 expression both in physiological conditions and upon growth perturbation. They propose that this function is carried out in imaginal tissues, where miR-184 levels are modulated by tissue stress. While several factors have already been involved in triggering sharp dilp8 induction at the transcriptional level, this study adds another level of complexity to the regulation of Dilp8 by proposing that its expression is fine-tunned post-transcriptionally through repression by miR-184.

Major Comments

Overall, the manuscript is well organized, and the logics of the experimental plan well presented. The results are clear, and I appreciate the quality of the pupariation curves. However, I believe that two main conclusions of the paper are not fully supported by the results presented in the figures: the direct regulation of dilp8 3'UTR by miR-184, and the specificity of this regulation in imaginal discs. Here I develop in more details these two aspects. 1. The strategy of the 3'UTR sensor is not fully optimized. Indeed, in most experiments, qRT-PCR is used to assess dilp8 expression levels, although it reflects both transcriptional and post-transcriptional. Importantly, to show that post-transcriptional regulation is involved in the response to tissue damage, the levels of the 3'UTR sensor should be analyzed in discs expressing RAcs (showing at the same time that the response is cell-autonomous in the discs). The expected upregulation of the sensor should be prevented by simultaneous expression of miR-184. This approach would shed light on the relative contribution of transcriptional versus post-transcriptional regulation of dilp8 in response to growth perturbation. 2. In my opinion, the use of a 3'UTR sensor is not sufficient to conclude that the regulation by miR-184 is direct, as miR-184 could also regulate an intermediate factor that acts on dilp8 post-transcriptional regulation. To solve this issue, a common strategy is to generate a 3'UTR sensor with mutated binding sites that should abolish the regulation by miR-184. This mutated 3'UTR might also respond differently to tissue damage, which would strongly support the conclusions of the study. 3. Concerning the tissue-specific regulation of Dilp8 by miR-184, these results need to be strengthened. Indeed, this comes mostly from phenotypes observed with rn-GAL4. Although this is a classical tool for driving expression in imaginal discs, rn-GAL4 also drives strong expression in other tissues that could contribute to triggering a delay, such as the CNS and part of the gut (proventriculus). In our hands, some growth phenotypes in the wing obtained with rn-GAL4 could be fully reverted by blocking GAL4 in the CNS indicating that the phenotype was not wing-specific. Importantly, miR-184 seems to be highly expressed in the CNS according to FlyBase, reinforcing the possibility that it plays a role in this organ. Here I propose approaches to confirm that miR-184 mediated regulation of dilp8 and developmental timing indeed occur in the discs: - Another driver with less secondary expression sites could be used (pdmR11F02-GAL4), or rn-GAL4 could be combined with an elav-GAL80 to prevent expression in most neurons. - The authors could identify the source of Dilp8 upregulation in miR-184 mutants using tissue-specific qRT-PCR instead of whole larvae expression like in Fig 4A-B. - This tissue-specific upregulation could be functionally tested using a rescue experiment, in which the delay observed in miR-184 mutants could be rescued by disc-specific downregulation of Dilp8 (using pdm2-GAL4 for instance).

Optional: Because it is known that dilp8 is strongly regulated at the transcriptional level, the relative input from post-transcriptional upregulation is an important question arising from this study. Although it might be a more long-term approach, I believe that generating a Dilp8 mutant lacking its 3'UTR or, even better, with mutated miR-184 binding sites, would shed light on the role of this regulation for the response to growth perturbation and/or developmental stability (fluctuating asymmetry).

Minor Comments

• I think that a number of results could be moved to SI as they are either controls, or reproduce published data without bringing novelty. For instance, results in Fig 5A-D are similar to data published by Sanchez et al, as stated in the text. Fig6A as well.
• Fig 6D is quite mysterious, as it suggests that basal JNK activation regulates miR-184, which is different from a context of tissue damage. I think that this result could be removed. Alternatively, if the authors want to dig in that direction, more experiments should be provided, such as bskDN expression in an RAcs context and the effects on miR-184 levels and the 3'UTR sensor (since transcript levels are already published).
• The references related to Dilp8 should be checked more in detail in the intro and discussion. About Dilp8 and developmental stability: remove the ref to Colombani et al 2012, instead put Boone et al 2016 and add Blanco-Obregon et al 2022 (in addition to Garelli et al 2012 who initially identified this phenotype. About Lgr3 as the receptor for Dilp8: add Colombani et al, Current Biology 2015, and cite here Vallejo et al 2015, Garelli et al 2015. Among the important transcriptional regulators of Dilp8, Xrp1 could be mentioned (Boulan et al 2019, Destefanis et al 2022) as it plays a complementary function to JNK depending on the type of tissue stress.

Significance

General Assessment

This study provides convincing data showing that the conserved microRNA miR-184 plays a role in regulating developmental timing in Drosophila through modulating the levels of Dilp8, a key factor in the coupling between tissue growth and developmental transitions. The results are convincing, but the general conclusions of the paper need to be strengthened regarding the direct regulation of dilp8 by miR-184 and the tissue-specificity of this interaction.

Advance

Dilp8 is a key factor that modulates growth and timing in response to developmental perturbations and contributes to developmental precision in physiological conditions. As such, its regulation has been studied by different groups in the last decade, leading to the identification of several inputs for its transcriptional regulation. Here, the authors uncover a post-transcriptional regulation by miR-184, adding another level of regulation of Dilp8 that contribute to ensuring proper regulation of developmental timing, and opening the possibility that miR-184 might play similar roles in other species.

Audience

This study is of interest for researchers in the field of basic science, with a focus on developmental timing, tissue damage and biological function of microRNAs.

Reviewer expertise

Drosophila, growth control, developmental timing, Dilp8.

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Reply to the reviewers

1. General Statements

We thank the reviewer for their positive comments regarding the research article titled "The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish" by Uddin GM and colleagues. We appreciate your input, and we will address these comments as indicated below with specific responses to each point raised by reviewers.

The main changes in the updated manuscript are as follows:

We have revised the introduction to now incorporate additional background information on mitochondria, NAD, and mitochondrial dynamics and function. This addition aims to provide readers with a broader understanding of the mitochondrial context in relation to our study.

Furthermore, we recognize that previous studies have explored mitochondrial function in the context of the ketogenic diet. While our specific investigation centered on mitochondrial morphology, we acknowledge the importance of comprehensively investigating mitochondrial function. To this end, we have added new data showing how BHB impacts mitochondrial oxidative phosphorylation in HeLa cells (Sup Fig 2), and how both BHB and NMN impact oxygen consumption/glycolysis in zebrafish (Fig 7).

We have also added new behaviour analysis of the zebrafish (Fig 6), and have re-framed the discussion around neurodevelopment generally, rather than ASD specifically.

Finally, we have now included a section in our manuscript that discusses the limitations of our study. These limitations can be further investigated to explore and characterize the full mechanistic potential behind the effects of the ketogenic diet and/or NMN on mitochondrial dynamics.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

*Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Uddin GM and colleagues presented a research article entitled 'The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish'. Roles of ketogenic diet (KD) and NAD+ precursors in health promotion and longevity, as well as on the alleviation of a broad range of diseases are evident. However, their roles in autism are not well done, which is the novelty of the current study. Addressing below questions will improve the quality of the paper.

Major concerns 1. In the introduction section, a broad overview of the roles of ketogenic diet (KD) in neurodegenerative disease (and ageing, if possible) should be provided. E.g., the authors should summarize exciting progress on the use of KD to treat Alzheimer's disease in animal models (PMID: 23276384). *

Response: Thank you for your valuable suggestion. While it is true that the KD appears to be beneficial in neurodegenerative (and other disease) models, our focus in this paper is looking at neurodevelopment, rather than all potential benefits of the KD. Nonetheless, we have addressed this comment by incorporating a brief overview of the roles of the KD in neurodegenerative diseases, including Alzheimer's disease (AD), in the introduction section of the manuscript. Specifically, we have summarized the exciting progress made in utilizing KD to treat AD in animal models, as highlighted in the suggested study. This addition helps to provide a better overview of the potential therapeutic effects of KD in neurodegenerative diseases and strengthens the introduction section of the manuscript.

• Roles of high fat diet to treat diseases could be extended to rare premature ageing diseases. In such scenario, high fat and NAD+ boosting shared some joint mechanisms (PMID: 25440059 ). *

Response: This information and the reference are now added to the discussion.

*In the introduction, a more detailed introduction of NAD+ and its roles in mitochondrial homeostasis (especially mitophagy and the mitochondrial fusion-fission balance) should be included (PMID: 24813611; PMID: 30742114; PMID: 31577933). *

Response: Although our paper focused primarily on mitochondrial fission and fusion, we have incorporated a new paragraph in the introduction to provide a more detailed introduction detailing NAD+ and its roles in mitochondrial homeostasis, specifically highlighting mitophagy. We have included the suggested references.

• In regarding to the statement of KD increases NAD+, was it due to increased generation (to check protein levels and activities of different NAD+ synthetic enzymes, such as iNAMPT, NMNAT1-3, and NRK) and/or reduced consumption (in addition to reduced glycolysis, does KD inhibit the activities of CD38 and PARPs? In this paper, Sirtuins' activities is (are increased)). Detailed exploration of the activities of these proteins will unveil a clear molecular mechanisms on how KD affects/regulates NAD+. *

Response: Thank you for the comment. We agree that exploring the detailed mechanism of how the ketogenic diet (KD) affects NAD+ is an interesting question that will have important implications once answered. However, fully elucidating the mechanism of action would require a more comprehensive investigation, which is beyond the scope of this current project. We have now added this as a future direction in the manuscript.

*Fig. 1: in the NAD+ field, the normal used NR/NMN concentrations are normally high like to use 500 µM to 2-5 mM (as the NAD+ levels in cells are high). In addition to use 50 µM, the authors are strongly to have a dose-dependent study (50 µM, 500µM, 1, 2, 5 mM), and see changes of mitochondrial funciton and parameters. In this condition, NAD+ levels should be also checked. *

Response: We have added new supplemental data showing the initial dose response of the effects of BHB and NMN on mitochondrial morphology, which led us to choosing the relevant doses for the remainder of the paper. Our objective was not to investigate the broad impacts of different NMN concentrations on mitochondrial function and parameters, or NAD+ levels. As such, we have only focused on doses where we see effects on mitochondrial morphology.

*Fig. 2: a comprehensive characterization of mitochondrial fusion-fission should be performed. In addition to the protein evaluated, changes on other key fusion-fission proteins, like Bax, Bak, Mfn-1, Mfn-2, etc should be performed (PMID: 17035996; PMID: 24813611). *

Response: We agree that looking at other key proteins involved in mediating mitochondrial fission and fusion could provide additional insight. Indeed, given the changes in global acetylation that we see, it is expected that some other proteins may also be regulated in this way. However, there are at least a dozen proteins involved in mediating mitochondrial fusion and fission, not to mention many more proteins that regulate these proteins. Unfortunately, it is not feasible to analyze all the proteins involved in mitochondrial fusion-fission. Moreover, looking only at protein levels, doesn't necessarily inform about the activity of any protein. Instead, we concentrated in this paper on investigating known links between protein acetylation and mitochondrial dynamics, particularly focusing on the proteins that have known links to acetylation (i.e., DRP1, OPA1, MFNs). We have added a note in the discussion acknowledging that other means of regulation could also be occurring in parallel.

*Figs. 1-5 were focused on mitochondrial morphology, whether KD and NMN changed mitochondrial funciton should be explored, such as to use seahorse to check ECR and OCR. *

Response: Although our question was focused on morphology, we agree that mitochondrial function is important. We have added new data showing that BHB increases basal oxygen consumption in HeLa cells (Sup Fig 2), as well as new data showing that BHB and NMN influence oxygen consumption and glycolysis in our zebrafish model (Fig 7)

• Fig. 6: NR/NMN used in animal studies (via gavage or in drinking water in mice, and on plate for worms and flies) are normally high (e.g., in drinking water for mice could be 4-12 mM; for worms and flies are normally 1-5 mM); for zebrafish, while they are swimming in water, this reviewer concerned whether it was true that 50 µM of NMN was sufficient to show the benefit presented.*

Response: Our data show that these doses are indeed sufficient. We did look at some higher doses for NMN, but these were toxic, leading to poor survival and were not studied further.

*Minor concerns 1. Line 26: For 'a growing list of neurological disorders, including autism spectrum disorder (ASD)', please add AD in. *

Response: Line 26 is part of the abstract, which we feel should be focused more on the main message of the paper, which does not involve AD. As addressed above, we have added AD as an example in the introduction.

*Line 57: For 'with side effects such as gastrointestinal disturbances, nausea/vomiting, diarrhea, constipation, and hypertriglyceridemia being reported', rate of frequency shall be provided if any. *

Response: We have modified the statement to indicate the relative percent of patients suffering the various side effects.

*Reviewer #1 (Significance (Required)):

The novelty of the current study was to investigate effects of KD and NAD+ on autism. This investigation was not performed before and thus is the novelty.

Weakness, effects of KD and NAD+/NMN on mitochondrial function were not well-investigated and should be done. Introduction was not well done, many key information in the fields were not provided which may mislead the readers an over-evaluation of the novelty of the current study.*

Response: As outlined above, we have edited the introduction to include additional information requested by the reviewer. Moreover, our focus in this manuscript was to look at the mechanisms underlying changes in mitochondrial morphology, not mitochondrial function per se, though this is clearly important and related. Nonetheless, as discussed above, we have also added new data showing how BHB impacts mitochondrial function.

*My expertise lies in NAD+, mitochondria, and brain health.

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

The study examined the effect of beta-hydroxybutyrate and nicotinamide nucleotide on mitochondrial morphology and the molecular pathways which mitigate this effect as well as the effect of these treatments on behavior in zebrafish. The study is well done and well written. The only thing I think that could be improved are the bar in the graph some the significant comparisons. It is sometimes difficult to see which groups are being compared.*

Response: We're happy to adjust how the data is displayed in the relevant bar graphs, but it is not clear exactly what changes the reviewer would like. To some degree this will depend on the specific guideline of the final journal where we hope the manuscript will be published. As such, we have not made changes at this point.

***Referees cross-commenting**

The other reviewers do have some fair comments. Multiple doses would be helpful and showing bioenergetic data would complement the morphological measurements. Additionally, behavioral assays showing changes in social behavior in the Zebrafish would provide a stronger link to ASD. *

Response: As discussed above, we have added new information on doses and mitochondrial bioenergetics. With respect to behaviour, we have added thigmotaxis data and reworked the discussion around behaviour and neurodevelopment so that it is less specific to ASD.

*Reviewer #2 (Significance (Required)):

As beta-hydroxybutyrate is an important substrate for the ketogenic diet, this study helps explain the potential mechanisms in which the ketogenic diet may enhance mitochondrial function.

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

In this paper, Uddin and colleagues have investigated components of the ketogenic diet to understand changes in both mitochondrial morphology and protein expression, and zebrafish locomotor behaviour. They investigate whether beta-hydroxybutyrate (BHB) or nicotinamide nucleotide (NMN) application can later human mitochondria in HeLA cell lines, and also recue a locomotion defect in shank3b+/- zebrafish larvae that have previously been proposed as a model for autism. This study is strengthened by showing data from two species; however the link between the HeLA cell line data and larval zebrafish is not strong. The study would be improved by assessing zebrafish mitochondrial changes after drug application, and testing more than one concentration of BH and NMN in the behavioural assay. This is an interesting study, and it is nicely written and presented. I have made some comments to strengthen the study below.

Major comments My expertise is in modelling some aspects of autism in zebrafish. To this end I have focussed on the zebrafish part of this manuscript more fully. I have several comments related to the zebrafish experiments. 1. The changes in mitochondrial morphology, peroxisome number and mitochondrial protein levels were measured in HeLA cells and not comparable data is shown for zebrafish. The same experiments should be repeated using larval zebrafish or a zebrafish cell line. *

Response: We chose to use HeLa cells for the mechanistic studies due to practical reasons. Cell lines offer a controlled and well-established system for investigating cellular processes and molecular mechanisms. Measuring these parameters in tissues is significantly more challenging and requires different reagents (e.g., antibodies) and methodology (electron microscopy) that are not feasible in the current study.

On the other hand, zebrafish larvae were employed for the behavior studies, which cannot be conducted using cell lines. By utilizing zebrafish, we were able to examine the effects of beta-hydroxybutyrate (BHB) and nicotinamide nucleotide (NMN) on locomotor behavior, providing valuable insights into potential therapeutic implications for autism.

While we acknowledge the limitations of not directly measuring mitochondrial morphology, peroxisome number, and mitochondrial protein levels in zebrafish, we believe that our study provides significant contributions to understanding the effects of BHB and NMN in zebrafish behavior. Future studies could certainly consider incorporating zebrafish-specific experiments to complement the findings in HeLa cells.

• How did you choose the concentration of BHB and NMN to use in behavioural experiments? And the timing of application - I don't really understand why you waited 3 days after drug application to measure locomotion. *

Response: These doses chosen initially as they were similar the doses that induced mitochondrial elongation in HeLa cells and were tolerated by the fish larvae. As we saw promising effects at these initial doses, we decided to explore them in more detail. While we agree that it would be worth comparing the effects of additional doses, as well as looking at their effects at other timepoints, such work would be a major endeavour and is beyond the scope of our initial investigations, which we feel are worth reporting in their current state.

With respect to the treatment paradigm, fish larvae were treated 10-48 hours post fertilization, as this is a critical neurogenic developmental timepoint that is often used for exposure studies. Fish do not fully hatch until 3-4 days post fertilization, and display only minimal movement before 5 days, which is why we waited until 5 days to look at movement.

• Do the shank3b+/- larvae show any morphological deficits? Their decrease in locomotion is striking. Is the morphology also rescued by drug application? Can you tie this to the mitochondrial changes that you observed in HeLA cells?*

Response: We do not observe any gross changes in fish morphology that might explain a decrease in locomotion. Unfortunately, it is not feasible to look at mitochondrial morphology in the fish at this time. However, based on previous published work showing that the ketogenic diet promotes mitochondrial elongation in mouse brains (PMID:32380723), we would expect mitochondrial morphology also to be changed in the fish. Nonetheless, as we have not examined this directly in fish, we are not making this specific claim in this manuscript.

• In figure 6A you use time spent swimming as a readout of distance. This doesn't really make sense, because without also showing speed of swimming it is not possible to know whether time and distance correlate in the same way across genotypes. This figure could be improved by showing more detail - speed of swimming, time spent immobile etc. This can easily be extracted from the films that you have already made using the ViewPoint software. *

Response: As requested, we have reanalyzed the zebrafish movement data for a more refined analysis. In the revised version (Fig 6), we include analysis of both speed and distance travelled within a defined time. Importantly, these findings still support differences between WT and shank3b+/- fish that are restored by BHB and NMN to varying degrees.

• Showing a change in locomotion is not enough to claim that a model is autism-like. At a minimum I think that you need to show changes in social behaviour - likely using older fish (more than three weeks) that interact with each other. Changes in locomotion can be caused by so many factors, many of which are not indicative of autism. It is important that as a field we do not simply claim that locomotion can be used as a proxy for more complex disease phenotypes. This recent review may help you with this point:* https://www.frontiersin.org/articles/10.3389/fnmol.2020.575575/full.

Response: The reviewer makes an important point that the movement behaviour phenotypes that we see do not necessarily represent classic ASD phenotypes (i.e., repetitive behaviour, reduced sociability, and reduced communication). To begin to address this issue, we analyzed thigmotaxis, which can be a measure of anxiety. Notably, we also see differences that are reversed by BHB and NMN. However, we cannot model all ASD behaviours in a fish model, and we are not set up to look at social behaviour, especially in the young fish that we were studying. As such, even though Shank3 is a recognized ASD gene, and the shank3b+/- model we are studying is a validated ASD model (PMID: 29619162), we have re-phrased the manuscript in the context of neurodevelopment generally, rather than with respect to ASD specifically. As such, we ascribe the movement and thigmotaxis phenotypes as neurodevelopmental phenotypes that are improved by BHB and NMN.

*For the statistics, as far as I can tell, all of the data should be analysed by ANOVA or the non-parametric equivalent followed by a post-hoc test. Please check this and add information about normality in. *

Response: As requested, we have clarified our statistical methodology throughout the manuscript.

For the mechanistic data, we used t-tests for direct comparisons between two groups (e.g., vehicle vs. treatment). While multiple conditions such as vehicles, NMN, BHB, or etomoxir were tested, statistical comparisons were only conducted comparisons between the vehicle and each treatment group individually. As we are not also making comparisons between treatments this is not a multiple comparison, and ANOVA is not applicable in this context. We have clarified this rationale in the manuscript to avoid any confusion.

For the zebrafish study, where multiple factors were involved (e.g., treatments across different time points or conditions), we performed a two-way ANOVA followed by Tukey's post-hoc test to identify specific group differences. This approach was appropriate for analyzing these datasets and ensures robust conclusion.

With respect to normality testing, all datasets were assessed for normality using the Shapiro-Wilk test, and no violations of normality were observed. The updated text now includes these details.

*Minor comments

1. Make sure that you refer to the fish line as shank3b+/- throughout - see abstract.*

This has bee corrected.

• Please add a space between all numbers and units (e.g. 5 Mm). *

This has bee corrected.

• There is a spelling error on line 340 page 16: finings instead of findings. *

This has bee corrected.

• In figure 1, if each dot represents a different sample, then there appear to be many fewer samples analysed in 1D compared to 1B. Can you comment upon this please*

__Response: __A total of 80-150 cells were counted per condition, and the analyses were performed on 3 independent replicates with 2 independent technical replicates for each treatment condition. The quantification of mean mitochondrial branch length in Figure 1B was measured using Image-J and the MiNA plugin. The measurements were taken from three independent replicates using a standard region of interest (ROI) and randomly selected areas from each image.

In Figure 1D, NAD+ levels were measured 24 hours after treatment of vehicle, βHB, NMN, or Eto+βHB in HeLa cells (n=3-6/group). Each sample lysate represents an independent experimental dish from which coverslips were collected for image analysis.

The difference in sample numbers between Figure 1B and 1D arises because image analysis involves individual cells fixed and stained on coverslips, whereas the NAD assay requires the whole lysate from the entire cell culture dish. Therefore, the higher cell count in Figure 1B represents the number of cells analyzed on coverslips, while Figure 1D represents NAD levels from the lysate normalized to the protein concentration.

*Reviewer #3 (Significance (Required)):

I think that this will be interesting to autism researchers and it could lead to more investigation of the ketogenic diet. Some more work is needed, likely in other model organisms, before this research can be translated to human patients. *

__Response: __We agree that the findings of our study could be of interest to autism researchers and have implications for further investigation of the ketogenic diet (KD). It is important to note that further work, including studies in other model organisms, would be beneficial before translating this research to human patients.

Our study aimed to provide mechanistic insights into the effects of the KD on mitochondrial morphology and behavior. We recognize that the translation of research findings to human patients requires rigorous investigation, including preclinical and clinical studies. Our study contributes to the understanding of the underlying mechanisms involved in the KD's effects, laying the groundwork for future research and potential therapeutic avenues.

We appreciate your perspective and emphasize that our intention is to provide valuable insights into the mechanisms underlying the KD's effects rather than suggesting immediate translation to human patients. Further investigation and validation in diverse models and clinical settings will be necessary before considering clinical applications.

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Referee #3

Evidence, reproducibility and clarity

In this paper, Uddin and colleagues have investigated components of the ketogenic diet to understand changes in both mitochondrial morphology and protein expression, and zebrafish locomotor behaviour. They investigate whether beta-hydroxybutyrate (BHB) or nicotinamide nucleotide (NMN) application can later human mitochondria in HeLA cell lines, and also recue a locomotion defect in shank3b+/- zebrafish larvae that have previously been proposed as a model for autism. This study is strengthened by showing data from two species; however the link between the HeLA cell line data and larval zebrafish is not strong. The study would be improved by assessing zebrafish mitochondrial changes after drug application, and testing more than one concentration of BH and NMN in the behavioural assay.

This is an interesting study, and it is nicely written and presented. I have made some comments to strengthen the study below.

Major comments

My expertise is in modelling some aspects of autism in zebrafish. To this end I have focussed on the zebrafish part of this manuscript more fully. I have several comments related to the zebrafish experiments.

1. The changes in mitochondrial morphology, peroxisome number and mitochondrial protein levels were measured in HeLA cells and not comparable data is shown for zebrafish. The same experiments should be repeated using larval zebrafish or a zebrafish cell line.
2. How did you choose the concentration of BHB and NMN to use in behavioural experiments? And the timing of application - I don't really understand why you waited 3 days after drug application to measure locomotion.
3. Do the shank3b+/- larvae show any morphological deficits? Their decrease in locomotion is striking. Is the morphology also rescued by drug application? Can you tie this to the mitochondrial changes that you observed in HeLA cells?
4. In figure 6A you use time spent swimming as a readout of distance. This doesn't really make sense, because without also showing speed of swimming it is not possible to know whether time and distance correlate in the same way across genotypes. This figure could be improved by showing more detail - speed of swimming, time spent immobile etc. This can easily be extracted from the films that you have already made using the ViewPoint software.
5. Showing a change in locomotion is not enough to claim that a model is autism-like. At a minimum I think that you need to show changes in social behaviour - likely using older fish (more than three weeks) that interact with each other. Changes in locomotion can be caused by so many factors, many of which are not indicative of autism. It is important that as a field we do not simply claim that locomotion can be used as a proxy for more complex disease phenotypes. This recent review may help you with this point: https://www.frontiersin.org/articles/10.3389/fnmol.2020.575575/full.
6. For the statistics, as far as I can tell, all of the data should be analysed by ANOVA or the non-parametric equivalent followed by a post-hoc test. Please check this and add information about normality in.

Minor comments

1. Make sure that you refer to the fish line as shank3b+/- throughout - see abstract.
2. Please add a space between all numbers and units (e.g. 5 Mm).
3. There is a spelling error on line 340 page 16: finings instead of findings.
4. In figure 1, if each dot represents a different sample, then there appear to be many fewer samples analysed in 1D compared to 1B. Can you comment upon this please?

Significance

I think that this will be interesting to autism researchers and it could lead to more investigation of the ketogenic diet. Some more work is needed, likely in other model organisms, before this research can be translated to human patients.

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Referee #2

Evidence, reproducibility and clarity

The study examined the effect of beta-hydroxybutyrate and nicotinamide nucleotide on mitochondrial morphology and the molecular pathways which mitigate this effect as well as the effect of these treatments on behavior in zebrafish. The study is well done and well written. The only thing I think that could be improved are the bar in the graph some the significant comparisons. It is sometimes difficult to see which groups are being compared.

Referees cross-commenting

The other reviewers do have some fair comments. Multiple doses would be helpful and showing bioenergetic data would complement the morphological measurements. Additionally, behavioral assays showing changes in social behavior in the Zebrafish would provide a stronger link to ASD.

Significance

As beta-hydroxybutyrate is an important substrate for the ketogenic diet, this study helps explain the potential mechanisms in which the ketogenic diet may enhance mitochondrial function.

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Referee #1

Evidence, reproducibility and clarity

Uddin GM and colleagues presented a research article entitled 'The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish'. Roles of ketogenic diet (KD) and NAD+ precursors in health promotion and longevity, as well as on the alleviation of a broad range of diseases are evident. However, their roles in autism are not well done, which is the novelty of the current study. Addressing below questions will improve the quality of the paper.

Major concerns

1. In the introduction section, a broad overview of the roles of ketogenic diet (KD) in neurodegenerative disease (and ageing, if possible) should be provided. E.g., the authors should summarize exciting progress on the use of KD to treat Alzheimer's disease in animal models (PMID: 23276384).
2. Roles of high fat diet to treat diseases could be extended to rare premature ageing diseases. In such scenario, high fat and NAD+ boosting shared some joint mechanisms (PMID: 25440059 ).
3. In the introduction, a more detailed introduction of NAD+ and its roles in mitochondrial homeostasis (especially mitophagy and the mitochondrial fusion-fission balance) should be included (PMID: 24813611; PMID: 30742114; PMID: 31577933).
4. In regarding to the statement of KD increases NAD+, was it due to increased generation (to check protein levels and activities of different NAD+ synthetic enzymes, such as iNAMPT, NMNAT1-3, and NRK) and/or reduced consumption (in addition to reduced glycolysis, does KD inhibit the activities of CD38 and PARPs? In this paper, Sirtuins' activities is (are increased)). Detailed exploration of the activities of these proteins will unveil a clear molecular mechanisms on how KD affects/regulates NAD+.
5. Fig. 1: in the NAD+ field, the normal used NR/NMN concentrations are normally high like to use 500 µM to 2-5 mM (as the NAD+ levels in cells are high). In addition to use 50 µM, the authors are strongly to have a dose-dependent study (50 µM, 500µM, 1, 2, 5 mM), and see changes of mitochondrial funciton and parameters. In this condition, NAD+ levels should be also checked.
6. Fig. 2: a comprehensive characterization of mitochondrial fusion-fission should be performed. In addition to the protein evaluated, changes on other key fusion-fission proteins, like Bax, Bak, Mfn-1, Mfn-2, etc should be performed (PMID: 17035996; PMID: 24813611).
7. Figs. 1-5 were focused on mitochondrial morphology, whether KD and NMN changed mitochondrial funciton should be explored, such as to use seahorse to check ECR and OCR.
8. Fig. 6: NR/NMN used in animal studies (via gavage or in drinking water in mice, and on plate for worms and flies) are normally high (e.g., in drinking water for mice could be 4-12 mM; for worms and flies are normally 1-5 mM); for zebra fish, while they are swimming in water, this reviewer concerned whether it was true that 50 µM of NMN was sufficient to show the benefit presented.

Minor concerns

1. Line 26: For 'a growing list of neurological disorders, including autism spectrum disorder (ASD)', please add AD in.
2. Line 57: For 'with side effects such as gastrointestinal disturbances, nausea/vomiting, diarrhea, constipation, and hypertriglyceridemia being reported', rate of frequency shall be provided if any.

Significance

The novelty of the current study was to investigate effects of KD and NAD+ on autism. This investigation was not performed before and thus is the novelty.

Weakness, effects of KD and NAD+/NMN on mitochondrial function were not well-investigated and should be done. Introduction was not well done, many key information in the fields were not provided which may mislead the readers an over-evaluation of the novelty of the current study.

My expertise lies in NAD+, mitochondria, and brain health.

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Reply to the reviewers

We thank the reviewers for their thoughtful comments and overall very supportive feedback.

Reviewer #1 writes: "The study is very thorough and the experiments contain the appropriate controls. (...) The findings of the study can have relevance for human conditions involving disrupted mitochondrial dynamics, caused for example by mutations in mitofusins." Reviewer #2 writes: "The dataset is rich and the time-resolved approach strong." Reviewer #3 writes: "I admire the philosophy of the research, acknowledging an attempt to control for the many possible confounding influences. (...) This is a powerful and thoughtful study that provides a collection of new mechanistic insights into the link between physical and genetic properties of mitochondria in yeast."

We address all points below. We have not yet updated our text and figures since we expect substantial additions from new experiments. But we have included Figure R1 with some additional analyses of existing data at the bottom of the manuscript.

Reviewer1

1.1 Statistical comparisons are missing throughout the manuscript (with the exception of Fig. 2c). Appropriate statistical tests, along with p-values, should be used and reported where different gorups are compared, for example (but not limited to) Fig. 3d and most panels of Fig. 4.

We initially decided not to add too many extra labels to the already very busy plots, given that the magnitude of change mostly speaks for itself. However, we will try to find meaningful statistical tests together with a sensible graphical representation for all of the figures. For one example see Figure R1A.

1.2. I do not agree with the use of Atp6 protein as a direct read-out of mtDNA content. While Atp6 protein levels will decrease with decreasing mtDNA content, the inverse is not necessarily true: decreased Atp6 protein levels do not necessarily indicate decreased mtDNA levels, because they could alternatively or additionally be caused by decreased transcription and/or translation. Therefore, please do not equate Atp6 protein levels to mtDNA levels, and instead rephrase the text referencing the Atp6 experiments in the Results and Discussion sections to measure "mtDNA expression" or "mt-encoded protein" or similar. For example, on p. 14 line 431 should read "mtDNA expression" rather than "decreased synthesis of mtDNA", and line 440 on the same page "mean mtDNA levels" should be "mtDNA expression" or similar.

All three reviewers agree that using Atp6-NG as a direct proxy for mtDNA requires more validation, or at least rephrasing of the text. We agree that this is the most important point to address. We had previously tried using the mtDNA LacO array (Osman et al. 2015) to directly assess the amount of nucleoids per cell. However, the altered mitochondrial morphology of the Fzo1 depleted cells combined with the LacI-GFP which is still in mitochondria even when mtDNA is gone, increases the noise level to a point that we cannot interpret the signal. However, as this manuscript was in the submission process, the Schmoller lab (co-authors #2 and #7) adapted the HI-NESS system to label mtDNA in live yeast cells(Deng et al. 2025). This system promises much better signal to noise and we expect we can address all concerns regarding the actual count of nucleoids per cell. Should this unexpectedly fail for technical reasons, we will try to calibrate the Atp6-levels with DAPI staining at defined time points and will rephrase the text as the reviewer suggests.

1.3. In Fig. 3, the authors use the fluorescence intensity of a mitochondrially-targeted mCardinal as a read-out of mitochondrial mass. Please provide evidence that this is not affected by MMP, either with relevant references or by control experiments (e.g. comparing it to N-acridine orange or other MMP-independent dyes or methods).

Whether or not the import of any mitochondrial protein is dependent on the MMP depends largely on the signal sequence. The preSu9-signaling sequence was previously characterized as largely independent of the MMP compared to other presequences (Martin, Mahlke, and Pfanner 1991), which is why Vowinckel (Vowinckel et al. 2015) and others (Di Bartolomeo et al. 2020; Perić et al. 2016; Ebert et al. 2025) have previously used this as a neutral reference to the strongly MMP-dependent pre-Cox4 signal to estimate MMP. As one control in our own data, we consider that the population-averaged mitochondrial fluorescent signal Figure S3C stays constant in the first few hours, in agreement with the total averaged mitochondrial proteome (Fig R1E). As additional controls, we plan to compare the signal to an MMP independent dye as the reviewer suggests.

1.4. In Fig. 2e-f, the authors use a promoter reporter with Neongreen to answer whether the reduced levels of the nuclear-encoded mitochondrial proteins Mrps5 and Qcr7 are due to decreased expression or to protein degradation, and find no evidence of degradation of the Neongreen reporter protein. However, subcellular localization might affect the availability of the protein to proteases. Although not absolutely required, it would be relevant to know if the Neongreen fusion protein is found in the same subcellular compartment as Mrps5 and Qcr7 at 0h and 9h after Fzo1 depletion.

Here, it seems we need to explain the set-up and interpretation of the data better. The key point we are trying to make with the promoter-Neongreen construct is that the regulation is not mainly at the level of transcription. We are showing that the reduction in the levels of the actual protein (orange bars) is not (mainly) explained by a reduction in expression, since the promoter is similarly active at 0 and at 9 hours (grey bars). If expression from the promoter were strongly reduced, the Neongreen would be diluted with growth and would also decrease, but this is not the case. The fluorophore itself is just floating around in the cytosol and is not subject to the same post-translational regulation as Mrps5 and Qcr7, so there is no reason to expect degradation.

1.5. Fzo1 depletion leads to a very rapid drop in MMP during the first hour of depletion. In the Discussion, can the authors speculate on the possible mechanism of this rapid MMP drop that occurs well before mtDNA or mt-encoded proteins are decreased in level?

This is indeed an interesting point. We think there are likely three reasons causing this initial drop: Firstly, due to the fragmentation the mixing of mitochondrial content is disturbed and smaller fragments may have suboptimal stoichiometry of components (see also (Khan et al. 2024) who look at this in detail including the Fzo1 deletion); secondly, already fairly early, some mitochondrial fragments may not contain any mtDNA and therefore will be unable to synthesize ETC proteins; thirdly, altered morphological features like changes in the surface-to-volume ratios may play a role. Sadly, mechanistically following up on this is not possible with the tools in our hands and therefore outside of the scope of this manuscript. But we are happy to include these speculations in our discussion.

1.6. In Fig. 2a, the mtDNA copy number of Fzo1-depleted cells is ca 1.3-fold of the control cells at the 0h timepoint. Why might this be? Is it an impact of one of the inducers? If so, we might be looking at the combination of two different processes when measuring copy number: one that is an induction caused by the inducer(s), and the other a consequence of Fzo1 depletion itself.

We believe that this 30% increase is within the noise of the experiment rather than an effect of the induction. Since we normalize to t=0 uninduced, the first black data point does not have error bars, emphasizing this difference. None of the protein data suggests that there is an increase in mtDNA encoded proteins (see e.g. 2B, or Atp6 fluorescence data). In the planned HI-NESS experiment, we will see in our single cell data whether there is an actual increase in mtDNA upon TIR induction. Additionally, we will run a qPCR to carefully determine mtDNA levels of untreated wild-type cells, tetracycline treated wild-type cells and tetracycline induced TIR expressing cells to exclude effects of tetracycline as well as the expression of TIR on mtDNA.

Minor comments:

1.7. p. 3, line 71: "ten thousands of dividing cells.." should be "tens of thousands of dividing cells".

Thank you, will correct.

1.8.-p.4, line 116: please be even more clear with what the "depleted" cells and controls are treated with: are depleted cells treated with both inducers, and controls with neither?

We will make this more clear. Depleted cells are treated with both inducers, the control cells are not. However, in Figure 1A and in S1 we do controls to show that inducing TIR per se or adding aTC per se does not change growth rate or mitochondrial morphology. We will make this more clear.

1.9. -p.5, lines 147-148: the authors write "the rate with which the abundance of Cox2 and Var1 proteins decreases was similar to the rate of mtDNA loss" though the actual rate is not shown. Please calculate and show rates for these processes side by side to make comparison possible, or alternatively rephrase the statement.

Indeed this was not phrased well. We will call it dynamics rather than rates.

1.10. -Fig. 2d: changing the y-axis numbering to match those in panels a and b would facilitate comparisons.

Makes sense, we will change this.

1.11. Fig. 2e: it is recommended to label the western blot panels to indicate what protein is being imaged in each (Neongree,, Mrps5, Qcr7).

We will adapt the labelling to make it more clear.

1.12. -p.9, line 262: I suggest referencing Fig. 4e at the end of the first sentence for clarity.

We will modify the sentence as suggested.

1.13. -In the sections related to Fig. 3a and Fig. 5a as well as the connected supplemental data, the authors discuss both the median and the mean of mitochondrial mass and Atp6 protein, respectively. For purposes of clarity, I suggest decreasing the focus on the mean (that is provided only in the supplemental data) and focusing the text mainly on the median. The two show differing trends and it is very good that both are shown, but the clarity of the text can be improved by focusing more on the median where possible.

We will check the phrasing and simplify.

1.14. -p. 14, line 435: the statement that mt mass is maintained over the first 9h of depletion is only true for the mean mt mass, not for the median. Please make this clear or rephrase.

We will check phrasing, make it more clear and also point out the extended proteomics data (see Fig R1), which corresponds to the mean of the populations

1.15.-p.14, line 452: "mitofusions" should be "mitofusins".

Thanks for catching this.

Reviewer 2:

2.1. While inducible TIR is used to reduce background, the manuscript should rigorously exclude auxin/TIR off-targets (growth, mitochondrial phenotypes, gene expression). Please include full matched controls: (plus minus)auxin, (plus minus)TIR, epitope tag alone, and a degron control on an unrelated mitochondrial membrane protein.

We agree that rigorous controls are crucial for the interpretation of the results. However, we think we have already included most of the controls the reviewer is asking for, but we might have not pointed this out clearly enough. For example, in Fig 1A, we could make it more clear by adding more labels in which samples we added aTC, which is only described in the figure legend.

Here is a list of all the controls:

• Each depletion experiment is always matched with an experiment of the same strain without induction. So the genetic background as well as effects such as light exposure, time spent in the microfluidics systems, etc are controlled for.
• Figure S1D shows that the growth rate is wildtype like in a strain containing either the AID tag or the TIR protein AND upon addition of both chemicals. It also shows that the final genetic background (AID-tag and TIR) also grows like wildtype if the inducers are not added. This conclusively shows that neither the tags/constructs nor the chemicals per se affect growth rate
• In Figure S1C we show the mitochondrial morphology of the same controls. We will make sure to label them more consistently to match panel D, and include an actual wildtype and a FLAG-AID-Fzo1 strain without TIR treated with both aTC and 5-Ph-IAA as direct comparison
• In figure 1A we compare the Fzo1 protein levels of a strain with and without TIR. We show that in absence of TIR, adding either aTC or Auxin does not change Fzo1 levels and that the levels are comparable in the strain that is able to deplete Fzo1 directly before addition of 5-Ph-IAA (after 2 h of induction of TIR through addition of tetracycline)
• Additionally, in Figure S2C we show that two hours after adding aTC, the entire proteome does not change significantly apart from a strong induction of TIR. We can also make this more clear in the figure legend.
• Additionally, we will run a qPCR to carefully determine mtDNA levels of untreated wild-type cells, tetracycline treated wild-type cells and tetracycline induced TIR expressing cells to exclude effects of tetracycline as well as the expression of TIR on mtDNA. (also in response to 1.6.) In summary, we think we have controlled sufficiently for all confounding parameters and most importantly showed that addition of either aTC or Auxin as well as the FLAG-AID tag per se does not disturb mitochondria or cell growth. We do not see what a degron control on an unrelated protein will tell us. Depending on the nature of the protein, it may or may not have a phenotype that may or may not be related to morphology changes etc.

2.2. The Mitoloc preSu9 vs Cox4 import ratio is only a proxy of mitochondrial membrane potential (ΔΨm) and itself depends on mitochondrial mass, protein expression, matrix ATP, and import saturation. The authors need to calibrate ΔΨm with orthogonal dyes (TMRE/TMRM) and pharmacologic titrations (FCCP/antimycin/oligomycin) to generate a response curve; show that Mitoloc tracks dye-based ΔΨm across the relevant range and corrects for mass/photobleaching. Report single-cell ΔΨm vs mass residuals.

We completely agree that the MitoLoc system is only a rough proxy for the actual membrane potential. That is why we make no quantitative claims on the absolute value or absolute difference between groups of cells. We also make very clear in Fig 3B what we are actually measuring and can emphasize again in the text that this is only a proxy. We agree that it is a good idea to compare MitoLoc values to TMRE staining as the reviewer suggests, we will do these experiments in depleted and control cells at different timepoints. Please note though that also dye staining has its caveats, especially in dynamic live cell experiments. TMRM for example is not compatible with the acidic pH 5 medium that is typically used for yeast and subjecting cells to washing steps and higher pH may change both morphology of mitochondria and the MMP, especially in cells that are already “stressed”. We prefer not to complete elaborate pharmacological titration experiments because firstly, this was extensively done in the original MitoLoc paper by the Ralser lab ((Vowinckel et al. 2015), cited 120 times); secondly, the value of the MMP is not the most critical claim of the manuscript. See also 3.12. Please note that in Figure S4D we had already plotted MMP vs mitochondrial concentration.

2.3. To use Atp6-mNeon as a proxy for mtDNA is an assumption. Interpreting Atp6 intensity as "functional mtDNA" could be confounded by translation, turnover, or assembly. Please (i) report mtDNA copy number time courses (you have qPCR), nucleoid counts (DAPI/PicoGreen or TFAM/Abf2 tagging), and (ii) assess translation (e.g., 35S-labeling or puromycin proxies) and turnover (proteasome/AAA protease inhibition, mitophagy mutants -some data are alluded to- plus mRNA levels for mtDNA-encoded genes). This will support the "reduced synthesis" versus "increased degradation" conclusion.

We agree with all three reviewers that Atp6 is only a proxy for mtDNA (Jakubke et al. 2021; Roussou et al. 2024) and the correlation should be checked more carefully. We will use the very recently established Hi-NESS system to follow nucleoids/ mtDNA during depletion experiments. See detailed reply to 1.2.

(ii) in Figure 2C we inhibit mitochondrial translation and show that in this case control and depleted cells have the same level of Cox2, at least suggesting that degradation is not the key mechanism controlling the levels of mtDNA encoded proteins. We cannot do proteasome inhibitor assays since the nature of the AID-TIR systems requires an active proteasome. In figure S5C we show that the Atp6 depletion is similar in an atg32 deletion. This does not completely exclude a contribution of mitophagy to the observed phenotype, but does confirm that mitophagy is not the primary reason for cells becoming petite.

2.4. The promoter-NeonGreen reporters argue against transcriptional down-regulation of nuclear OXPHOS. Please add mRNA (RT-qPCR/RNA-seq) for representative genes and a pulse-chase or degradation-pathway dependency (e.g., proteasome/mitophagy/autophagy mutants) to firmly assign active degradation. The authors need to normalize proteomics to mitochondrial mass (e.g., citrate synthase/porin) to separate organelle abundance from protein turnover.

While we are happy to perform qPCR experiments for selected genes, a full RNA-seq experiment seems outside the scope of this study. As explained above, a proteasome inhibitor experiment is not possible in this set-up. Bulk mitophagy/autophagy seems unlikely to be the cause of the decrease of the nuclear-encoded OXPHOS proteins, since most other mitochondrial proteins do not decrease on average on population level in the first hours. This data is now plotted as additional figure (see below) and will be included in the supplementary of the revised manuscript (Fig R1E).

2.5. Using preSu9-mCardinal intensity as "mitochondrial concentration" is sensitive to expression, import competence, and morphology/segmentation. The authors should provide validation that this metric tracks 3D volume across fragmentation states (e.g., correlation with mito-GFP volumetrics; detergent-free CS activity; TOMM20/Por1 immunoblot per cell).

We agree that this is an important point and the co-authors discussed this point quite intensively. In figure S3A and B we show (using confocal data) that there is a very strong correlation between the total fluorescence signal and the 3D volume reconstruction. However, the slope of the correlation is different between tubular and fragmented mitochondria (compare panels A and B) and see figure legend. Since we are dealing with diffraction-limited objects it is likely that the 3D reconstruction is sensitive to morphology, especially if mitochondria are “clumping”. We therefore think that the total fluorescence signal is actually a better estimate of mitochondrial mass per cell than the 3D volume reconstruction (especially for our data obtained with a conventional epifluorescence microscope). The mean of the total mitochondrial fluorescence also better matches the population average mitochondrial proteome (Fig R1E). To consolidate this assumption, we will additionally compare our data to a strain with Tom70-Neongreen and to MMP independent dyes.

Notably, since the morphology is similarly altered in mothers and buds this is of minor impact for our main point – the unequal distribution between mother and buds.

2.6. The unequal mother-daughter distribution is compelling, but causality remains inferred. Test whether modulating inheritance machinery (actin cables/Myo2, Num1, Mmr1) or altering fission (Dnm1 inhibition) modifies segregation defects and rescues mtDNA/Atp6 decline. Complementation with Fzo1 re-expression at defined times would help order the phenotype cascade.

We agree that rescue experiments would be very useful. We have some preliminary data for tether experiments, for example with Num1. The general problem is that the fragmented mitochondria clump together. We have not found a method to restore an equal distribution between mother and daughter cells. We will try to optimize the assay, but are not overly confident it will work. Mmr1 deletion aggravates the Fzo1 phenotype, likely also because the distribution becomes even more heterogeneous, but we have not rigorously analyzed this.

We like the idea of the Fzo1 re-expression and will run such experiments. This will be especially powerful in combination with the new HI-NESS mtDNA reporter. We may be able to track exactly when cells reach the point-of-no return and become petite. This will also help connecting our mathematical model more directly to the data.

2.7. The model is useful but should include parameter sensitivity (segregation variance, synthesis slopes, initial nucleoid number) and prospective validation (e.g., predict rescue upon partial restoration of synthesis or inheritance, then test experimentally).

We will refine our model to include the to-be-measured nucleoids/mtDNA values. We will include a parameter sensitivity analysis with the updated model.

Reviewer 3:

3.1. About the use of Atp6 as a good proxy for mtDNA content. This is assumed from l285 onwards, based on a previous publication. As the link is fairly central to part of the paper's arguments, and the system in this study is being perturbed in several different ways, a stronger argument or demonstration that this link remains intact (and unchanged, as it is used in comparisons) would seem important.

We agree, see 1.2.

3.2. About confounding variables and processes. The study does an admirable job of being transparent and attempting to control for the many different influences involved in the physical-genetic link. But some remain less clearly unpacked, including some I think could be quite important. For example, there is a lot of focus on mito concentration -- but given the phenotypes are changing the sizes of cells, do concentration changes come from volume changes, mito changes, or both? In "ruling out" mitophagy -- a potentially important (and intuitive) influence, the argument is not presented as directly as it could be and it's not completely clear that it can in fact be ruled out in this way. There are a couple of other instances which I've put in the smaller points below.

Thank you for acknowledging our efforts to show transparent and well-controlled experiments! We address each of the specific points below.

3.3. full genus name when it first appears

We will add the full name.

3.4. I may be wrong here, but I thought the petite phenotype more classically arises from mtDNA deletion mutations, not loss? The way this is phrased implies that mtDNA loss is [always] the cause. Whether I'm wrong on that point or not, the petite phenotype should be described and referenced.

We can expand the text and cite additional relevant papers. The term “petite” refers to any strain that is respiratory incompetent and leads to small colonies (not necessarily small cells!) (Seel et al. 2023). This can be mutations or gene loss (fragments) on the mtDNA (these are called cytoplasmic petite), or chemically induced loss of mtDNA (e.g. EtBr), or mutations of nuclear genes required for respiration (these are termed nuclear petite; some nuclear petites show loss of mtDNA in addition to the mutation in the nuclear genome) (Contamine and Picard 2000).

3.5. para starting l59 -- should mention for context that mitochondria in (healthy, wildtype) yeast are generally much more fused than in other organisms

ok.

3.6. Fig 1C -- very odd choice of y-axis range! either start at zero or ensure that the data fill as much vertical space of the plot as possible

True, this was probably some formatting relic. We will adapt the axis to fill the full space. Most of our axes start at 0, but that doesn’t make so much sense here, since we consider the solidity in the control as “baseline”.

3.7. "wild-type like more tubular mitochondria" reads rather awkwardly. "more tubular mitochondria (as in the wild-type)"?

Thank you, sounds better.

3.8. l106 -- imaging artefacts? are mitos fragmenting because of photo stress? -- this is mentioned in l577-8 in the Methods, but the data from the growth rate and MMP comparison isn't given -- an SI figure would be helpful here. It would be reassuring to know that mito morphology wasn't changing in response to phototoxicity too.

In the methods we just briefly point out that we have done all our “due diligence” controls to check that we do not generate phototoxicity, something that we highlight in the cited review. We do not explicitly have a figure for this, but figure S1A shows that the solidity of the mitochondrial network in control cells stays the same over 9 hours, even though these cells are exposed to the same cultivation and imaging regime as the depleted cells. We will also add a picture of control cells after 9 h. In S1B we show that control cells containing TIR but no AID tag treated with both chemicals imaged over 9 hours also show the same solidity (~mitochondrial morphology) as untreated control. Also, the doubling times of cells grown in our imaging system (Fig R1B) are very similar to the shake flask (Fig R1A). All in all, we are very confident that our imaging settings did not impact our reported phenotypes.

3.9. para l146 -- so this suggests mtDNA-encoded proteins have a very rapid turnover, O(hours) -- is this known/reasonable?

Reference (Christiano et al. 2014) suggests that respiratory chain proteins are shorter lived than the average yeast protein. However, based on Figure 2C we think the dynamics mostly speak for a dilution by growth.

3.10. section l189 -- it's hard to reason fully about these statistics of mitochondrial concentration given that the petite phenotype is fundamentally affecting overall cell volume. can we have details on the cell size distribution in parallel with these results? to put it another way -- how does mitochondrial *amount* per cell change?

This is a good point. We report mostly on mitochondrial “concentrations” because we think this is what the cell actually cares about (mitochondrial activity in relationship to cytosolic activity). But we will include additional graphs on mitochondrial amount as well as size distributions (Fig R1C, related to Fig 4F). We can already point out that the size distribution of the population does not change much in the first hours. The “petite” phenotype refers to small colonies on growth medium with limited supply of a fermentable carbon source, not to smaller size of single cells.

3.11. l199 the mean in Fig S3C certainly does change -- it increases, clearly relative both to control and to its initial value. rather than sweeping this under the carpet we should look in more detail to understand it (a consequence of the increased skew of the distribution)?

This relates somewhat to the previous point. The increase in average concentration is not due to an increased amount in the population, but due to the fact that it is the small buds that get a very high amount of the mitochondria which “exaggerates” the asymmetric/heterogenous distribution. This will be clarified by the figures we mention in the point above.

3.12. para line 206 -- this doesn't make it clear whether your MMP signal is integrated over all mitochondria in the cell, or normalised by mitochondrial content? this matters quite a lot for the interpretation if the distributions of mitochondrial content are changing. reading on, this is even more important for para line 222. Reading further on, there is an equation on l612 that gives a definition, but it doesn't really clarify (apologies if I'm misunderstanding).

For each cell, we basically calculate the relative mitochondrial enrichment of the MMP sensitive vs the MMP insensitive pre-sequence.

So, MMP= (total intensity of mitochondrial pre-Cox4 Neongreen/ total intensity of mitochondrial pre-Su9 Cardinal) / (total cytosolic pre-Cox4 Neongreen/ total cytosolic pre-Su9 Cardinal).

We calculate this value for each cell, but we do not have the optical resolution to calculate it for individual mitochondrial fragments.

Both constructs are driven by the same strong promoter, so transcription of the fluorophore should never limit the uptake. Also, in Figure 3D we compare control and depleted cells with similar total mitochondrial concentration, so the difference must be due to a different import of the two fluorophores, see also Fig S4D. The calculated “MMP” value is of course only a crude proxy for the actual membrane potential in millivolts and we do not want to make any claims on absolute values or quantitative differences. But essentially what we are interested in is “mitochondrial health/activity” and we think the system is good at reporting this. See also 2.2.

3.13. l230 -- a point of personal interest -- low mito concentrations are connected to low "function" (MMP) and give extended division times -- this is interestingly exactly the model needed to reproduce observations in HeLa cells (https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1002416). That model went on to predict several aspects of downstream cellular behaviour -- it would be very interesting to see how compatible that picture (parameterised using HeLa observations) is with yeast!

Thank you for pointing out your interesting paper, which we will include in our discussion. Another recent preprint about fission yeast (Chacko et al. 2025) also fits into this picture. Since you were kind enough to disclose your identity, we would be happy to discuss this further with you in person if we can maybe follow-up on this.

3.14. l239 "less mitochondria" -- a bit tricky but I'd say "fewer mitochondria" or "less mitochondrial content"

Thanks, we will think about how to best rephrase this, probably less mitochondrial content.

3.15. Section l234 So here (and in Fig 4) the focus is on overall distributions of mitochondrial concentration in different cells (mother-to-be, mother, bud; gen 1, gen >1). But we've just seen that one effect of fzo1 is to broader the distribution of mitochondrial concentration across cells. Can't we look in more depth at the implications of this heterogeneity? For example in Fig 4F (which is cool) we look at the distribution of all fzo1 mothers-to-be, mothers, and buds. But this loses information about the provenance. For example, do mothers-to-be with extremely low mito concentrations just push everything to the bud, while mothers-to-be with high mito concentrations distribute things more evenly? It would seem very easy and very interesting to somehow subset the distribution of mothers-to-be by concentration and see how different subsets behave

This is a good point. When analyzing the data, we pretty much plotted everything against everything and then chose the graphs that we think will best guide the reader through the story-line. We can make additional supplementary plots where we show the starting concentrations/amounts of the mother in relationship to the resulting split ratio at the end of the cycle (Fig R1D).

3.16. l285 -- experimental design -- do we know that Atp6 will continue to be a good proxy for functional mtDNA in the face of the perturbations provided by Fzo1 depletion? Especially if there is impact on the expression of mitoribosomes, the relationship between mtDNA and Atp6 may look rather different in the mutant?

This is actually our top-priority experiment now. We will use the HI-NESS system and possibly DAPI staining to make a more direct link to mtDNA/ nucleoid numbers, see 1.2.

3.17. l290 -- ruled out mitophagy. This message could be much clearer. Comparing Fig S5C and Fig 3A side-by-side is a needlessly difficult task -- put Fig 3A into Fig S5. Then we see that when mitophagy is compromised, the distribution of mitochondrial concentration has a lower median and much lower upper quartile than in the mitophagy-equipped Fzo1 mutant? What is going on here? For a paper motivated by disentangling coupled mechanisms, this should be made clearer!

Thanks for pointing this out. We can of course easily include the control in the corresponding figure. Compromising mitophagy is likely to generally affect mitochondrial health and turnover a little bit, independent of what is going on with Fzo1. The second evidence that speaks against large-scale mitophagy is the proteomics data: On population level the dynamics of the respiratory chain proteins are very different from those of other (nuclear encoded) mitochondrial proteins. We will add additional supplementary figures to make this more clear, see Fig R1E. Most mitochondrial proteins in the proteomics experiment stay constant in the first few hours, consistent with the imaging data showing that the mean mitochondrial content of the population does not change initially. This again highlights that it is the unequal distribution which is the problem and not massive degradation of mitochondria.

3.18. With the Atp6 signal, how do we know that fluorescence from different cells is comparable? Buds will be smaller than mother cells for example, potentially leading to less occlusion of the fluorescent signal by other content in the cytoplasm

This is of course a general problem that anyone faces doing quantitative fluorescence microscopy. From the technical side, we have done the best we could by taking a reasonable amount of z-slices and by choosing fluorophores that are in a range with little cellular background fluorescence (e.g. Neongreen is much better than GFP). From a practical standpoint, we are always comparing to the control, which is subject to the same technical limitations as the depleted cells and the cell sizes are very similar. So, even if we are systematically overestimating the Atp6 concentration in the bud by a few %, the difference to the control would still be qualitatively true. We therefore do not think that any of our conclusions are affected by this.

3.19. l343 -- maintenance of mtDNA -- here the point about l285 (is the Atp6-mtDNA relationship the same in the Fzo1 mutant) is particularly important, as we're directly tying findings about the protein product to implications about the mtDNA

We will carefully address this, see above.

3.20. l367 -- on a first read this description of the model feels like lots of choices have been made without being fully justified. Why a log-normal distribution (when the fit to the data looks rather flawed); why the choice of 5 groups for nucleoid number (why not 3? or 8?); the process used for parameter fitting is very unclear (after reading the methods I think some of these values are read directly from the data, but the shapes of the distributions remain unexplained). l705 -- presumably the ratio was drawn from a log-normal distribution and then the corresponding nucleoid numbers were rounded to integers? the ratio itself wasn't rounded? (also l367) How were the log-normal distributions fitted to experiments (Figs. S7A,B)? Just by eye?

We will update our model based on measured nucleoid counts and then explain more stringently the choices we make/ parameters we select.

3.21. l711 by random selection -- just at random? ("selection" could be confusing) Overall, it feels like the model may be too complicated for what it needs to show. Either (a) the model should show qualitatively that unequal inheritance and reduced production leads to rapid loss -- which a much simpler model, probably just involving a couple of lines of algebra, could show. Or (b) the model should quantitatively reproduce the particular numerical observations from the experiments -- it's not totally clear that it does this (do the cell-cycle-based decay timescales in Fig 7 correspond to the hour-based decay timescales in other plots, for example). At the moment the model is at a (b) level of detail but it's only clear that it's reporting the (a) level of results.

If the HI-NESS and Fzo1 re-addition experiments work as explained above, all parameters will have direct experimental data, and we should get much closer to (a).

3.22. A lot of the discussion repeats the results; depending on editorial preferences some of this text could probably be pared back to focus on the literature connections and context.

We will think about streamlining the discussion once some of the additional material alluded to above has been added.

3.23. Data availability -- it looks like much of the data required to reproduce the results is not going to be made available. Images and proteomic data are promised, but the data associated with mitochondrial concentration and other features are not mentioned. For FAIR purposes all the data (including statistics from analysis of the images) should be published.

We maybe didn’t phrase this clearly. All data will be made available. Where technically feasible, this will be directly accessible in a repository, otherwise by request to the corresponding author.

On our OMERO server, we have deposited many TB of raw images as well as all the intermediate steps such as segmentation masks, and the csv files with all the extracted data for each cell (including background corrections etc). Additionally, we can include csvs with the data grouped in a way that we used to generate all the box blots etc. As of now, the OMERO data is unfortunately only available by requesting a personal guest login from our bioinformatics facility, but we were promised that with the next technical update there will be a public link available. The proteomics data and the model are already fully accessible. The raw western blot images with corresponding ponceau staining will be included with the final publication either as additional supplementary material or in whatever format matches the journal requirements.

3.24 l660 -- can an overview of the EM protocol be given, to avoid having to buy the Mayer 2024 article?

The cited paper is open access. But we can also include more details in our method section.

References:

Chacko, L. A., H. Nakaoka, R. Morris, W. Marshall, and V. Ananthanarayanan. 2025. 'Mitochondrial function regulates cell growth kinetics to actively maintain mitochondrial homeostasis', bioRxiv.

Christiano, R., N. Nagaraj, F. Frohlich, and T. C. Walther. 2014. 'Global proteome turnover analyses of the Yeasts S. cerevisiae and S. pombe', Cell Rep, 9: 1959-65.

Contamine, V., and M. Picard. 2000. 'Maintenance and integrity of the mitochondrial genome: a plethora of nuclear genes in the budding yeast', Microbiol Mol Biol Rev, 64: 281-315.

Deng, Jingti, Lucy Swift, Mashiat Zaman, Fatemeh Shahhosseini, Abhishek Sharma, Daniela Bureik, Francesco Padovani, Alissa Benedikt, Amit Jaiswal, Craig Brideau, Savraj Grewal, Kurt M. Schmoller, Pina Colarusso, and Timothy E. Shutt. 2025. 'A novel genetic fluorescent reporter to visualize mitochondrial nucleoids', bioRxiv: 2023.10.23.563667.

Di Bartolomeo, F., C. Malina, K. Campbell, M. Mormino, J. Fuchs, E. Vorontsov, C. M. Gustafsson, and J. Nielsen. 2020. 'Absolute yeast mitochondrial proteome quantification reveals trade-off between biosynthesis and energy generation during diauxic shift', Proc Natl Acad Sci U S A, 117: 7524-35.

Ebert, A. C., N. L. Hepowit, T. A. Martinez, H. Vollmer, H. L. Singkhek, K. D. Frazier, S. A. Kantejeva, M. R. Patel, and J. A. MacGurn. 2025. 'Sphingolipid metabolism drives mitochondria remodeling during aging and oxidative stress', bioRxiv.

Jakubke, C., R. Roussou, A. Maiser, C. Schug, F. Thoma, R. Bunk, D. Horl, H. Leonhardt, P. Walter, T. Klecker, and C. Osman. 2021. 'Cristae-dependent quality control of the mitochondrial genome', Sci Adv, 7: eabi8886.

Khan, Abdul Haseeb, Xuefang Gu, Rutvik J. Patel, Prabha Chuphal, Matheus P. Viana, Aidan I. Brown, Brian M. Zid, and Tatsuhisa Tsuboi. 2024. 'Mitochondrial protein heterogeneity stems from the stochastic nature of co-translational protein targeting in cell senescence', Nature Communications, 15: 8274.

Martin, J., K. Mahlke, and N. Pfanner. 1991. 'Role of an energized inner membrane in mitochondrial protein import. Delta psi drives the movement of presequences', J Biol Chem, 266: 18051-7.

Osman, C., T. R. Noriega, V. Okreglak, J. C. Fung, and P. Walter. 2015. 'Integrity of the yeast mitochondrial genome, but not its distribution and inheritance, relies on mitochondrial fission and fusion', Proc Natl Acad Sci U S A, 112: E947-56.

Perić, Matea, Peter Bou Dib, Sven Dennerlein, Marina Musa, Marina Rudan, Anita Lovrić, Andrea Nikolić, Ana Šarić, Sandra Sobočanec, Željka Mačak, Nuno Raimundo, and Anita Kriško. 2016. 'Crosstalk between cellular compartments protects against proteotoxicity and extends lifespan', Scientific Reports, 6: 28751.

Roussou, Rodaria, Dirk Metzler, Francesco Padovani, Felix Thoma, Rebecca Schwarz, Boris Shraiman, Kurt M. Schmoller, and Christof Osman. 2024. 'Real-time assessment of mitochondrial DNA heteroplasmy dynamics at the single-cell level', The EMBO Journal, 43: 5340-59-59.

Seel, A., F. Padovani, M. Mayer, A. Finster, D. Bureik, F. Thoma, C. Osman, T. Klecker, and K. M. Schmoller. 2023. 'Regulation with cell size ensures mitochondrial DNA homeostasis during cell growth', Nat Struct Mol Biol, 30: 1549-60.

Vowinckel, J., J. Hartl, R. Butler, and M. Ralser. 2015. 'MitoLoc: A method for the simultaneous quantification of mitochondrial network morphology and membrane potential in single cells', Mitochondrion, 24: 77-86.

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Referee #3

Evidence, reproducibility and clarity

This article addresses the connection between perturbed mitochondrial structure and genetics in yeast. When mitochondrial fusion is compromised, what is the chain of causality -- the mechanism -- that leads to mtDNA populations becoming depleted? This is a fascinating question, linking physical cell biology to population genetics. I admire the philosophy of the research, acknowledging and attempt to control for the many possible confounding influences. The manuscript describes the context and the research tightly and digestibly; the figures illustrate the results in a clear and natural way.

For transparency, I am Iain Johnston and I am happy for this review to be treated as public domain. To my eyes my most important shortcoming as a review is my relative lack of familiarity with the yeast fzo1 mutant; while I am familiar with analysis of yeast mito morphology and mtDNA segregation, a reviewer familiar with the nuances of this strain and its culture would be a useful complement.

I have a few more general points and a collection of smaller points below that I believe might help make the story more robust.

General points

1. About the use of Atp6 as a good proxy for mtDNA content. This is assumed from l285 onwards, based on a previous publication. As the link is fairly central to part of the paper's arguments, and the system in this study is being perturbed in several different ways, a stronger argument or demonstration that this link remains intact (and unchanged, as it is used in comparisons) would seem important.
2. About confounding variables and processes. The study does an admirable job of being transparent and attempting to control for the many different influences involved in the physical-genetic link. But some remain less clearly unpacked, including some I think could be quite important. For example, there is a lot of focus on mito concentration -- but given the phenotypes are changing the sizes of cells, do concentration changes come from volume changes, mito changes, or both? In "ruling out" mitophagy -- a potentially important (and intuitive) influence, the argument is not presented as directly as it could be and it's not completely clear that it can in fact be ruled out in this way. There are a couple of other instances which I've put in the smaller points below.

Smaller points

l47 full genus name when it first appears

l58 I may be wrong here, but I thought the petite phenotype more classically arises from mtDNA deletion mutations, not loss? The way this is phrased implies that mtDNA loss is [always] the cause. Whether I'm wrong on that point or not, the petite phenotype should be described and referenced.

para starting l59 -- should mention for context that mitochondria in (healthy, wildtype) yeast are generally much more fused than in other organisms

Fig 1C -- very odd choice of y-axis range! either start at zero or ensure that the data fill as much vertical space of the plot as possible

l105 "wild-type like more tubular mitochondria" reads rather awkwardly. "more tubular mitochondria (as in the wild-type)"?

l106 -- imaging artefacts? are mitos fragmenting because of photo stress? -- this is mentioned in l577-8 in the Methods, but the data from the growth rate and MMP comparison isn't given -- an SI figure would be helpful here. It would be reassuring to know that mito morphology wasn't changing in response to phototoxicity too.

para l146 -- so this suggests mtDNA-encoded proteins have a very rapid turnover, O(hours) -- is this known/reasonable?

section l189 -- it's hard to reason fully about these statistics of mitochondrial concentration given that the petite phenotype is fundamentally affecting overall cell volume. can we have details on the cell size distribution in parallel with these results? to put it another way -- how does mitochondrial amount per cell change?

l199 the mean in Fig S3C certainly does change -- it increases, clearly relative both to control and to its initial value. rather than sweeping this under the carpet we should look in more detail to understand it (a consequence of the increased skew of the distribution)?

para line 206 -- this doesn't make it clear whether your MMP signal is integrated over all mitochondria in the cell, or normalised by mitochondrial content? this matters quite a lot for the intepretation if the distributions of mitochondrial content are changing. reading on, this is even more important for para line 222. Reading further on, there is an equation on l612 that gives a definition, but it doesn't really clarify (apologies if I'm misunderstanding).

l230 -- a point of personal interest -- low mito concentrations are connected to low "function" (MMP) and give extended division times -- this is interestingly exactly the model needed to reproduce observations in HeLa cells (https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1002416). That model went on to predict several aspects of downstream cellular behaviour -- it would be very interesting to see how compatible that picture (parameterised using HeLa observations) is with yeast!

l239 "less mitochondria" -- a bit tricky but I'd say "fewer mitochondria" or "less mitochondrial content"

Section l234 So here (and in Fig 4) the focus is on overall distributions of mitochondrial concentration in different cells (mother-to-be, mother, bud; gen 1, gen >1). But we've just seen that one effect of fzo1 is to broader the distribution of mitochondrial concentration across cells. Can't we look in more depth at the implications of this heterogeneity? For example in Fig 4F (which is cool) we look at the distribution of all fzo1 mothers-to-be, mothers, and buds. But this loses information about the provenance. For example, do mothers-to-be with extremely low mito concentrations just push everything to the bud, while mothers-to-be with high mito concentrations distribute things more evenly? It would seem very easy and very interesting to somehow subset the distribution of mothers-to-be by concentration and see how different subsets behave

l285 -- experimental design -- do we know that Atp6 will continue to be a good proxy for functional mtDNA in the face of the perturbations provided by Fzo1 depletion? Especially if there is impact on the expression of mitoribosomes, the relationship between mtDNA and Atp6 may look rather different in the mutant?

l290 -- ruled out mitophagy. This message could be much clearer. Comparing Fig S5C and Fig 3A side-by-side is a needlessly difficult task -- put Fig 3A into Fig S5. Then we see that when mitophagy is compromised, the distribution of mitochondrial concentration has a lower median and much lower upper quartile than in the mitophagy-equipped Fzo1 mutant? What is going on here? For a paper motivated by disentagling coupled mechanisms, this should be made clearer!

With the Atp6 signal, how do we know that fluorescence from different cells is comparable? Buds will be smaller than mother cells for example, potentially leading to less occlusion of the fluorescent signal by other content in the cytoplasm

l336 -- similar to the Jajoo et al. mechanism in fission yeast -- but are you talking about feedback control of the mtDNA or the protein (or mRNA) product?

l343 -- maintenance of mtDNA -- here the point about l285 (is the Atp6-mtDNA relationship the same in the Fzo1 mutant) is particularly important, as we're directly tying findings about the protein product to implications about the mtDNA

l367 -- on a first read this description of the model feels like lots of choices have been made without being fully justified. Why a log-normal distribution (when the fit to the data looks rather flawed); why the choice of 5 groups for nucleoid number (why not 3? or 8?); the process used for parameter fitting is very unclear (after reading the methods I think some of these values are read directly from the data, but the shapes of the distributions remain unexplained). l705 -- presumably the ratio was drawn from a log-normal distribution and then the corresponding nucleoid numbers were rounded to integers? the ratio itself wasn't rounded? (also l367) How were the log-normal distributions fitted to experiments (Figs. S7A,B)? Just by eye? l711 by random selection -- just at random? ("selection" could be confusing) Overall, it feels like the model may be too complicated for what it needs to show. Either (a) the model should show qualitatively that unequal inheritance and reduced production leads to rapid loss -- which a much simpler model, probably just involving a couple of lines of algebra, could show. Or (b) the model should quantitatively reproduce the particular numerical observations from the experiments -- it's not totally clear that it does this (do the cell-cycle-based decay timescales in Fig 7 correspond to the hour-based decay timescales in other plots, for example). At the moment the model is at a (b) level of detail but it's only clear that it's reporting the (a) level of results.

A lot of the discussion repeats the results; depending on editorial preferences some of this text could probably be pared back to focus on the literature connections and context.

Data availability -- it looks like much of the data required to reproduce the results is not going to be made available. Images and proteomic data are promised, but the data associated with mitochondrial concentration and other features are not mentioned. For FAIR purposes all the data (including statistics from analysis of the images) should be published.

l660 -- can an overview of the EM protocol be given, to avoid having to buy the Mayer 2024 article?

Significance

This is a powerful and thoughtful study that provides a collection of new mechanistic insights into the link between physical and genetic properties of mitochondria in yeast. Cell biologists, geneticists, and the mitochondrial field will find this of potentially deep interest. Because of the mode and dynamics of inheritance in budding yeast, findings here may not be directly transferrable to other eukaryotes, but these insights are still of interest for researchers outside of yeast for their insight into how this well-studied system manages its mitochondrial populations.

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Referee #2

Evidence, reproducibility and clarity

Dengler and colleagues use an AID-based acute depletion of Fzo1 in budding yeast, coupling microfluidics live imaging, single-cell quantification (>30k cells), proteomics, an mtDNA-encoded Atp6 reporter, and simple modeling to argue that fusion loss causes (i) rapid fragmentation and ΔΨm decline, (ii) progressive mtDNA/RC depletion, and (iii) unequal mother-daughter mitochondrial inheritance; together with a failure of compensatory synthesis, these changes drive petite formation. The time-resolved design is valuable, but several readouts are indirect, and some claims (particularly those regarding membrane potential, synthesis "failure," and causality) appear over-interpreted without additional controls.

Major points

1. While inducible TIR is used to reduce background, the manuscript should rigorously exclude auxin/TIR off-targets (growth, mitochondrial phenotypes, gene expression). Please include full matched controls: {plus minus}auxin, {plus minus}TIR, epitope tag alone, and a degron control on an unrelated mitochondrial membrane protein.
2. The Mitoloc preSu9 vs Cox4 import ratio is only a proxy of mitochondrial membrane potential (ΔΨm) and itself depends on mitochondrial mass, protein expression, matrix ATP, and import saturation. The authors need to calibrate ΔΨm with orthogonal dyes (TMRE/TMRM) and pharmacologic titrations (FCCP/antimycin/oligomycin) to generate a response curve; show that Mitoloc tracks dye-based ΔΨm across the relevant range and corrects for mass/photobleaching. Report single-cell ΔΨm vs mass residuals.
3. To use Atp6-mNeon as a proxy for mtDNA is an assumption. Interpreting Atp6 intensity as "functional mtDNA" could be confounded by translation, turnover, or assembly. Please (i) report mtDNA copy number time courses (you have qPCR), nucleoid counts (DAPI/PicoGreen or TFAM/Abf2 tagging), and (ii) assess translation (e.g., 35S-labeling or puromycin proxies) and turnover (proteasome/AAA protease inhibition, mitophagy mutants -some data are alluded to- plus mRNA levels for mtDNA-encoded genes). This will support the "reduced synthesis" versus "increased degradation" conclusion.
4. The promoter-NeonGreen reporters argue against transcriptional down-regulation of nuclear OXPHOS. Please add mRNA (RT-qPCR/RNA-seq) for representative genes and a pulse-chase or degradation-pathway dependency (e.g., proteasome/mitophagy/autophagy mutants) to firmly assign active degradation. The authors need to normalize proteomics to mitochondrial mass (e.g., citrate synthase/porin) to separate organelle abundance from protein turnover.
5. Using preSu9-mCardinal intensity as "mitochondrial concentration" is sensitive to expression, import competence, and morphology/segmentation. The authors should provide validation that this metric tracks 3D volume across fragmentation states (e.g., correlation with mito-GFP volumetrics; detergent-free CS activity; TOMM20/Por1 immunoblot per cell).
6. The unequal mother-daughter distribution is compelling, but causality remains inferred. Test whether modulating inheritance machinery (actin cables/Myo2, Num1, Mmr1) or altering fission (Dnm1 inhibition) modifies segregation defects and rescues mtDNA/Atp6 decline. Complementation with Fzo1 re-expression at defined times would help order the phenotype cascade.
7. The model is useful but should include parameter sensitivity (segregation variance, synthesis slopes, initial nucleoid number) and prospective validation (e.g., predict rescue upon partial restoration of synthesis or inheritance, then test experimentally).

Significance

The dataset is rich and the time-resolved approach strong, but key conclusions rely on indirect proxies and need orthogonal validation and at least one causal rescue experiment to avoid over-interpretation.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by Dengler et al examines the mechanisms underlying the mtDNA depletion observed in cells where mitochondrial fusion is disrupted by depletion of the fusion factor Fzo1. In Saccharomyces cerevisiae, the authors deplete Fzo1 and use live-cell imaging of thousands of cells to follow the effects and their dynamic following Fzo1 depletion. They find that Fzo1-depleted cells show very rapid mitochondrial fragmentation (within 1h of Fzo1 depletion), and also an immediate drop in mitochondrial membrane potential (MMP). MtDNA is lost by 15h, and along with it the expression of mitochondrially-encoded proteins. Nuclear-encoded mitochondrial proteins are also decreased though somewhat later, and the authors find that this is largely due to their degradation (probably a consequence of lack of mitochondrial import into low-MMP cells). Most importantly, the study identifies two separate mechanisms that together contribute to the loss of mt-encoded proteins in Fzo1-depleted cells: unequal distribution of mitochondria during cell division and the reduction of a fusion-dependent compensatory synthesis of mt-encoded proteins. Unexpectedly, Fzo1-depleted cells end up passing an increased (rather than decreased) amount of mitochondria and mitochondria-encoded proteins to their daughters. Over several generations, and combined with the loss of the compensatory synthesis of more mt-encoded proteins, this leads to the progressive loss of mtDNA and mtDNA-encoded proteins in the population.

The study is very thorough and the experiments contain the appropriate controls. The conclusions are convincing and largely supported by the experimental data that has been appropriately replicated. The data presentation is generally clear although the text could benefit from some streamlining.

However, addressing the following major comments is required:

1. Statistical comparisons are missing throughout the manuscript (with the exception of Fig. 2c). Appropriate statistical tests, along with p-values, should be used and reported where different gorups are compared, for example (but not limited to) Fig. 3d and most panels of Fig. 4.
2. I do not agree with the use of Atp6 protein as a direct read-out of mtDNA content. While Atp6 protein levels will decrease with decreasing mtDNA content, the inverse is not necessarily true: decreased Atp6 protein levels do not necessarily indicate decreased mtDNA levels, because they could alternatively or additionally be caused by decreased transcription and/or translation. Therefore, please do not equate Atp6 protein levels to mtDNA levels, and instead rephrase the text referencing the Atp6 experiments in the Results and Discussion sections to measure "mtDNA expression" or "mt-encoded protein" or similar. For example, on p. 14 line 431 should read "mtDNA expression" rather than "decreased synthesis of mtDNA", and line 440 on the same page "mean mtDNA levels" should be "mtDNA expression" or similar.
3. In Fig. 3, the authors use the fluorescence intensity of a mitochondrially-targeted mCardinal as a read-out of mitochondrial mass. Please provide evidence that this is not affected by MMP, either with relevant references or by control experiments (e.g. comparing it to N-acridine orange or other MMP-independent dyes or methods).
4. In Fig. 2e-f, the authors use a promoter reporter with Neongreen to answer whether the reduced levels of the nuclear-encoded mitochondrial proteins Mrps5 and Qcr7 are due to decreased expression or to protein degradation, and find no evidence of degradation of the Neongreen reporter protein. However, subcellular localization might affect the availability of the protein to proteases. Although not absolutely required, it would be relevant to know if the Neongreen fusion protein is found in the same subcellular compartment as Mrps5 and Qcr7 at 0h and 9h after Fzo1 depletion.
5. Fzo1 depletion leads to a very rapid drop in MMP during the first hour of depletion. In the Discussion, can the authors speculate on the possible mechanism of this rapid MMP drop that occurs well before mtDNA or mt-encoded proteins are decreased in level?
6. In Fig. 2a, the mtDNA copy number of Fzo1-depleted cells is ca 1.3-fold of the control cells at the 0h timepoint. Why might this be? Is it an impact of one of the inducers? If so, we might be looking at the combination of two different processes when measuring copy number: one that is an induction caused by the inducer(s), and the other a consequence of Fzo1 depletion itself.

Minor comments:

• p. 3, line 71: "ten thousands of dividing cells.." should be "tens of thousands of dividing cells".
• p.4, line 116: please be even more clear with what the "depleted" cells and controls are treated with: are depleted cells treated with both inducers, and controls with neither?
• p.5, lines 147-148: the authors write "the rate with which the abundance of Cox2 and Var1 proteins decreases was similar to the rate of mtDNA loss" though the actual rate is not shown. Please calculate and show rates for these processes side by side to make comparison possible, or alternatively rephrase the statement.
• Fig. 2d: changing the y-axis numbering to match those in panels a and b would facilitate comparisons.
• Fig. 2e: it is recommended to label the western blot panels to indicate what protein is being imaged in each (Neongree,, Mrps5, Qcr7).
• p.9, line 262: I suggest referencing Fig. 4e at the end of the first sentence for clarity.
• In the sections related to Fig. 3a and Fig. 5a as well as the connected supplemental data, the authors discuss both the median and the mean of mitochondrial mass and Atp6 protein, respectively. For purposes of clarity, I suggest decreasing the focus on the mean (that is provided only in the supplemental data) and focusing the text mainly on the median. The two show differing trends and it is very good that both are shown, but the clarity of the text can be improved by focusing more on the median where possible.
• p. 14, line 435: the statement that mt mass is maintained over the first 9h of depletion is only true for the mean mt mass, not for the median. Please make this clear or rephrase.
• p.14, line 452: "mitofusions" should be "mitofusins".

Referees cross-commenting

I think that the reviews of the other two reviewers are both insightful and constructive. Especially the rescue experiment suggested by Reviewer 2 could provide strong support for the interpretations of the study. Note that all three reviewers ask for validation of the use of Atp6p as a read-out of mtDNA function, and that all agree the data is powerful and the study of value to the field.

Significance

The fact that disruption of mt fusion leads to mtDNA loss has been known for some time, but the mechanism behind this phenomenon has remained unknown to date. This thorough and precise study by Dengler et al uses state-of-the-art single-cell analysis to dissect the mechanisms underlying the mtDNA loss following the disruption of mt fusion, and convincingly reveal that it is caused by two different mechanisms: i) the inequal inheritance of mitochondria between mother and bud, and ii) the loss of a compensatory mechanism that normally maintains homeostatic mt protein levels. In the process, the authors shed light on the dynamics of the events following Fzo1 depletion, revealing dramatically fast mt fragmentation and a loss of MMP, which in turn can be expected to act as a stress signal and influence a number of cellular processes.

The findings of the study can have relevance for human conditions involving disrupted mitochondrial dynamics, caused for example by mutations in mitofusins. The study will be of interest to researchers in mitochondrial biology ranging from dynamics and mtDNA maintenance to mitochondrial medicine.

The field of expertise of this reviewer: mtDNA maintenance. I am not able to properly evaluate the modelling in Fig. 7.

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Reply to the reviewers

Response to the reviewers

We thank the reviewers for recognizing the importance of study, and how it “addresses a long-standing question in the heterogeneity of cellular responses to stressors”, “makes a conceptual advance by identifying transcription factors as the limiting determinant of IFN-β induction in KSHV-infected cells”, and “serves as a crucial starting point for understanding cellular heterogeneity”. We agree that our findings appeal to a broad audience interested in virology, immunology, cell biology, and gene transcription.

We also thank the reviewers for their insightful suggestions that will greatly strengthen our study. Below we detail how we plan to address their comments experimentally and how we have already edited the text to respond to them.

Referee #1

One experiment that may provide some insight into the selective RelA activation is to quantify viral genomes within the high and low IFN producing cells. Perhaps, the genome as a PAMP, is more abundant in the inducing cells.

We have added a note in the Discussion section (line 417) that we have evidence that the cGAS PAMP in our system is mitochondrial DNA, not viral DNA. Moreover, our results suggest that the variation in PAMP levels are not the source of heterogeneity, as this would cause heterogeneous activation of the cGAS-STING-TBK1-IRF3 axis. Instead, we have discovered that TBK1 and IRF3 are activated even in cells without interferon-β induction.

Referee #2

1) While the study presents intriguing evidence for AP-1 involvement in regulating IFN-β responses, the reliance on total c-Jun levels as a readout is limiting. Because c-Jun activity depends on phosphorylation and promoter binding, additional experiments (i.e., phospho-c-Jun analysis or ChIP at the IFNB1 promoter) would strengthen the link between AP-1 activity and the observed reporter outcomes.

We agree that that a stronger link between AP-1 activity and IFN induction would improve our study, so we have cloned interferon-β reporter constructs that contain mutations in the AP-1 binding sites. We plan to use this reporter, as well as IFN-β reporter constructs that contain mutations in either the AP-1, IRF3, or NF-κB binding sites, to mechanistically test the connection between AP-1 and activation of the IFN promoter. As a control, we will test that the mutations block reporter induction after stimulation with a well characterized agonist of the IFN induction pathway such as poly(I:C). We have previously investigated c-Jun and ATF2 phosphorylation during KSHV reactivation and caspase inhibition. Surprisingly, in preliminary experiments we did not detect phosphorylation of either AP-1 subunit. We will confirm this result and add these data to the manuscript.

2) The data presented demonstrating that Serine 386 phosphorylation does not distinguish first responder cells is strong. Including complementary data on Ser396 phosphorylation would strengthen the conclusion, as this well-established activation marker is readily detectable with available reagents and would help confirm that the potentiation of IRF3 activity is not the driver of the observed heterogeneity.

We will complement the Ser386 results with Ser396 staining.

3) Consider updating the title to more directly reflect the findings (e.g. "Interferon-β induction heterogeneity during KSHV infection is correlated to expression of ATF2 and RelA")

We have updated the title to “Interferon-β induction heterogeneity during KSHV infection is correlated to levels and activation of the transcription factors ATF2 and RelA, and not IRF3”

*4) To ease the interpretation of data, indicate what the black and white circles indicate in the figure legends. *

We have updated the figures to be more intuitive, using + and -.

5) IE ORF50 is used to show no differences between first responders and non-responders, but showing early and late genes across tdTomato positive and negative cells would rule out potential differences in progression through reactivation.

We added a clarification in the Results section (line 195), explaining that we have examined the progression of viral reactivation through single-cell transcriptomics in our previous publication, and that the results indicate that viral gene expression plays a small role in interferon-β heterogeneity. We favor the scRNA-seq dataset for this conclusion, because the tdTomato negative cell population represents a mix of non-reactivating cells, which would not be expected to make IFN, and reactivating cells that fail to induce IFN expression.

6) The data in Figure 5D (quantified in E and F) show a compelling trend. This could be further clarified by plotting a trend line that connects the results of independent experiments, rather than only showing individual data points. Such visualization would make the consistency of the observed trend across experiments more apparent.

We have added lines in the graphs in Figure 5 to ease visualization.

Referee #3

A major worry comes from using lentiviral transduction to insert the reporter promoter into cells without selecting for clones. Lentiviral transduction introduces heterogeneity due to random insertion of their vector. This results in different copy numbers for the reporter construct, leading to heterogeneity in the reporter expression. Additionally, the expression of foreign proteins, particularly in immune cells, can be perceived as danger signals (10.1007/s12015-016-9670-8) and occasionally trigger p65 activation. To control for this, the authors could validate their reporter results by including a non-IFNb promoter (e.g., constitutive) expressing tdTomato and verifying that these cell populations do not also express endogenous IFNb mRNAs.

We did not select clonal cell lines because different cells may have different reactivation propensity. Moreover, we did not want the tdTomato signal to reflect specific regulation of a single genomic region. We have now added an explanation as to why we did not clonally select that cell lines in the Results section (line 157). Our control conditions that do not result in IFN-β induction show that lentiviral insertion is not sufficient to cause IFN induction, as we did not detect IFN-β mRNA in the untreated reporter cells (first bar in Figure 1C). We also clarified in the Results section (line 184) that the selective enrichment of both IFN-β and tdTomato mRNA in the sorted tdTomato+ cells demonstrates that tdTomato is a faithful reporter for rare IFN-β expression, regardless of heterogeneous lentiviral transduction in the population. To further verify that lentiviral transduction does not play a role in introducing heterogeneity in induction of our tdTomato reporter and of IFN-β, we will measure IFN-β levels in BC-3 cells constitutively expressing tdTomato, which we have already created. We may also sort BC-3 cells constitutively expressing tdTomato and check that the tdTomato signal is not predictive of IFN expression in these cells. However, the expectation is that all or most cells will be tdTomato positive, which may make sorting for tdTomato negative cells impossible.

Regarding AP1 and NF-kB activation, the authors could investigate downstream genes such as GADD45B, HSPA1A, and ATF-3 (for AP1), and IL-6, TNFAIP3 (A20) (for both AP1 and NFkB). It would be interesting to determine if these genes are exclusively expressed in tdTomato-expressing cells.

We will quantify the mRNA levels of these genes by performing qPCR on our cDNA from sort experiments. So far, we have detected IL-6 induction but no enrichment of this transcript in the sorted tdTomato+ samples.

While the authors observed no direct correlation between c-Jun alone and IFN-b production, it is conceivable that TPA-induced c-Jun primes the cells that become fully transcriptionally active upon a stimulus like viral reactivation. I propose that the authors attempt to inhibit c-Jun activation during KSHV reactivation (TPA + caspase inhibitor) using inhibitors like SP600125 and subsequently assess whether this blockade reduces the proportion of IFNb+ cells.

We have tried using the suggested inhibitor (SP600125), but found that it inhibits KSHV reactivation, making any result on IFN levels difficult to interpret. Currently, we are testing a dual AP-1 and NF-κB inhibitor (SP100030) and may add these data to the results if we do not encounter similar issues.

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Referee #3

Evidence, reproducibility and clarity

Summary

Kaku and Gaglia's study provides one step further in the ongoing debate surrounding viral versus innate immune heterogeneity. They addressed this question by creating a reporter B cell line (BC-3) that expresses tdTomato under the IFNb promoter. This particular cell line is known to be latently infected with KSHV, and lytic infection can be induced by treatment with the protein kinase C activator TPA.

Through FACS sorting upon KSHV lytic infection, the authors observed a correlation between the promoter reporter activation and endogenous IFNb and IFNl mRNA levels. However, this correlation did not extend to viral replication, indicating that only a fraction of virus-infected cells produce IFN. They identified these cells as "first responders" upon viral replication by treating them with anti-IFNAR, confirming that IFN production is triggered by the cGAS-STING pathway sensing lytic virus infection.

Surprisingly, p-IRF3 activation was not limited to IFN-producing cells, suggesting the involvement of other key transcription factors. Indeed, they found a correlation between NF-kB and AP1 activation and IFN production. The study concludes that the combined action of NF-kB, AP1, and IRF3 is crucial for robust IFN production.

Major comment

The author effectively dissects the necessary components for IFNb activation, despite acknowledging the limitations of their findings. All my potential anecdotal queries, such as the role of other viruses or agonists and the treatment of cells with NF-kB inhibitors, are thoroughly addressed in their discussion.

However, a major worry comes from using lentiviral transduction to insert the reporter promoter into cells without selecting for clones. Lentiviral transduction introduces heterogeneity due to random insertion of their vector. This results in different copy numbers for the reporter construct, leading to heterogeneity in the reporter expression. Additionally, the expression of foreign proteins, particularly in immune cells, can be perceived as danger signals (10.1007/s12015-016-9670-8) and occasionally trigger p65 activation. To control for this, the authors could validate their reporter results by including a non-IFNb promoter (e.g., constitutive) expressing tdTomato and verifying that these cell populations do not also express endogenous IFNb mRNAs.

Minor comments

Regarding AP1 and NF-kB activation, the authors could investigate downstream genes such as GADD45B, HSPA1A, and ATF-3 (for AP1), and IL-6, TNFAIP3 (A20) (for both AP1 and NFkB). It would be interesting to determine if these genes are exclusively expressed in tdTomato-expressing cells.

While the authors observed no direct correlation between c-Jun alone and IFN-b production, it is conceivable that TPA-induced c-Jun primes the cells that become fully transcriptionally active upon a stimulus like viral reactivation. I propose that the authors attempt to inhibit c-Jun activation during KSHV reactivation (TPA + caspase inhibitor) using inhibitors like SP600125 and subsequently assess whether this blockade reduces the proportion of IFNb+ cells.

Significance

The study presents a valuable dataset and serves as a crucial starting point for understanding cellular heterogeneity, particularly regarding the known concept of IRF+NFkB in IFNb production. While this mechanism isn't novel (10.1074/jbc.273.5.2714), the authors demonstrated the difference in activation in a cellular level. This finding can be the basis of future research utilizing more physiologically relevant models, such as primary cells or tissues, to identify factors contributing to varying cellular responses.

However, the authors acknowledge that these findings should be interpreted with caution and require further validation through additional studies across different models and viral infections. This research will be particularly relevant to those in basic research seeking to deepen their understanding of the dynamic differences in innate immune responses and viral infections.

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Referee #2

Evidence, reproducibility and clarity

In the manuscript "Interferon-β induction heterogeneity during KSHV infection is correlated to expression and activation of enhanceosome transcription factors other than IRF3", Kaku and Gaglia address a long-standing question in the initiation of host antiviral responses: what drives the heterogeneity in the initiation of IFN responses within a presumably homogenous population of cells. In this study, the authors focus on host factors that contribute to the heterogeneity in IFN induction. They use a KSHV lytic reactivation model (TPA + Caspase inhibitor treated BC-3 cells) and FACS-based reporter assays to enhance the resolution in the detection of molecular drivers of "first responder" cells that make IFN. They find that IRF3 activation alone does not predict IFN expression; rather, the expression of ATF2 and RelA is predictive of IFN-β induction. The authors carefully control for off-target effects of TPA treatment in BJAB cells and paracrine signaling through the inclusion of IFN-neutralizing antibodies. Overall, the manuscript is well-written and easy to follow, and the data compellingly support their conclusion that cell-specific transcription factor activity limits IFN production to cell subsets. Demonstrating coordinated occupancy or functional interplay of these factors would increase confidence in the proposed model and broaden the impact for readers interested in virology, immunology, and transcriptional regulation.

Comments:

1. While the study presents intriguing evidence for AP-1 involvement in regulating IFN-β responses, the reliance on total c-Jun levels as a readout is limiting. Because c-Jun activity depends on phosphorylation and promoter binding, additional experiments (i.e., phospho-c-Jun analysis or ChIP at the IFNB1 promoter) would strengthen the link between AP-1 activity and the observed reporter outcomes.
2. The data presented demonstrating that Serine 386 phosphorylation does not distinguish first responder cells is strong. Including complementary data on Ser396 phosphorylation would strengthen the conclusion, as this well-established activation marker is readily detectable with available reagents and would help confirm that the potentiation of IRF3 activity is not the driver of the observed heterogeneity.

Minor Comments:

1. Consider updating the title to more directly reflect the findings (e.g. "Interferon-β induction heterogeneity during KSHV infection is correlated to expression of ATF2 and RelA".
2. To ease the interpretation of data, indicate what the black and white circles indicate in the figure legends.
3. The authors predominantly rely on the IE gene ORF50 as a marker of KSHV reactivation and show no differences in expression between first responder cells and those that don't. Measurement of early and late genes across TdTomato-positive and negative cells would rule out potential differences in progression through reactivation that might influence IFN production.
4. The data in Figure 5D (quantified in E and F) show a compelling trend. This could be further clarified by plotting a trend line that connects the results of independent experiments, rather than only showing individual data points. Such visualization would make the consistency of the observed trend across experiments more apparent.

Significance

This study addresses an important and long-stading question in the heterogeneity of cellular responses to stressors, such as viruses. The study is well designed and presented, making it appealling to a broad audience interested in virology, immunology, cell biology, and gene transcription.

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Referee #1

Evidence, reproducibility and clarity

The manuscript discusses why only a small proportion of KSHV infected cells produce high level of IFN during lytic reactivation in the presence of caspase inhibition, highlighting cellular heterogeneity as a key factor in innate immune regulation in KSHV infection. Using a dt-TOMATO reporter fused to the IFN promoter, the author generated a stable cell line in BC3 cells (a primary effusion lymphoma line). The authors observed that while IRF3 and TBK1 were activated in nearly all infected cells, only those with both high baseline levels of the AP-1 component ATF2 and activated NF-κB (phosphorylated RelA) produced robust FN. These findings suggest that AP-1 and NF-B, rather than IRF3, are the limiting factors for IFN induction in individual cells.

Overall the findings are interesting and important. While there remain many unknowns, such as why RelA is activated in only a subset of cells, this manuscript takes us one step close to determining how IFN is ultimately induced in KSHV infection.

One experiment that may provide some insight into the selective RelA activation is to quantify viral genomes within the high and low IFN producing cells. Perhaps, the genome as a PAMP, is more abundant in the inducing cells.

Significance

The study makes a conceptual advance by identifying transcription factors as the limiting determinant of IFN-β induction in KSHV-infected cells, highlighting how innate immune responses are regulated during herpesvirus infection and how the regulation influences viral persistence and immune evasion.

The above findings will be of important to researchers studying herpesvirus biology, innate immunity (IFN signaling), and host-pathogen interaction.

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Reply to the reviewers

We thank the editor and the reviewers for their positive and constructive comments. Below is our point-by-point responses.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Metabolic dysfunction-associated steatotic liver disease (MASLD) ranges from simple steatosis, steatohepatitis, fibrosis/cirrhosis, and hepatocellular carcinoma. In the current study, the authors aimed to determine the early molecular signatures differentiating patients with MASLD associated fibrosis from those patients with early MASLD but no symptoms. The authors recruited 109 obese individuals before bariatric surgery. They separated the cohorts as no MASLD (without histological abnormalities) and MASLD. The liver samples were then subjected to transcriptomic and metabolomic analysis. The serum samples were subjected to metabolomic analysis. The authors identified dysregulated lipid metabolism, including glyceride lipids, in the liver samples of MASLD patients compared to the no MASLD ones. Circulating metabolomic changes in lipid profiles slightly correlated with MASLD, possibly due to the no MASLD samples derived from obese patients. Several genes involved in lipid droplet formation were also found elevated in MASLD patients. Besides, elevated levels of amino acids, which are possibly related to collagen synthesis, were observed in MASLD patients. Several antioxidant metabolites were increased in MASLD patients. Furthermore, dysregulated genes involved in mitochondrial function and autophagy were identified in MASLD patients, likely linking oxidative stress to MASLD progression. The authors then determined the representative gene signatures in the development of fibrosis by comparing this cohort with the other two published cohorts. Top enriched pathways in fibrotic patients included GTPase signaling and innate immune responses, suggesting the involvement of GTPase in MASLD progression to fibrosis. The authors then challenged human patient derived 3D spheroid system with a dual PPARa/d agonist and found that this treatment restored the expression levels of GTPase-related genes in MASLD 3D spheroids. In conclusion, the authors suggested the involvement of upregulated GTPase-related genes during fibrosis initiation. Overall, the current study might provide some resources regarding transcriptomic and metabolomic data derived from obese patients with and without MASLD. However, several concerns should be carefully addressed.

1. A recent study, via proteomic and transcriptomic analysis, revealed that four proteins (ADAMTSL2, AKR1B10, CFHR4 and TREM2) could be used to identify MASLD patients at risk of steatohepatitis (PMID: 37037945). It is not clear why the authors did not include this study in their comparison. Thank you for the suggestion. The RNA sequencing dataset (GSE135251) from study PMID 37037945 is the same dataset we used as an external benchmark in our study, referred to as the EU cohort on page 4 in the manuscript. In addition to PMID 37037945, we have cited the original transcriptomic study (PMID 33268509) for the EU cohort. In the revised manuscript, we discussed this proteome-transcriptome paper in the Discussion section and highlighted the potential of AKR1B10 as a biomarker in early MASLD.

The authors recruited 109 patients but only performed transcriptomic and metabolomic analysis in 94 liver samples. Why did the authors exclude other samples?

We thank the reviewer for their question and we understand the confusion. The discrepancy in sample size between liver and plasma cohorts is due to the fact that, for certain cases, we were unable to get sufficient liver tissue slices (“Exclusion criteria included: age The authors mentioned clinical data in Table 1 but did not present the table in this manuscript.

Table 1 (key patient characteristics) was included in the main document after the Methods section, and Table S1 (additional patient characteristics) was provided as a supplemental file in our original submission.

The generated metabolomic data could be a very useful resource to the MASLD community. However, it is very confusing how the data was generated in those supplemental tables. There is no clear labeling of human clinical information in those tables. Also, what do those values mean in columns 47-154? This reviewer assumed that they are the raw data of metabolomic analysis in plasma samples. However, without clear clinical information in these patients, it is impossible that any scientist can use the data to reproduce the authors' findings.

We appreciate this suggestion. To ensure accessibility of the data resources, we created a GitHub repository for both data and code, available at https://github.com/SLINGhub/MASLD_dual_omics____.

The GitHub repository includes clinical data for all 109 participants with patient characteristics and histological gradings, as well as processed omics data (log₂-transformed). We have generated artificial IDs for each patient so that we can include all the requested data in an organized manner. A code template is also provided to replicate the main statistical results from this study. In addition, for readers interested in conducting analyses from the raw data, we have deposited the raw sequencing files and mass spectrometry data in GEO and Zenodo, as detailed in the ‘Data Availability’ section.

In Fig. 5B, the authors excluded the steatosis and fibrosis overlapped genes. Steatosis and fibrosis specific genes could simply reflect the outcomes rather than causes. In this case, the obtained results might not identify the gene signatures related to fibrosis initiation.

We appreciate this comment, but we do not fully understand the reviewer’s point since we did not exclude overlapped genes in our analysis, and it was unclear to us whether excluding overlapping genes has anything to do with causality of both processes.

In Figure 5B, we identified the gene signatures associated with steatosis and fibrosis after adjusting for potential confounders such as age, sex, BMI and diabetes status. Our results showed that these signatures were relatively independent, sharing a limited number of genes. We then examined genes uniquely associated with each process by additional adjustment (e.g., adjusting steatosis models for fibrosis grades). To us this was not an unreasonable approach, given that steatosis precedes fibrosis in most cases, especially in morbid obesity.

We nevertheless agree with the reviewer’s point that the gene expression changes we identified represent statistical associations without warranting causality. To specifically address fibrosis initiation mechanisms within the limitation of the current study design, we performed a separate comparative analysis between patients with fibrosis+steatosis versus those with steatosis alone (Table S11), which still identified GTPase regulation as a potential key mechanism in fibrosis initiation (Figure 6B).

In Fig. 6D, the authors used 3D liver spheroid to validate their findings. However, there is no images showing the 3D liver spheroid formation before and after PPARa/d agonist treatment. It is not clear whether the 3D liver spheroid was successfully established.

There is extensive literature (>40 papers) from the Lauschke lab on 3D liver spheroid culture, including but not limited to PMIDs 27143246, 28264975, 32775153, 37870288 and 39605182. Images of the spheroids can be seen in Figure 1c of Adv. Sci. 2024, 2407572 and elafibrinor treatment did not affect the morphology of the spheroids.

The authors suggested that targeting LX-2 cells with Rac1 and Cdc42 inhibitors could reduce collagen production. Did the authors observe these two genes upregulated in mRNA and protein expression levels in their cohort when compared MASLD patients with and without fibrosis? Did the authors observe that the expression levels of Rac1 and Cdc42 are correlated with fibrosis progression in MASLD patients?

Regarding comments 7 and 8, we targeted Rac1 and Cdc42 in the LX-2 cell experiment as they are common and major GTPases. Protein-level data are not available in our dataset, but we examined their transcript-level expression. RAC1 and CDC42 expression levels were positively associated with fibrosis progression, with coefficients of 0.362 (q = 0.027) and 0.342 (q = 0.031), respectively. These results are presented in Table S5, and the corresponding boxplots are shown here.

Figure R1. RAC1 and CDC42 expression levels in individuals with different fibrosis *levels. *

Other studies have revealed several metabolite changes related to MASLD progression (PMID: 35434590, PMID: 22364559). However, the authors did not discuss the discrepancies between their findings with the previous studies.

Thank you for the suggestion. We have incorporated a discussion of the two studies into the Discussion section, highlighting the consistencies and discrepancies between our plasma metabolomic results and previous findings. The main differences may stem from variations in MASLD spectrum and the degree of obesity in the cohorts.

Reviewer #1 (Significance (Required)):

Overall, the current study might provide some new resources regarding transcriptomic and metabolomic data derived from obese patients with and without MASLD. The MASLD research community will be interested in the resource data.

We thank this reviewer for the positive and constructive evaluation of our manuscript.

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

Summary:

In this paper, Kaldis and collaborators investigate the molecular heterogeneity of a 109 morbidly obese patient cohort, focusing on liver transcriptomics and metabolomics analysis from liver and serum. The main finding (i.e. upregulation of GTPase-coding genes) was validated in spheroids and a human HSC cell line. As these proteins are involved in critical cellular functions related to metabolism and cytoskeleton dynamics, these findings shed light on their involvement in human liver pathology which so far has been poorly (or even not) documented to date. This is an interesting addition to the current knowledge about chronic liver pathology. However the manuscript suffers from the lack of a clear-cut definition of patient subgroups and the seemingly indistinct use of generic (MASLD, NAS score) and more granular terms (MASH, fibrosis) across the various analysis they performed.

We thank this reviewer of highlighting the novelty of our manuscript. We agree that mixing generic and granular terms can be confusing and we tried to use of terms consistently throughout, which has been further improved in the revised version.

Figure 1 and Table 1 provide comprehensive information regarding histological phenotypes, NAS scores, and patient characteristics. From Figure 2 onward, we specifically focused on steatosis and fibrosis as distinct histological features, identifying molecular signatures associated with each process.

The term ‘MASH’ was used only when referring to the ex vivo 3D spheroids derived from histologically confirmed MASH patients for validation purposes. As our primary cohort represents early disease stages, we did not characterize molecular features of MASH in that data set.

In this cohort, the term 'NAS' was mentioned only in Section 1 to characterize the disease spectrum. Additionally, in Figures 3A and 6A, we illustrated the association between gene expression levels and NAS in two external cohorts. This was due to the absence of steatosis grades in the two datasets. NAS is an additive measure of multiple scores (steatosis, inflammation and ballooning), but does not account for fibrosis grades.

Our study focuses on the molecular features of steatosis grades and fibrosis grades as the main histological processes, with all terminology aligned with this stated objective. This allows us to map the transcriptome and metabolome to pathologist-defined steatosis/fibrosis severity (i.e., 0,1,2,3) and identify genes/metabolites that are correlated with increasing steatosis/fibrosis score.

Major comments:

• Are the key conclusions convincing?

The conclusions are generally consistent with findings from numerous previous studies, as many of the genes identified and their associations with disease states have been previously reported. However, I found it difficult to discern which specific disease stages the authors are referring to throughout the manuscript. Terms such as MASLD (Fig. 1F), steatosis (Fig. 4A), MASH, fibrosis (Fig. 6), and the composite NAS score (Fig. 1G) are used interchangeably, without clearly explaining whether or how the patient cohort was stratified to distinguish between isolated steatosis, MASH, and MASH with or without fibrosis. It is also unclear whether subgroups were propensity score-matched.

As explained in our previous point, we believe that we did not carelessly use the terms interchangeably, but rather used them as they were available or pertinent to the comparisons in discussion. We have provided a comprehensive cohort description in the first section (Table 1, including all histological features and NAS scores), then focused specifically on steatosis and fibrosis in subsequent analyses. We identified distinct molecular processes underlying these two histological features and validated key fibrosis-related pathways.

Regarding the comment of ‘propensity score-matched subgroups’, we would like to clarify that the only “sub”-group analysis performed in this paper is the transition from steatosis to steatosis with fibrosis. We have consistently used linear regression as the association analysis framework, without binarization of outcomes. We recall that this is a cross-sectional study with challenging recruitment situation from a bariatric surgery clinic that naturally represents the spectrum of MASLD in obesity. We acknowledge that the sampling can always be biased in such a study. However, given the invasiveness of liver resection, the study is also limited by the reality that not all patients would agree to the study, nor it is feasible to form a perfect subgroup meeting 1:1 ratio as in large-scale epidemiology studies based on plasma samples.

In a related point, the authors mention that 76% of patients are non-fibrotic, introducing a marked imbalance between fibrotic (n=26) and non-fibrotic (n=83) samples. Given this disparity and potential inter-individual variability, it would be helpful to include observed fold changes or effect sizes to give readers a sense of the magnitude of the biological dysregulations being reported.

As explained in our previous response, our study design examines associations between histological and molecular features rather than using a case-control approach. For effect size quantification, we report standardized linear regression coefficients, i.e. the change in gene expression Z-score per one-point increase in steatosis or fibrosis grade. We also provided fold changes in our comparative analysis of steatosis+fibrosis versus fibrosis-free steatosis. These effect sizes were fully documented in the Supplemental Tables.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

• The authors seem pretty enthusiastic about elafibranor, despite a failed phase 3 clinical trial. I would qualify elafibranor as a useful tool in preclinical model. We agree with the reviewer and indeed used elafibranor as a research tool for PPARa/d modulation rather than a clinically promising prospect. Discussion regarding elafibranor has been updated.

• The authors should make clearly the pronounced sex bias in their study, which includes mostly women (and btw refer to sex and not gender in the manuscript). Thank you for this important point. We added "Notably, the cohort was predominantly female (76.1%)" to the 'Overview of the study' section in the manuscript. We also replaced all 'gender' with 'sex' throughout the manuscript. In this cohorts, individuals with previous gender reassignment were excluded (see Materials and Methods).

• The "MASH" status of the spheroid model is overstated. As described in the text it is much closer to a lipotoxicity model (and even glucotoxicity as Glc concentration is 2g/L). The 3D cultures were established from cells isolated from patients with histologically confirmed MASH. Besides steatosis, we observe increased secretion of pro-inflammatory cytokines, activation of hepatic stellate cells and increased deposition of collagen, thus phenocopying the critical disease hallmarks. Additionally, unbiased omics profiling (transcriptomics, proteomics and lipidomics) reveals significant increases in collagen biosynthesis, inflammatory signaling and cholesterol biosynthesis in MASH patient-derived cultures compared to controls. These differences largely overlapped with the results from analyses of six MASH case-control cohort studies. All of these results have been published previously (PMID 39605182).

This is confusing with panel D in which the authors establish a relationship between fibrotic patients (F2/F3 vs F0/S0, so I guess "no MASLD liver?) and this model. Is the relationship maintained for steatotic-only patients?

In Figure 6D, we compared GTPase-related gene expression between patients with fibrosis grade 2/3 (n = 26) and those without fibrosis and steatosis (n = 24). Principal component regression resulted in a positive correlation (β = 9.97) between log2 fold changes in 3D spheroids and human fibrosis samples, indicating consistent directional changes in both systems.

To answer the question from the reviewer, we compared the expression levels of GTPase-related genes in patients with steatosis but no fibrosis (n = 18) to those without fibrosis and steatosis (n = 24), we observed a negative correlation (β = -10.91). This indicates that GTPase-related gene changes in our 3D spheroids do not align with steatosis-related changes in humans.

Therefore, under the assumption that fibrosis follows steatosis in the majority of the cases of MASLD progression, the result indicates that the alterations in GTPase-related gene expression in the 3D spheroid model specifically is reflective of fibrosis rather than steatosis.

Figure R2. Comparison of expression level changes in GTPase-related genes between this human cohort and an independent 3D spheroid system: (A) positive correlation with fibrosis grade 2/3 patients versus controls (left), and (B) negative correlation with steatosis-only patients versus controls (right).

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

I am not convinced that HSC and LX2 cells express significant levels of PPARα. However, did the authors check for this parameter in their LX2 cell line and assessed whether PPARα/b activation by elafibranor (and/or pemafibrate as it is PPARα selective) alter GTPase expression? Whether negative or positive, this could give a clue about possible intercellular crosstalk in the spheroid model.

We thank this reviewer to point this out. In response, we analysed the mRNA expression of all PPARs in LX-2 cells with and without Elafibranor treatment, respectively (see Figure R3, same as Figure S8G in the Supplemental Material). We confirmed PPARs are expressed in LX-2 cells at the mRNA level (Figure R3A). Elafibranor does not affect their mRNA levels, which is consistent with previous reports that its primary mechanism is through binding and altering the activity of PPAR proteins, not gene expression (PMID 33326461 and PMID 37627519).

*Figure R3. Gene signatures in LX-2 cells with and without Elafibranor treatment (n = 3). *

In addition, we assessed mRNA levels of selected GTPase-related genes in LX-2 cells with and without Elafibranor treatment (Figure R3B). Although statistical power was limited, we observed a consistent trend toward reduced RHOU, DOCK2, and RAC1 expression with Elafibranor. this preliminary signal suggests that Elafibranor may counter the elevated GTPase levels seen in MASH patient spheroids, potentially via crosstalk among hepatic cell types, including HSCs.

To further investigate intercellular crosstalk in GTPase regulation among hepatic cell types, we evaluated signature GTPase-related genes in LX-2 cells, spheroid co-cultures (hepatocytes, HSCs, Kupffer cells), and hepatocyte monocultures. As shown in Figure R4 (same as Figure S10 in the supplemental material), TGFB1 served as a positive control, exhibiting the most pronounced induction upon TGF-β1 treatment in hepatocytes. Despite varied alterations across the selected GTPase-related genes, TGF-β1 treatment produced a trend toward increased VAV1 and DOCK2 expression in co-culture, hepatocytes, and LX-2 cells, and this was reversed by the TGF-β inhibitor in co-culture and hepatocytes. Other GTPase genes, including RAC1, RAB32, and RHOU, displayed cell type–specific responses to TGF-β1. These observations suggest that the regulation of GTPases is mediated by multiple hepatic cell types, supporting the importance of intercellular crosstalk.

Figure R4. Expression of GTPase-related genes in spheroid co-culture, hepatocyte monoculture, and LX-2 cells (n = 3). Controls for each gene and experiment were normalized to 1 to enable comparison across treatment groups.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

The experiment mentioned above is cheap (cell culture, RT-QPCR) and can be performed within a couple of weeks.

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

• Are the experiments adequately replicated and statistical analysis adequate? There is no indication of group size, number of replicates for in vitro experiments

Thank you for this suggestion. We have added the sample sizes to all relevant sections: ‘n = 4’ in the figure legends for 3D spheroid experiments and ‘n = 8–10’ for the LX-2 experiments. This information has also been incorporated into the corresponding experimental descriptions in the Methods section.

**Referees cross-commenting**

I believe there is a general consensus on this potentially interesting contribution to the field, with three main points: (1) the need for a careful group-by-group comparison that accounts for potential confounders, (2) a more rigorous exploitation/characterization of the spheroid system, and (3) the need to benchmark the authors' findings against the available literature.

Thank you for summarizing the main points. Our responses are as follows:

• We adjusted for key confounders (sex, gender, age, BMI, diabetes) in all statistical analysis to minimize potential bias, mostly using linear regression (rather than group-to-group comparison). In response to Reviewer 3, comment 1, we also conducted additional statistical analyses exploring molecular changes in diabetic vs. non-diabetic individuals.
• We provided detailed characterization of the spheroid model (response to Reviewer 3, comment 3) and we have done additional experiments in LX-2 cells.
• We benchmarked our findings using external human cohorts, mouse models, and single cell spheroid systems:
• Compared our liver transcriptomics data with two published liver RNA-seq datasets (EU cohort, PMID 31467298; VA cohort, PMID 33268509) as shown in Figure 1G. In Figures 3A and 6A, we also included sidebars indicating gene alterations in these cohorts, showing consistent trends. Moreover, we examined the expression alterations of GTPase-related genes in these datasets in response to Reviewer 3’s comment 2.
• Assessed genes linked to fibrosis progression in hepatic stellate cells from a murine liver fibrosis model (PMID 34839349), confirming differential expression of GTPases and their regulators during fibrosis initiation (Figure S9A).
• Examined GTPase-related genes in an independent single-cell human spheroid system (PMID 37962490). This enabled cell-type-specific information of GTPase regulation in response to TGF-β (Figure S9C). We also expanded the discussion section on both the consistencies and discrepancies between our findings and previously published studies.

Reviewer #2 (Significance (Required)):

The authors identified GTPases as players in the progression of MASLD. This is an interesting preliminary report warranting further molecular investigations (in which liver cell types, which GTPase pathway(s) are involved, which functions are controlled through this pathway...)

• State what audience might be interested in and influenced by the reported findings.

This paper will have an impact in the hepatology field

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I have expertise in the analysis of "MASLD" human cohorts and in the molecular biology of chronic liver diseases.

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

Summary:

Metabolic dysfunction associated liver disease (MASLD) describes a spectrum of progressive liver pathologies linked to life style-associated metabolic alterations (such as increased body weight and elevated blood sugar levels), reaching from steatosis over steatohepatitis to fibrosis and finally end stage complications, such as liver failure and hepatocellular carcinoma. Treatment options for MASLD include diet adjustments, weight loss, and the receptor-β (THR-β) agonist resmetirom, but remain limited at this stage, motivating further studies to elucidate molecular disease mechanisms to identify novel therapeutic targets. In their present study, the authors aim to identify early molecular changes in MASLD linked to obesity. To this end, they study a cohort of 109 obese individuals with no or early-stage MASLD combining measurements from two anatomic sides: 1. bulk RNA-sequencing and metabolomics of liver biopsies, and 2. metabolomics from patient blood. Their major finding is that GTPase-related genes are transcriptionally altered in livers of individuals with steatosis with fibrosis compared to steatosis without fibrosis.

Major comments:

1. Confounders (such as (pre-)diabetes) The patient table shows significant differences in non-MASLD vs. MASLD individuals, with the latter suffering more often from diabetes or hypertriglyceridemia.

Rather than just stating corrections, subgroup analyses should be performed (accompanied with designated statistical power analyses) to infer the degree to which these conditions contribute to the observations. I.e., major findings stating MASLD-associated changes should hold true in the subgroup of MASLD patients without diabetes/of female sex and so forth (testing for each of the significant differences between groups).

Our original statistical analysis employed linear regression to examine associations between molecular variables (genes/metabolites) and histological progression (steatosis and fibrosis), with adjustment for potential confounders including diabetic status, age, sex, and BMI. We specifically focused on these two histological features to elucidate the disturbed molecular processes during their progression. Regression coefficients represent the expected change in abundance levels (in units of standard deviation of the corresponding molecule) per one-unit increase in histological grades.

To address the reviewer's question, we conducted additional subgroup analyses to determine whether our major findings remain consistent in individuals with and without diabetes. We assessed linear associations between gene signatures and histological features separately in non-diabetic (n = 71) and diabetic individuals (n = 23). Statistical power was estimated by comparing the variance explained by the full regression model (y ~ x + a + b + c) against the reduced model (y ~ a + b + c), converting the incremental R² for x into Cohen's f², and applying pwr.f2.test with the corresponding degrees of freedom and sample size at α = 0.05.

For both steatosis and fibrosis, the results in the non-diabetic subgroup (n = 71) showed high consistency with findings in our original analysis (n = 94, adjusted for diabetes), indicating that our originally reported gene signatures, after correction for diabetic status, remain valid in non-diabetic individuals.

In contrast, for diabetic individuals (n = 23), associations between genes and histological features did not closely replicate our original findings. Notably, we observed larger estimate effects for fibrosis-associated genes in diabetic individuals, suggesting a potential interaction between diabetes and fibrosis progression.

Figure R5. Subgroup analysis of the association between gene expressions and steatosis grades

Figure R6. Subgroup analysis of the association between gene expressions and fibrosis grades

On the comment "degree to which these conditions contribute to the observations," our original analysis adjusted for diabetes status to identify molecular signatures independently associated with fibrosis without the confounding of diabetes status. Consequently, the reported gene signatures in the original analysis more closely reflect patterns in the non-diabetes group, as demonstrated in our subgroup analysis plots. We also comment that, unfortunately, we did not adjust for the interaction of fibrosis and diabetes in the original analysis.

Furthermore, our additional analyses revealed a close relationship between diabetes and liver fibrosis. Consistent with Figure 1C, hepatic fibrosis is significantly correlated with insulin resistance parameters in clinical assays, including blood insulin levels and HOMA2-IR. To explore this association further, we compared gene expression profiles between diabetic MASLD patients (n = 21) and non-diabetic MASLD patients (n = 43). Although few genes reached significance after multiple testing correction, 166 genes showed differential expression (p 0.32) between these groups.

We identified 55 genes as potential "diabetic markers" that both showed differential expression between diabetic and non-diabetic MASLD patients and were significantly associated with steatosis or fibrosis progression. These genes are predominantly downregulated metabolic genes (e.g., BAAT, G6PC1, SULT2A1, MAT1A), suggesting that diabetes may exacerbate metabolic suppression as fibrosis advances. Given the high prevalence of diabetes in the MASLD population, our analysis supports the hypothesis that diabetes worsens MASLD outcomes, likely through impaired metabolic capability during fibrosis progression.

Regarding the comment on the "subgroup of female sex," our original analysis also adjusted for sex as a potential confounder. Since our cohort is predominantly female (>76%), the majority of our findings likely holds true in the female sub-population, similar to what we observed in our diabetes subgroup analysis.

External validation

Additionally, to back up the major GTPase signature findings, it would be desirable to analyze an external dataset of (pre)diabetes patients (other biased groups) for alternations in these genes. It would be important to know if this signature also shows in non-MASLD diabetic patients vs. healthy patients or is a feature specific to MASLD. Also, could the matched metabolic data be used to validate metabolite alterations that would be expected under GTPase-associated protein dysregulation?

We appreciate the comments regarding the validation GTPase as a unique MASLD signature by external datasets. As shown in our previous analysis, after adjusting for diabetes status, the gene signatures remained largely preserved in the non-diabetes subgroup. Before we respond further, we also preface that publicly available liver tissue data, with appropriate and full-scale clinical metadata and sufficient sample sizes, are extremely rare. To the best of our knowledge, the public data sets we brought into our paper were the most prominent data of reliable quality.

In the paper, we benchmarked our RNAseq dataset against two datasets: the VA cohort and EU cohort (Figure 1). Our cohort focused primarily on early MASLD patients with obesity, which aligns more closely with the disease spectrum represented in the VA cohort (Figure 1G). Notably, in the published paper for the VA cohort, Hoang et al. highlighted Rho GTPase signaling as one of the top pathways in the fibrosis PPI network (Figure 1B from publication PMID 31467298).

We interrogated GTPase-related genes in both the VA and EU cohorts. As shown in Figure R7 (below), GTPase-related genes demonstrated a strong association with fibrosis grades in the VA cohort, as expected. The EU cohort comprises more advanced MASLD cases with higher fibrosis grades, and our re-analysis in this cohort specifically focused on MASH patients (as designated by the authors). In those MASH patients, GTPase-related genes did not show significant positive associations with fibrosis progression. This finding is consistent with our hypothesis that GTPase regulation is triggered more prominent during the early progression of fibrosis rather than at later stages.

Unfortunately, diabetes status was not available in the GEO repository for the VA cohort. Available liver tissue sequencing datasets with balanced representation of diabetic and nondiabetic patients are rare, especially those derived from obese individuals and reflecting the early-to-middle stages of MASLD. In our own cohort, for instance, only two diabetic patients without MASLD were recruited (Table 1). While we cannot rule out a role for insulin resistance in GTPase regulation, we will plan future experiments using mouse models to examine GTPase-mediated fibrosis under diabetic and nondiabetic conditions.

Regarding the comment ‘validate metabolite alterations that would be expected under GTPase-associated protein dysregulation,’ we note that GTPases are primarily involved in cytoskeletal organization, vesicle trafficking, and other cellular processes, with few well-established links to specific metabolite signatures. Nevertheless, in our partial correlation network integrating hepatic genes and metabolites, we observed co-regulated metabolites associated with GTPase-related genes (Figure R8). These included palmitoleoyl ethanolamide (N-acylethanolamine, an anti-inflammatory metabolite and PPARα ligand), phenylacetic acid (a phenylalanine metabolite), biotin (a coenzyme), arginine, lysine, melatonin (a tryptophan metabolite), and several lipid species such as PC 32:0 and CAR 20:1. While causal relationships cannot be inferred from this dataset, our integrative network highlights potential connections related to the trafficking of these metabolites that warrant further investigation.

Figure R7. Associations between GTPase-related genes to fibrosis in this study and two external cohorts. Asterisks denote significant associations with q value Figure R8. Integrative subnetwork of GTPase-related genes. Blue squares represent GTPase-related genes, red circles indicate metabolites connected to these genes, and the purple diamond denotes fibrosis, which is connected to RHOU.*

3D liver spheroid MASH model, Fig. 6D/E

This 3D experiment is technically not an external validation of GTPase-related genes being involved in MASLD, since patient-derived cells may only retain changes that have happened in vivo. To demonstrate that the GTPase expression signature is specifically invoked by fibrosis the LX-2 set up is more convincing, however, the up-regulation of the GTPase-related genes upon fibrosis induction with TGF-beta, in concordance with the patient data, needs to be shown first (qPCR or RNA-seq).

We agree with the reviewer that experiments in LX-2 (HSC) cells are important and as we have described under ‘Reviewer #2’ we have done this (Figure R3 and Figure R4). Because HSCs only comprise a minor cell population of liver cells, the signals observed in patient bulk RNA data are likely driven primarily by hepatocytes. Nevertheless, we have highlighted the importance of hepatic cell crosstalk in Figure R4 and in our response to Reviewer #2. Additionally, in Supplementary Figure S9B, we identify the potential cell types of origin for the GTPase signals (predominantly hepatocytes and HSCs) using a single-cell dataset from an independent study (PMID: 37962490).

Additionally, the description of the 3D model is too uncritical. The maintenance of functional human PHHs in 3D has only become available this year (PMID: 40240606) marking a break-through in the field. Since the authors did not use this system, I would strongly assume their findings are largely attributable to the mesenchymal cells in the 3D culture, and these limitations need to be stated.

We humbly disagree with the reviewer on the 3D liver spheroids. The paper that the reviewer is referencing is related to the proliferation of hepatocytes in organoids, not – at least not directly – their functional maintenance. Here, we use a spheroid model of mature fully differentiated cells, which is conceptually different from the organoid approach. Maintenance of such functional human hepatocytes for multiple weeks in culture has been possible for close to a decade (PMID 27143246). Moreover, particularly for the modeling of chronic liver disease, such as MASH, it is important to use directly patient-derived cells as short induction cycles (typically 1-2 weeks) of disease phenotypes in organoid models do not faithfully reproduce the molecular signatures that stem from chronic exposures in vivo.

The 3D liver spheroid model we used here is derived from livers from patients with a histologically confirmed diagnosis of MASH. The isolated cells are fully mature and thus do not require in vitro differentiation. There are no MSCs in the 3D cultures; rather the spheroids contain hepatocytes, stellate cells, Kupffer cells as well as various other immune cell types present in the liver at the time of isolation (T cells, B cells, NK cells). Furthermore, the model is extensively characterized at the transcriptomic, proteomic and lipidomic level (PMID 39605182).

Novelty / references

Similar studies that also combined liver and blood lipidomics/metabolomics in obese individuals with and without MASLD (e.g. PMID 39731853, 39653777) should be cited. Additionally, it would benefit the quality of the discussion to state how findings in this study add new insights over previous studies, if their findings/insights differ, and if so, why.

Thank you for the suggestion. We added the two papers into the discussion section. Specifically, we discussed the consistent findings (such as AKR1B10 in PMID 37037945 and mitochondrial dysfunction in PMID 39731853) and discrepancies (such as limited plasma metabolomic changes and circulating sphingolipid alterations in multiple human and mouse models) in comparison with previously published omics studies in MASLD patients. Also, we thoroughly discussed our findings (e.g., lipid dysregulation, dysregulated tryptophan metabolism, GTPase regulation) and potential mechanisms with extensive literature supports from of human, animal, and cell studies.

Minor comments:

1. The quality of Supplementary Figures (e.g. S7) makes is impossible to read the labels Thank you for this feedback. The resolution of the figures was impaired in the initial upload. We will provide all supplementary figures with high resolution in our revised submission and ensure all labels are clearly readable.

For Figure S7C, we presented the correlation matrix of more than 200 GTPase-related genes along with the TGF-β genes TGFB1 and TGFB3. This illustrates the overall co-expression patterns of GTPase-related genes rather than displaying individual gene labels, with arrows now included to highlight TGFB1 and TGFB3.

Reviewer #3 (Significance (Required)):

The authors provide an overall sound study on the hepatic transcriptomic and metabolomic signatures in an Australian cohort of 109 obese non-to-early stage MASLD patients. They perform thorough analyses of metabolome and transcriptome in liver biopsies and metabolome in blood, using standard technologies such as RNA sequencing and mass spectrometry. Their key finding is a GTPase-associated gene signature related to fibrosis onset. Limitations of the study include potential cohort confounders (raising the need for expanded control experiments), limited discussion of similar studies, and limits in cell-type resolution, the latter of which is related to the molecular read out, and has in parts been started to be addressed by in vitro experiments in an immortalized HSC lines. Taken together, given additional control analyses will be performed, the results could be of interest to an expert community in the field of molecular hepatology and, while still descriptive, hold the potential to prompt mechanistic follow-up studies.

We thank this reviewer for a balanced, positive, and constructive evaluation of our manuscript.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Metabolic dysfunction associated liver disease (MASLD) describes a spectrum of progressive liver pathologies linked to life style-associated metabolic alterations (such as increased body weight and elevated blood sugar levels), reaching from steatosis over steatohepatitis to fibrosis and finally end stage complications, such as liver failure and hepatocellular carcinoma. Treatment options for MASLD include diet adjustments, weight loss, and the receptor-β (THR-β) agonist resmetirom, but remain limited at this stage, motivating further studies to elucidate molecular disease mechanisms to identify novel therapeutic targets.

In their present study, the authors aim to identify early molecular changes in MASLD linked to obesity. To this end, they study a cohort of 109 obese individuals with no or early-stage MASLD combining measurements from two anatomic sides: 1. bulk RNA-sequencing and metabolomics of liver biopsies, and 2. metabolomics from patient blood. Their major finding is that GTPase-related genes are transcriptionally altered in livers of individuals with steatosis with fibrosis compared to steatosis without fibrosis.

Major comments:

1. Confounders (such as (pre-)diabetes) The patient table shows significant differences in non-MASLD vs. MASLD individuals, with the latter suffering more often from diabetes or hypertriglyceridemia. Rather than just stating corrections, subgroup analyses should be performed (accompanied with designated statistical power analyses) to infer the degree to which these conditions contribute to the observations. I.e., major findings stating MASLD-associated changes should hold true in the subgroup of MASLD patients without diabetes/of female sex and so forth (testing for each of the significant differences between groups).
2. External validation Additionally, to back up the major GTPase signature findings, it would be desirable to analyze an external dataset of (pre)diabetes patients (other biased groups) for alternations in these genes. It would be important to know if this signature also shows in non-MASLD diabetic patients vs. healthy patients or is a feature specific to MASLD. Also, could the matched metabolic data be used to validate metabolite alterations that would be expected under GTPase-associated protein dysregulation?
3. 3D liver spheroid MASH model, Fig. 6D/E This 3D experiment is technically not an external validation of GTPase-related genes being involved in MASLD, since patient-derived cells may only retain changes that have happened in vivo. To demonstrate that the GTPase expression signature is specifically invoked by fibrosis the LX-2 set up is more convincing, however, the up-regulation of the GTPase-related genes upon fibrosis induction with TGF-beta, in concordance with the patient data, needs to be shown first (qPCR or RNA-seq). Additionally, the description of the 3D model is too uncritical. The maintenance of functional human PHHs in 3D has only become available this year (PMID: 40240606) marking a break-through in the field. Since the authors did not use this system, I would strongly assume their findings are largely attributable to the mesenchymal cells in the 3D culture, and these limitations need to be stated.
4. Novelty / references Similar studies that also combined liver and blood lipidomics/metabolomics in obese individuals with and without MASLD (e.g. PMID 39731853, 39653777) should becited. Additionally, it would benefit the quality of the discussion to state how findings in this study add new insights over previous studies, if their findings/insights differ, and if so, why.

Minor comments:

1. The quality of Supplementary Figures (e.g. S7) makes is impossible to read the labels

Significance

The authors provide an overall sound study on the hepatic transcriptomic and metabolomic signatures in an Australian cohort of 109 obese non-to-early stage MASLD patients. They perform thorough analyses of metabolome and transcriptome in liver biopsies and metabolome in blood, using standard technologies such as RNA-sequencing and mass spectrometry. Their key finding is a GTPase-associated gene signature related to fibrosis onset. Limitations of the study include potential cohort confounders (raising the need for expanded control experiments), limited discussion of similar studies, and limits in cell-type resolution, the latter of which is related to the molecular read out, and has in parts been started to be addressed by in vitro experiments in an immortalized HSC lines. Taken together, given additional control analyses will be performed, the results could be of interest to an expert community in the field of molecular hepatology and, while still descriptive, hold the potential to prompt mechanistic follow-up studies.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

In this paper, Kaldis and collaborators investigate the molecular heterogeneity of a 109 morbidly obese patient cohort, focusing on liver transcriptomics and metabolomics analysis from liver and serum. The main finding (ie upregulation of GTPase-coding genes) was validated in spheroids and a human HSC cell line. As these proteins are involved in critical cellular functions related to metabolism and cytoskeleton dynamics, these findings shed light on their involvement in human liver pathology which so far has been poorly (or even not) documented to date. This is an interesting addition to the current knowledge about chronic liver pathology. However the manuscript suffers from the lack of a clear-cut definition of patient subgroups and the seemingly indistinct use of generic (MASLD, NAS score) and more granular terms (MASH, fibrosis) across the various analysis they performed.

Major comments:

• Are the key conclusions convincing?

The conclusions are generally consistent with findings from numerous previous studies, as many of the genes identified and their associations with disease states have been previously reported. However, I found it difficult to discern which specific disease stages the authors are referring to throughout the manuscript. Terms such as MASLD (Fig. 1F), steatosis (Fig. 4A), MASH, fibrosis (Fig. 6), and the composite NAS score (Fig. 1G) are used interchangeably, without clearly explaining whether or how the patient cohort was stratified to distinguish between isolated steatosis, MASH, and MASH with or without fibrosis. It is also unclear whether subgroups were propensity score-matched.

In a related point, the authors mention that 76% of patients are non-fibrotic, introducing a marked imbalance between fibrotic (n=26) and non-fibrotic (n=83) samples. Given this disparity and potential inter-individual variability, it would be helpful to include observed fold changes or effect sizes to give readers a sense of the magnitude of the biological dysregulations being reported. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? - The authors seem pretty enthusiastic about elafibranor, despite a failed phase 3 clinical trial. I would qualify elafibranor as a useful tool in preclinical model.<br /> - The authors should make clearly the pronounced sex bias in their study, which includes mostly women (and btw refer to sex and not gender in the manuscript).<br /> - The "MASH" status of the spheroid model is overstated. As described in the text it is much closer to a lipotoxicity model (and even glucotoxicity as Glc concentration is 2g/L). This is confusing with panel D in which the authors establish a relationship between fibrotic patients (F2/F3 vs F0/S0, so I guess "no MASLD liver?) and this model. Is the relationship maintained for steatotic-only patients?<br /> - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. I am not convinced that HSC and LX2 cells express significant levels of PPARα. However, did the authors check for this parameter in their LX2 cell line and assessed whether PPARα/b activation by elafibranor (and/or pemafibrate as it is PPARα selective) alter GTPase expression? Whether negative or positive, this could give a clue about possible intercellular crosstalk in the spheroid model.<br /> - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

The experiment mentioned above is cheap (cell culture, RT-QPCR) and can be performed within a couple of weeks. - Are the data and the methods presented in such a way that they can be reproduced?

Yes - Are the experiments adequately replicated and statistical analysis adequate?

There is no indication of group size, number of replicates for in vitro experiments

Referees cross-commenting

I believe there is a general consensus on this potentially interesting contribution to the field, with three main points: (1) the need for a careful group-by-group comparison that accounts for potential confounders, (2) a more rigorous exploitation/characterization of the spheroid system, and (3) the need to benchmark the authors' findings against the available literature.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The authors identified GTPases as players in the progression of MASLD. This is an interesting preliminary report warranting further molecular investigations (in which liver cell types, which GTPase pathway(s) are involved, which functions are controlled through this pathway...)
• State what audience might be interested in and influenced by the reported findings. This paper will have an impact in the hepatology field
• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. I have expertise in the analysis of "MASLD" human cohorts and in the molecular biology of chronic liver diseases.

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

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

Metabolic dysfunction-associated steatotic liver disease (MASLD) ranges from simple steatosis, steatohepatitis, fibrosis/cirrhosis, and hepatocellular carcinoma. In the current study, the authors aimed to determine the early molecular signatures differentiating patients with MASLD associated fibrosis from those patients with early MASLD but no symptoms. The authors recruited 109 obese individuals before bariatric surgery. They separated the cohorts as no MASLD (without histological abnormalities) and MASLD. The liver samples were then subjected to transcriptomic and metabolomic analysis. The serum samples were subjected to metabolomic analysis. The authors identified dysregulated lipid metabolism, including glyceride lipids, in the liver samples of MASLD patients compared to the no MASLD ones. Circulating metabolomic changes in lipid profiles slightly correlated with MASLD, possibly due to the no MASLD samples derived from obese patients. Several genes involved in lipid droplet formation were also found elevated in MASLD patients. Besides, elevated levels of amino acids, which are possibly related to collagen synthesis, were observed in MASLD patients. Several antioxidant metabolites were increased in MASLD patients. Furthermore, dysregulated genes involved in mitochondrial function and autophagy were identified in MASLD patients, likely linking oxidative stress to MASLD progression. The authors then determined the representative gene signatures in the development of fibrosis by comparing this cohort with the other two published cohorts. Top enriched pathways in fibrotic patients included GTPas signaling and innate immune responses, suggesting the involvement of GTPas in MASLD progression to fibrosis. The authors then challenged human patient derived 3D spheroid system with a dual PPARa/d agonist and found that this treatment restored the expression levels of GTPase-related genes in MASLD 3D spheroids. In conclusion, the authors suggested the involvement of upregulated GTPase-related genes during fibrosis initiation. Overall, the current study might provide some resources regarding transcriptomic and metabolomic data derived from obese patients with and without MASLD. However, several concerns should be carefully addressed.

1. A recent study, via proteomic and transcriptomic analysis, revealed that four proteins (ADAMTSL2, AKR1B10, CFHR4 and TREM2) could be used to identify MASLD patients at risk of steatohepatitis (PMID: 37037945). It is not clear why the authors did not include this study in their comparison.
2. The authors recruited 109 patients but only performed transcriptomic and metabolomic analysis in 94 liver samples. Why did the authors exclude other samples?
3. The authors mentioned clinical data in Table 1 but did not present the table in this manuscript.
4. The generated metabolomic data could be a very useful resource to the MASLD community. However, it is very confusing how the data was generated in those supplemental tables. There is no clear labeling of human clinical information in those tables. Also, what do those values mean in columns 47-154? This reviewer assumed that they are the raw data of metabolomic analysis in plasma samples. However, without clear clinical information in these patients, it is impossible that any scientist can use the data to reproduce the authors' findings.
5. In Fig. 5B, the authors excluded the steatosis and fibrosis overlapped genes. Steatosis and fibrosis specific genes could simply reflect the outcomes rather than causes. In this case, the obtained results might not identify the gene signatures related to fibrosis initiation.
6. In Fig. 6D, the authors used 3D liver spheroid to validate their findings. However, there is no images showing the 3D liver spheroid formation before and after PPARa/d agonist treatment. It is not clear whether the 3D liver spheroid was successfully established.
7. The authors suggested that targeting LX-2 cells with Rac1 and Cdc42 inhibitors could reduce collagen production. Did the authors observe these two genes upregulated in mRNA and protein expression levels in their cohort when compared MASLD patients with and without fibrosis?
8. Did the authors observe that the expression levels of Rac1 and Cdc42 are correlated with fibrosis progression in MASLD patients?
9. Other studies have revealed several metabolite changes related to MASLD progression (PMID: 35434590, PMID: 22364559). However, the authors did not discuss the discrepancies between their findings with the previous studies.

Significance

Overall, the current study might provide some new resources regarding transcriptomic and metabolomic data derived from obese patients with and without MASLD. The MASLD research community will be interested in the resource data.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The manuscript by Xu et al. investigated split gene drive systems by targeting multiple female essential genes involved in fertility and viability in Drosophila. The authors evaluate the suppression efficiency through individual corsses and cage trials. Resistance allele formation and fitness costs are explored by examining the sterility and fertility of each line. Overall, the experimental design is sound and methods are feasible. The work is comprehensive, and conclusions are well supported by the data. This work offers informative insights that could guide the design of suppression gene drive systems in other invasive disease vectors or agricultural pests.

However, several points requiring clarification or improvement:

1 Methodological clarity: Some experimental details are indufficiently described, for example, regarding the setup of genetic crosses involving different Cas9 derivatives. In line 197-198, "the mated females, together with females that were mated with Cas9 only males", it is unclear whether the latter group refers to gRNA-females.

-We thank the reviewer for pointing out this ambiguity. The latter group refers to Cas9 females crossed to Cas9 males. We have clarified this both in the methods (line 207) and results (line 505-509).

2.Regarding the inheritance rates, you included the reverse orientation of CG4415-Cas9, as I understood, it means this component is in reverse orientation with fluorescent marker. Since it is standard to design adjacent components in opposite direction to avoid transcriptional interference, the rationale for including this comparison should be better justified.

• In our construct, ‘CG4415 (reverse orientation)’ indicates that Cas9 was oriented in the same direction as the fluorescent marker, while the other Cas9 constructs (nanos-Cas9 and CG4415-Cas9) places them in opposite directions. “reverse” just indicates a change from a “standard” in another study. Our previous publication showed that Cas9 orientation relative to the marker had little apparent effect on drive performance at the yellow-G locus. In this study, we compared both orientations in a fertility gene and again observed similar results, suggesting that orientation relative to the marker does not substantially affect drive efficiency in our system. We have clarified this in the figure legend text.

Embryo resistance is inferred from the percentage of sterile drive females derived from drive mothers. How many female individuals were analysed per line and why deep sequencing was not employed to directly detect resistance alleles.

-Embryo resistance can mean slightly different things for different applications. The most important is probably the fraction of females that have little to no fertility due to embryo resistance. Some of these may not have complete embryo resistance alleles, but instead, have mosaicism, with a sufficient level of resistance to still cause sterility. It is unclear exactly what proportion of resistance to wild-type may cause this, and thus, proportions from pooled sequencing, which could include both complete and all levels of mosaicism, may not be sufficient to measure this parameter. Another relevant parameter that we did not measure is the fraction of males rendered unable to do drive conversion (this value should be closer to the complete resistance rate, but probably still lower because of the multiple gRNAs). Even in this case, deep sequencing would not allow us to determine exactly what is happening in males, making individual sequencing a preferred approached. It is very nice, of course, for characterizing which resistance alleles are present overall, but in this study, we wanted to put a bit more emphasis on the effect of resistance, rather than its sequence characterizing.

We analyzed 30 females per line for lines targeting nox, oct, dec and stl, 9 females for ndl and 276 individuals for line tra-v2 (Data Set S4). We believe such individual analyses sufficiently detected embryo resistance causing sterility within reasonable error. Note that we did also randomly genotype several sterile females and found mutations at target sites that disrupted gene functions.

In response to this comment, we have added some text to justify our measurement of resistance alleles and include some of this discussion:

“Note also that this defines embryo resistance as sufficient to induce sterility, but these may be mosaic rather than complete resistance. Further, note that the multiplex gRNA design in males may allow for continued drive conversion with a complete (as opposed to mosaic) embryo resistance allele, if some sites remain wild-type.”

Masculinisation phenotypes were observed upon disruption of tra gene. How strong intersexes were distinguished from males? What molecular markers were used to determine genetic sex. This information should be clearly provided.

-We observed two types of strong masculinisation phenotypes (Figure S2), one with bigger body size than wildtype males, and the other was identical to wildtype males. The homozygosity of the drive allele could be assessed by the brightness of red fluorescence in the eyes. However, we also randomly genotyped these masculinized females (as part of a batch that included males) to confirm their sex using primers for the Y-linked gene PP1Y2. A specific band was detected in wild-type males but not in masculinized females, confirming their genetic sex. This information has been added to the manuscript (lines 477-480).

It would be more appropriate to use "hatchability"rather than "fertility" when referring to egg-to-larva viability.

-Thank you for the suggestion. We used egg-to-adult survival rates as a proxy for the fertility of their parents because they usually laid similar number of eggs. However, it still technically incorrect language. We have fixed this in line 582 and elsewhere in the section.

In cage trials, a complete gene drive is mimicked by introducing Cas9 to the background population, but this differs from actual complete gene drive, due to potential effects from separate insertion sites (different chromosome or loci). These difference could impact the system's performance and should be discussed.

-We appreciate this point and have added discussion on the limitations of mimicking a complete gene drive using split components (line 766-779).

7.Given the large amount of data presented, it would improve readability and interpretation if each result section concluded with a concise summary highlighting the key findings and implications.

-Thank you for the suggestion. We have added brief summaries at the end of each results section to highlight the key findings and their significance.

Reviewer #1 (Significance (Required)):

The authors evaluate suppression efficiency through individual courses and cage trials. Resistance allele formation and fitness costs are explored by examining the sterility and fertility of each line. Overall, the experimental design is sound and methods are feasible. The work is comprehensive, and conclusions are well supported by the data. This work offers informative insights that could guide the design of suppression gene drive systems in other invasive disease vectors or agricultural pests.

-We appreciate the reviewer’s positive assessment of our work.

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

Paper summary

The manuscript by Xu. et al presents an insightful and valuable contribution to the field of gene drive research. The manuscript by Xu et al. presents an insightful and valuable contribution to the field of gene drive research. The strategy of targeting and disrupting female fertility genes using selfish homing genetic elements was first proposed by Burt in 2003. However, for this approach to be effective, the phenotypic constraints associated with gene disruption have meant that the pool of suitable target genes remains relatively small - notwithstanding the significant expansion in accessible targets enabled by CRISPR-based genome editing nucleases. Population suppression gene drives are well developed as proof-of-principle systems, with some now in the late stages of development as genetic control strains. However, advancing the pipeline will require a broader set of validated target genes - both to ensure effectiveness across diverse species and to build redundancy into control strategies, reducing reliance on any single genetic target.

In their paper, the authors conduct a systematic review of nine female fertility genes in Drosophila melanogaster to assess their potential as targets for homing-based suppression gene drives. The authors first conduct a thorough bioinformatic review to select candidate target genes before empirically testing candidates through microinjection and subsequent in vivo analyses of drive efficiency, population dynamics, and fitness costs relating to fecundity and fertility. After finalising their results, the authors identify two promising candidate target genes - oct and stl - which both demonstrate high gene conversion rates and, regarding the latter, can successfully suppress a cage population at a high release frequency. However, the manuscript suffers from a lack of in-depth discussion of a key limitation in its experimental design - namely, that the authors utilise a split-drive design to assess population dynamics and fitness effects when such a drive will not reflect release scenarios in the field. The review below highlights some major strengths and weaknesses of the paper, with suggestions for improvement.

Key strengths

The study's most significant strength is in its systematic selection and empirical testing of nine distinct genes as targets for homing-based gene drive, hence providing a valuable resource that substantially expands the pool of potential targets beyond the more commonly studied target genes (e.g. nudel, doublesex, among others). The identification of suitable target genes presents a significant bottleneck in the development of gene drives and the work presented here provides a foundational dataset for future research. The authors bolster the utility of their results by assessing the conservation of candidate genes across a range of pest species, suggesting the potential for broader application.

A key finding in the paper is the successful suppression of a cage population using a stl-targeting gene drive (albeit at a high release frequency). This provides a critical proof-of-principal result demonstrating that stl is a viable target for a suppression drive. While in the paper suppression was not possible at lower release frequencies, together, the results provide evidence for complex population dynamics and threshold effects that may govern the success or failure of a gene drive release strategy - hence moving the conversation from a technical perspective ("can it work") to how a gene drive may be implemented. Moreover, the authors also employ a multiplexed gRNA strategy for all their gene drive designs and in particular their population suppressive gene drive targeting stl. This provides further proof-of-principal evidence for multiplexed gRNAs in order to combat the evolution of functional resistance following gene drive deployment.

Finally, a further strength of this paper is in the clever dissection of fitness effects resulting from maternal Cas9 deposition. The authors design and perform a robust set of crosses to elucidate the parental source of fitness effects (i.e. maternally, paternally, or biparentally derived Cas9), finding (as they and others have before) that embryonic fitness was significantly reduced when Cas9 was inherited from a maternal source. As discussed, the authors conclude that maternal deposition is particularly pronounced in the context of split drives as opposed to complete drives, with the implication being that a complete drive might succeed where a split-drive has failed; thus providing a key directive for future study.

Concerns

The manuscript's central weakness lies in its interpretation of the results from the cage experiments - namely that a split-drive system was used to "mimic the release of a complete drive". In the study, mosquitoes carrying the drive element (i.e. the gRNA) were introduced into a population homozygous for the Cas9 element over several generations. This design is likely not representative of a real-world scenario and, as the authors state, likely exaggerates fitness costs. This is because the females carrying Cas9 will maternally deposit Cas9 protein into her eggs, with activity spanning several generations. When mated with a drive-carrying male the gRNA will immediately co-exist with maternally deposited Cas9, leading to early somatic cleavage and significant fitness costs (reflected in the author's own fertility crosses). This is fundamentally different to how a complete drive would function in a real-world release, where complete-drive males would mate with wild-type females not carrying Cas9. Their offspring would carry the drive element but would not be exposed to maternally deposited cas9, thus deleterious maternal effects would only begin to appear in the subsequent generation from females carrying the drive. Fitness costs measured from split-drive designs are therefore likely substantially overestimated compared to what would occur during the initial but critical release phase of a complete drive. This flaw weakens the paper's ability to predict the failure or success of the screened targets in a complete drive design, thus weakening the interpretation of the results from the cage trials. As a suggestion for improvement, the authors should explicitly and more prominently discuss the limitations of their split-drive model compared to complete drive models, both in the Results and Discussion. It is also recommended to include a schematic for both strategies that contrasts the experimental setup design (i.e. release of the drive into a Cas9 homozygous background) with a complete-drive release, clearly illustrating differences in maternal deposition pathways. This will not only contextualise the results and support the author's conclusion that observed fitness costs are likely an overestimate but will further strengthen the arguments that the candidate target genes found in this study may still be viable in a complete-drive system.

-We sincerely appreciate the thoughtful review and the valuable comments and suggestions provided, which have helped improve both the clarity and readability of this study. We have revised several parts in the discussion of the manuscript and hope that these changes adequately address the concerns raised. We have also made Figure S5 to illustrate the differences between two release strategies (biparental-Cas9 split drive in our study and complete drive in real release).

Please note that this type of fitness cost may have partially undermined our cage study (the fitness effect is notable, but still small compared to total fitness costs), but this is also among the first studies to propose and investigate this phenomenon in the first place (it is also noted in another preprint from our lab but to our knowledge not proposed elsewhere). Thus, part of the impact of our manuscript is showing that this is important, which may inform future cage studies in our lab and elsewhere.

A second weakness in the manuscript relates to its limited explanation and discussion of key concepts. For example, the manuscript reports a stark difference in outcome of the two stl-targeting drives, where a high initial release in cage 1 led to population elimination versus a failure of the drive to spread in cage 2. The authors attribute this to vague "allele effects" and stochastic factors such as larval competition; however the results appear reminiscent of the Allee effect, which is a well-characterised phenomenon describing the correlation of population size (or density) and individual fitness (or per capita population growth rate). Using their results as an example, is it plausible that the high-frequency initial release in cage 1 imposed enough genetic load to quickly drive the population density below the Allee threshold thus quickly leading to population eradication. In cage 2, the low-frequency at initial release was insufficient to cross the Allee threshold. Omitting mention of this ecological principal greatly weakens the Discussion, and further presents a missed opportunity to discuss one of the more crucial strengths of the paper - that is, in providing a deeper insight into the practical requirements for successful field implementation.

-While we do indeed mention this Allee effect (the “allele effect” noted above is a misspelling that we have corrected), we were hesitant to give it much discussion, considering that the specific Allee effect in our cages is likely of a very different nature than one would find in nature (we explain that it is likely due to bacterial growth that occurs when fewer larvae are present). However, it is perhaps still a good excuse to cover it in the discussion, while still noting that the specific Allee effect in our cage may not be representative. We have added the following text: “Nonetheless, the successful result in the cage with high release study may point to a potential field strategy for a drive that is less efficient (perhaps even one found to be less efficient in initial field tests compared to laboratory tests). If the initial release frequency of the drive is sufficiently high and widespread, then short-term high genetic load may substantially reduce the population, perhaps enough for Allee effects to become important. At this point, even if average genetic load is slowly declining without additional drive releases, persistent moderate genetic load coupled with the Allee effect may be sufficient to ensure population elimination.”

In a similar vein, the authors provide only a superficial mechanistic discussion into the fitness costs associated with drives targeting key candidate genes. The paper would benefit from a deeper discussion regarding the specific molecular functions of top-performing genes (stl, oct, nox) and how unintended Cas9 activity could disrupt their activity, integrating known molecular functions with observed fitness costs. For instance, oct encodes a G-protein coupled receptor essential for ovulation and oviduct muscle relaxation, thus disruption to the oct gene would directly impair egg-laying which would account for the observed phenotypic effects. A deeper discussion linking unintended Cas9 activity to the specific, sensitive functions of target genes would elevate the paper from a descriptive screen to a more insightful mechanistic study.

-We appreciate the reviewer’s comment. We have added a discussion to further explain fitness cost caused by unintended Cas9 activity disrupting target gene functions. However, keep in mind that the exact timing of Cas9 cleavage and the exact timing of these gene’s essential functions is still somewhat uncertain, which may limit insights from this line of analysis compared to a situation where ideal, high quality data is available for both of these. Here is the new material in the discussion:

“The functions of the top-performing genes suggests a mechanistic basis for the observed fitness costs. Aside from germline cells, nanos has expression in other ovary cells as well. CG4415 lacks this expression, but our Cas9 construct with this promoter may have a different expression pattern that the native gene, as evidenced by its support for good drive conversion in females. stl is essential for ovarian follicle development, and its disruption likely in non-germline ovary cells could compromise egg chamber development and fertility. oct encodes the octopamine β2 receptor, a G-protein coupled receptor critical for ovulation and fertilization, so if it were similarly lost, egg-laying would be directly impaired. nox, which encodes NADPH oxidase, contributes to calcium flux and smooth muscle contraction during ovulation, so its disruption may prevent egg laying. tra is needed in the whole body for sexual development, but may also play an important role in ovary function. Thus, unintended Cas9 activity at these non-germline ovary cells can directly interfere with sensitive reproductive functions, potentially explaining the fertility costs observed in drive carriers. This issue could potentially be overcome if promoters were available that were truly restricted to germline cells rather than other reproductive cells, though it remains unclear if such promoters both exist and would retain their expression pattern at a non-native locus.”

It is curious that the authors chose two genes on the X chromosome as targets. In insects (such as Drosophila here) that have heterogametic sex chromosomes, homing is not possible in the heterogametic sex as there is no chromosome to home to - so there will be no homing in males. On top of that, there is usually some fitness effect in carrier (heterozygous) females, so in a population these are nearly always bad targets for drives - unless there is some other compelling reason to choose that target?

-Our rationale for testing X-linked targets is twofold. First, these genes are likely to play important roles in sex-specific functions and may have a different expression pattern (which is why specifically Dec was included), potentially reducing fitness costs. Although homing cannot occur in males, if drive conversion at these sites in females is very high and fitness costs are minimal, the resulting genetic load could still be sufficient to suppress populations (thus, such candidates could be superior even in diploids if they happen to have a lower fitness costs). Second, X-linked targets may have broader relevance for suppression drives in haplodiploid pests (e.g., fire ants), which has the same population dynamics as an X-linked target in a diploid populations. Our results therefore could have provided useful insights for such scenarios (such as for fire ants: Liu et al., bioRxiv 2025) if drive performance was sufficient for followup testing.

Minor comments

• Enhanced clarity in the Figures and data presentation would greatly improve readability. For example, Figure 5 is critical yet difficult to interpret; consider changing x-axis labels from icons to explicit text (e.g. "biparental Cas9", "maternal cas9", "paternal Cas9"). Similarly, Figure 4 is difficult to read and the y-axis label "population size" is ambiguous; consider adding shapes or dashes (rather than relying solely on colour) and clarifying the y-axis (e.g. no. adults collected) in the legend.

-We appreciate the reviewer’s comment and have revised Figure 4 as suggested. Regarding Figure 5, we attempted to replace the icons with text labels; however, this was not possible because there is very little horizontal space and two generations to specify. Instead, we have revised the figure legend to provide a clearer explanation, which can hopefully improve clarity..

• Expand on or include a schematic to show the differences in construction between the tra-v1 and tra-v2 constructs to better contextualise the discrepancies in results (e.g. inheritance rates of 61%-66% for tra-v1 and 81%-83% for tra-v2 between the two.

-We have expanded Figure 2 to compare the constructs of tra-v1 and tra-v2. The further explanation of these two constructs was added into the result section: ‘When targeting tra, we originally tested the 4-gRNA construct tra-v1. However, the drive inheritance rate was relatively low (61%-66%), and sequencing revealed that only the middle two gRNAs were active (Table S3). Lack of cleavage at the outmost sites is particularly detrimental to achieving high drive conversion. Therefore, a second construct tra-v2 was tested that retained the two active gRNAs and included two new gRNAs. It showed substantially improved drive inheritance (81%-83%). ’

• Minor typos e.g.:

o Line 87: "form" to "from"

o Line 484: "expended" to "expanded

o Line 560: "foor" to "for"

o Line 732: "conversed" to "conserved

-We have revised these typos.

• Clarify the split drive system: the authors introduce split drive for the first time in Line 118. They should at least give a clear definition and explanation of split drive and complete drive in the introduction.

-We have included an introduction of split drive and complete drive in the introduction (line 47-53).

• Line 237-238., The fitness evaluation lacks a clear description of controls. How were non-drive flies generated and validated as controls?

-Drive heterozygotes were crossed with Cas9 homozygotes to generate the flies used for fitness evaluation. From the same cross, non-drive progeny were obtained and used as controls, ensuring they shared a comparable genetic background and rearing conditions with the drive-carrying individuals. We have now clarified in the manuscript results that “these served as the controls because they had the same environment and parents as the drive flies”.

• Line 409-412.,line 423.,The high inheritance rates of stl and oct drives are impressive; however, variation in results across Cas9 promoters should be explained further in the discussion.

-In the discussion section (lines 751-765), we included a dedicated paragraph addressing the variation observed between the nanos and CG4415 promoters. We have now expanded it to briefly note some differences:

“Our previous works showed that both nanos and CG4415 have high drive conversion rates8, but nanos failed to suppress target populations in a homing drive targeting the female fertility gene yellow-G due to its fitness cost in drive females27. CG4415 had much lower maternal deposition, which allowed the elimination of cage populations by targeting yellow-G8. Here, we tested both promoters with drives targeting oct and stl, with both showing slightly higher drive efficiency than the drive targeting yellow-G in small-scale crosses. CG4415 has slightly worse though still good performance in females, likely due to male-biased expression compared to nanos.”

• Line 414: The CG4415 promoter yielded reduced drive conversion rates in females, yet is still referred to as a promising promoter. This conclusion seems optimistic and should be clarified/more justified.

-Based on our previous study cited in this context, CG4415 shows relatively lower germline conversion rates compared to nanos, although still remaining at a high level. Importantly, CG4415 also exhibits reduced maternal deposition relative to nanos, which could help mitigate fitness costs associated with maternal deposition—an important consideration for suppression systems. Taken together, while its conversion efficiency is lower (but only slightly), the potential benefits of reduced maternal deposition and perhaps even fitness costs provide a rationale for regarding CG4415 as a promising promoter. We state this when first introducing the promoter in the “Drive efficiency assessment” results subsection.

• Specify the number of flies released, sex ratio, and cage size per generation (Line 466). This is essential for reproducibility.

-We appreciate the reviewer’s comment and have revised the text to clarify our release approach, which differed from that used in other studies (which tend to have substantial fitness differences between lines in the first generation that can complicate analysis and change results). Rather than directly releasing drive males or females into cages, we first crossed drive males with non-drive females and then mixed them with non-drive females mated to non-drive males. The offspring (including males and females) from these crosses were recorded as the G0 generation, and their ratios were recorded as release frequency. We have specified the release ratio adult numbers in the following paragraph and supplementary file.

Reviewer #2 (Significance (Required)):

Overall the manuscript presents a valuable and timely resource for gene drive research, in particular for its systematic appraisal of potential target genes for population suppression drives and its rigorous assessment of the impact of maternal Cas9 deposition. The value in the generation and empirical testing of a novel multiplexed stl-targeting gene drive that led to population eradication in a cage trial should not be understated. While several key aspects of the discussion of the manuscript should be strengthened, the study presents a meaningful contribution to the field, extending previous work and and outlines important considerations for the design and implementation of effective gene drive systems.

-We thank the reviewer for their encouraging and constructive comments. We are pleased that the systematic evaluation of target genes, the analysis of maternal Cas9 deposition, and the multiplexed stl-targeting drive were recognized as valuable contributions. We have strengthened the discussion as suggested, and we believe these revisions further enhance the manuscript as an aid for the design and implementation of future gene drive systems.

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

In this study, Xu and colleagues explored how CRISPR-based homing gene drives could be used to suppress insect populations by targeting female fertility genes in Drosophila melanogaster. They engineered split gene drives with multiplexed guide RNAs to target nine candidate genes, seeking to prevent functional resistance and achieve high drive conversion with minimal fitness costs.

Here my comments about this work:

Abstract: While the stated aim of the study on line 16 is to "maintain high drive conversion efficiency with low fitness costs in female drive carriers," the conclusion in lines 29-31 shifts focus toward the broader challenges and future optimization of gene drive systems. This conclusion does not clearly highlight the specific results of the study or how they relate directly to the original objective. It would be more effective to emphasize the actual findings, such as which target genes performed best and under what conditions, and how these findings support or contradict the stated goals. The study primarily aimed to assess the efficiency of specific female fertility genes and to evaluate strategies for minimizing the formation of functional resistance alleles, rather than proposing a protocol for optimization. Therefore, better alignment is needed between the study's aim, experimental design, and concluding statements. Clarifying this alignment would also help refine the paper's focus and more accurately communicate its contribution, including whether it is exploratory, comparative, or methodologically driven.

-We have revised the abstract to clarify the alignment as suggested by the reviewer. We note that this discrepancy is due to the initial aim of our study being different than some of the important lessons learned along the way regarding fitness effects from Cas9 deposition in split drives. Still, we agree that it would be better to be more consistent in our wording and conclusions.

Introduction: One of the key design elements in this study is the use of multiplexed gRNAs. It is reasonable to assume that this strategy may influence fitness costs, potentially in more than one way. Given that assessing fitness cost is a major focus of the study, it would be helpful to include a brief discussion of previous research examining how multiplexed gRNAs may impact fitness in gene drive systems. A short review of relevant studies, if available, would provide important context for interpreting the results and could help clarify whether any observed fitness costs might be attributed, at least in part, to the multiplexing strategy itself. This addition could be appropriately placed around line 102, where gRNA design is discussed.

-We have added an explanation in the Discussion to mention this. However, it has not been conclusively shown that multiplexed gRNAs have any effect on fitness. Indeed, there have been some multiplexed constructs that seem to have no fitness effect, and some that have high fitness costs. This doesn’t rule out the potential for multiplexed gRNAs to influence fitness itself, but it means that the mechanism may be complex. The new text reads:

“Another potential though unconfirmed source of fitness cost arises from increased cleavage events associated with multiplexed gRNAs, where the greater number of gRNAs can enhance the overall cut rate compared to single-gRNA designs.”

Line 42: Cas12a also showed efficacy using gene drives in yeast and Drosophila.

-We now mention Cas12a at the beginning of the introduction.

Line 133: The paragraph begins by stating that homologs of the target genes were identified and aligned. To improve clarity, especially for readers who are new to gene drive research, it would be helpful to begin the paragraph with a brief introductory sentence explaining the purpose of this step. For example, you could state the importance of identifying and aligning homologs to assess the conservation of target sites across species, which is critical for evaluating the broader applicability of gene drive strategies. This context would guide the reader and clarify the relevance of the analysis.

-We have added the explanation as suggested.

Lines 144-145: You mention that "the exception was tra, for which two constructs containing different gRNA sets were generated." For clarity, it would be helpful to provide a brief explanation of why two different gRNA sets were used for tra, and whether this differs from the approach taken with the other target genes. It's currently unclear whether all other genes were targeted using a single, standardized set of gRNAs, and this should be explicitly stated here for consistency, even though it is mentioned later in the plasmid construction section. Additionally, I suggest combining the sections on gRNA target design and plasmid construction. Since these components are closely related and sequential in the experimental workflow, presenting them together would improve the logical flow and help readers follow the methodology more smoothly.

-We have combined both the gRNA target design and plasmid construction sections. We also discuss the two tra constructs early in the results section (see response to reviewer 2).

Line 210: The analysis of the cage experiments was based on models from previous studies that used a simplified assumption of a single gRNA at the target site. While I understand this approach has precedent, it raises important questions about potential limitations. Specifically, could simplifying the analysis to one gRNA affect the conclusions of this study, given that the experimental design involves multiplexed gRNAs with four distinct target sites? The implications of using this simplified model should be clearly addressed, as the dynamics of drive efficiency, resistance formation, and fitness effects may differ when multiple gRNAs are employed. Additionally, while I am not a statistician, it is worth asking whether more sophisticated modeling approaches could be applied to account for all four gRNAs, rather than reducing the system to a single-gRNA framework. A discussion of the modeling choices and their potential consequences would strengthen the interpretation of the results.

-We have clarified this. While we have modeled multiple gRNAs with high fidelity in SLiM, the maximum likelihood method is not very amenable to such treatment. It may cause our fitness estimate to be a small overestimate, but give the low fitness inferences, would certainly not have a large enough effect to fundamentally change any conclusion (and should be of a consistent level across all cages). We now discuss this in the methods section.

Lines 297-300: Your results show that the expression of all target genes was higher in females, except for oct, which had higher expression in males. Additionally, oct expression decreased in adults. Given that oct is functionally important for ovulation and fertilization, processes that are primarily required in adult females, this pattern is somewhat unexpected. Could there be a possible explanation for the lower expression of oct, particularly in females and especially in adults, where its function would presumably be most critical? A brief discussion or hypothesis addressing this discrepancy would help clarify the biological relevance and interpretation of the expression data.

-Based on transcriptome data from FlyBase, derived from Graveley et al. (2011), Oct is indeed expressed slightly higher in adult males than in adult females. This difference may be attributed to the fact that the female flies used in the study were virgins; Oct expression could be upregulated post-mating to mediate ovulation. Additionally, Oct is expressed not only in reproductive tissues but also in other organs such as the nervous system, where sex-specific differences in cell type composition or neural activity may contribute to the observed expression bias. However, high expression does not necessarily correlate with essential expression. Though Oct could have multiple functions, it’s still possible that the only apparent phenotype upon knockout is female sterility. We have added the following text: “This male-biased expression may result from the use of virgin females in the dataset, as oct is likely upregulated after mating. Moreover, oct is also expressed in non-reproductive tissues such as the nervous system, which may contribute to sex-specific differences in expression38. While oct may have multiple functions, it is possible that it is only essential for female fertility.”

Lines 346-347: What is the distance between the gRNA target sites within each gene? Are all of the gRNAs confirmed to be active? It would be valuable to include a table summarizing the distance between target sites for each gene, the activity levels of the individual gRNAs, and the corresponding homing rates. This would help determine whether there is a correlation between gRNA spacing and drive efficiency. For example, Lopez del Amo et al. (Nature Communications, 2020) demonstrated that even a 20-nucleotide mismatch at each homology arm can significantly reduce drive conversion. Including such a comparative analysis in your study could provide important insights into how gRNA arrangement influences overall drive performance and would be incredibly helpful for future multiplexing designs.

-We have showed previously that close spacing of gRNAs should help maintain high drive conversion efficiency, and this is alluded to indirectly in the introduction (we now mention it more directly). In our study, gRNAs were positioned in close proximity without overlap, with the general distance between the outermost cut sites within each gene being We have added a summary table (Table S3) presenting the sequencing results, which also showed gRNA activity levels. Notably, most but not all gRNAs were active, at least for embryo resistance (low to moderate activity may still be present in the germline). Coupled with varying activity levels for those that were active, this likely contributed to reduced drive conversion due to mismatches at the homology arms. This observation supports the notion that drive performance could be optimized by selecting and arranging more active gRNAs. Consistent with this, our second construct targeting tra (tra-v2) exhibited a higher inheritance rate than the original construct, suggesting that gRNA arrangement and activity critically influence drive efficiency. Testing the activity of every single gRNA requires the construction of multiple gRNA lines, since in vitro or ex vivo tests will not be accurate as in vivo transformation test. However, in our study, as long as drive conversion rates were reasonably high, further optimization was not needed. Therefore, the multiplexing gRNA design can not only maximize drive conversion, but also reduce labor filtering an increased number of 1-gRNA designs with lower performance.

Line 434: I was not able to find any sequencing data. This is important to evaluate gRNA activities and establish correlations with drive efficiency.

-We have added a summary of the sequencing results in Table S3, though these are for embryo resistance alleles. Note that while high gRNA activity is correlated with high drive inheritance, these are not directly related. For suppression drives, germline resistance rates are usually of low importance compared to drive inheritance, so we did not assess these in detail (and pessimistically assumed complete germline resistance in our cage models).

Line 482: Did the authors test Cas9-only individuals (without the drive) against a wild-type population? This would help determine whether Cas9 alone has any unintended fitness effects. Additionally, is Cas9 expression stable over time and across generations? It would be helpful to include any observations or thoughts on the long-term stability and potential fitness impact of Cas9 in the absence of the drive element.

-We did not perform a direct comparison of Cas9-only individuals and wild-type flies in this study. However, previous studies (Champer et al., Nature Communications, 2020 - Langmuller et al., eLife 2022), which we now cite in the discussion, found no significant fitness difference between very similar Cas9-expressing lines and wild type in the absence of a drive element, indicating no significant fitness impact from Cas9 alone (though we cannot exclude a small effect, it certainly could not come close to explaining our results). In our experiments, Cas9 expression was generally stable across generations, as indicated by consistent drive inheritance and fertility test results obtained from independent batches. Separate from this study, we did observe rare instability in one nanos-Cas9 line, which had remained stable for over five years but recently became inactive (low population maintenance size may have caused stochastic removal of the functional allele). It is something to watch out for, but probably not on the timescale of a single study.

Discussion: I would appreciate a more direct and clearly stated conclusion that summarizes the key findings of the study. While the discussion addresses the main outcomes in depth, presenting a concise concluding paragraph, either at the end of the discussion or as a standalone conclusion section, would provide a stronger and more definitive closing statement. This would help reinforce what the study ultimately achieved and ensure the main takeaways are clearly communicated to the reader.

-We have revised and expanded the last paragraph of the discussion section to make our findings more direct and clear.

Overall, I believe this is an important study that offers valuable insights for advancing the design of CRISPR-based gene drives. The findings contribute to the development of more efficient and practical gene drive prototypes, bringing the field closer to real-world applications.

Reviewer #3 (Significance (Required)):

In this study, Xu and colleagues explored how CRISPR-based homing gene drives could be used to suppress insect populations by targeting female fertility genes in Drosophila melanogaster. They engineered split gene drives with multiplexed guide RNAs to target nine candidate genes, seeking to prevent functional resistance and achieve high drive conversion with minimal fitness costs. Among the targets, the stall (stl) and octopamine β2 receptor (oct) genes performed better, showing the highest inheritance rates in lab crosses. When tested in population cages, the stl drive was able to completely eliminate a fly population, but only when released at a high enough frequency, while other cages failed. These failures were traced and explained by fitness cost in drive-carrying females, caused largely by maternally deposited Cas9, which led to embryo resistance and reduced fertility. Through additional fertility assays and modeling, the team confirmed that the origin and timing of Cas9 expression, particularly from mothers, significantly impacted drive success. Surprisingly, even when Cas9 was driven by promoters with supposedly low somatic activity, such as nanos, fitness still persisted. The study revealed that while gene drives can be powerful, their effectiveness relies on finely balanced factors like promoter choice, drive architecture, and gene function. Overall, the research offers valuable lessons for designing robust, next-generation gene drives aimed at ecological pest control.

-We sincerely appreciate the reviewer’s positive and thoughtful comments. We agree that the points raised highlight the importance of our findings and hope that our revisions have further improved both the clarity and overall content of the manuscript.

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Referee #3

Evidence, reproducibility and clarity

In this study, Xu and colleagues explored how CRISPR-based homing gene drives could be used to suppress insect populations by targeting female fertility genes in Drosophila melanogaster. They engineered split gene drives with multiplexed guide RNAs to target nine candidate genes, seeking to prevent functional resistance and achieve high drive conversion with minimal fitness costs.

Here my comments about this work:

Abstract: While the stated aim of the study on line 16 is to "maintain high drive conversion efficiency with low fitness costs in female drive carriers," the conclusion in lines 29-31 shifts focus toward the broader challenges and future optimization of gene drive systems. This conclusion does not clearly highlight the specific results of the study or how they relate directly to the original objective. It would be more effective to emphasize the actual findings, such as which target genes performed best and under what conditions, and how these findings support or contradict the stated goals. The study primarily aimed to assess the efficiency of specific female fertility genes and to evaluate strategies for minimizing the formation of functional resistance alleles, rather than proposing a protocol for optimization. Therefore, better alignment is needed between the study's aim, experimental design, and concluding statements. Clarifying this alignment would also help refine the paper's focus and more accurately communicate its contribution, including whether it is exploratory, comparative, or methodologically driven.

Introduction: One of the key design elements in this study is the use of multiplexed gRNAs. It is reasonable to assume that this strategy may influence fitness costs, potentially in more than one way. Given that assessing fitness cost is a major focus of the study, it would be helpful to include a brief discussion of previous research examining how multiplexed gRNAs may impact fitness in gene drive systems. A short review of relevant studies, if available, would provide important context for interpreting the results and could help clarify whether any observed fitness costs might be attributed, at least in part, to the multiplexing strategy itself. This addition could be appropriately placed around line 102, where gRNA design is discussed.

Line 42: Cas12a also showed efficacy using gene drives in yeast and Drosophila.

Line 133: The paragraph begins by stating that homologs of the target genes were identified and aligned. To improve clarity, especially for readers who are new to gene drive research, it would be helpful to begin the paragraph with a brief introductory sentence explaining the purpose of this step. For example, you could state the importance of identifying and aligning homologs to assess the conservation of target sites across species, which is critical for evaluating the broader applicability of gene drive strategies. This context would guide the reader and clarify the relevance of the analysis.

Lines 144-145: You mention that "the exception was tra, for which two constructs containing different gRNA sets were generated." For clarity, it would be helpful to provide a brief explanation of why two different gRNA sets were used for tra, and whether this differs from the approach taken with the other target genes. It's currently unclear whether all other genes were targeted using a single, standardized set of gRNAs, and this should be explicitly stated here for consistency, even though it is mentioned later in the plasmid construction section. Additionally, I suggest combining the sections on gRNA target design and plasmid construction. Since these components are closely related and sequential in the experimental workflow, presenting them together would improve the logical flow and help readers follow the methodology more smoothly.

Line 210: The analysis of the cage experiments was based on models from previous studies that used a simplified assumption of a single gRNA at the target site. While I understand this approach has precedent, it raises important questions about potential limitations. Specifically, could simplifying the analysis to one gRNA affect the conclusions of this study, given that the experimental design involves multiplexed gRNAs with four distinct target sites? The implications of using this simplified model should be clearly addressed, as the dynamics of drive efficiency, resistance formation, and fitness effects may differ when multiple gRNAs are employed. Additionally, while I am not a statistician, it is worth asking whether more sophisticated modeling approaches could be applied to account for all four gRNAs, rather than reducing the system to a single-gRNA framework. A discussion of the modeling choices and their potential consequences would strengthen the interpretation of the results.

Lines 297-300: Your results show that the expression of all target genes was higher in females, except for oct, which had higher expression in males. Additionally, oct expression decreased in adults. Given that oct is functionally important for ovulation and fertilization, processes that are primarily required in adult females, this pattern is somewhat unexpected. Could there be a possible explanation for the lower expression of oct, particularly in females and especially in adults, where its function would presumably be most critical? A brief discussion or hypothesis addressing this discrepancy would help clarify the biological relevance and interpretation of the expression data.

Lines 346-347: What is the distance between the gRNA target sites within each gene? Are all of the gRNAs confirmed to be active? It would be valuable to include a table summarizing the distance between target sites for each gene, the activity levels of the individual gRNAs, and the corresponding homing rates. This would help determine whether there is a correlation between gRNA spacing and drive efficiency. For example, Lopez del Amo et al. (Nature Communications, 2020) demonstrated that even a 20-nucleotide mismatch at each homology arm can significantly reduce drive conversion. Including such a comparative analysis in your study could provide important insights into how gRNA arrangement influences overall drive performance and would be incredibly helpful for future multiplexing designs.

Line 434: I was not able to find any sequencing data. This is important to evaluate gRNA activities and establish correlations with drive efficiency.

Line 482: Did the authors test Cas9-only individuals (without the drive) against a wild-type population? This would help determine whether Cas9 alone has any unintended fitness effects. Additionally, is Cas9 expression stable over time and across generations? It would be helpful to include any observations or thoughts on the long-term stability and potential fitness impact of Cas9 in the absence of the drive element.

Discussion: I would appreciate a more direct and clearly stated conclusion that summarizes the key findings of the study. While the discussion addresses the main outcomes in depth, presenting a concise concluding paragraph, either at the end of the discussion or as a standalone conclusion section, would provide a stronger and more definitive closing statement. This would help reinforce what the study ultimately achieved and ensure the main takeaways are clearly communicated to the reader.

Overall, I believe this is an important study that offers valuable insights for advancing the design of CRISPR-based gene drives. The findings contribute to the development of more efficient and practical gene drive prototypes, bringing the field closer to real-world applications.

Significance

In this study, Xu and colleagues explored how CRISPR-based homing gene drives could be used to suppress insect populations by targeting female fertility genes in Drosophila melanogaster. They engineered split gene drives with multiplexed guide RNAs to target nine candidate genes, seeking to prevent functional resistance and achieve high drive conversion with minimal fitness costs. Among the targets, the stall (stl) and octopamine β2 receptor (oct) genes performed better, showing the highest inheritance rates in lab crosses. When tested in population cages, the stl drive was able to completely eliminate a fly population, but only when released at a high enough frequency, while other cages failed. These failures were traced and explained by fitness cost in drive-carrying females, caused largely by maternally deposited Cas9, which led to embryo resistance and reduced fertility. Through additional fertility assays and modeling, the team confirmed that the origin and timing of Cas9 expression, particularly from mothers, significantly impacted drive success. Surprisingly, even when Cas9 was driven by promoters with supposedly low somatic activity, such as nanos, fitness still persisted. The study revealed that while gene drives can be powerful, their effectiveness relies on finely balanced factors like promoter choice, drive architecture, and gene function. Overall, the research offers valuable lessons for designing robust, next-generation gene drives aimed at ecological pest control.

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Referee #2

Evidence, reproducibility and clarity

Paper summary

The manuscript by Xu. et al presents an insightful and valuable contribution to the field of gene drive research. The manuscript by Xu et al. presents an insightful and valuable contribution to the field of gene drive research. The strategy of targeting and disrupting female fertility genes using selfish homing genetic elements was first proposed by Burt in 2003. However, for this approach to be effective, the phenotypic constraints associated with gene disruption have meant that the pool of suitable target genes remains relatively small - notwithstanding the significant expansion in accessible targets enabled by CRISPR-based genome editing nucleases. Population suppression gene drives are well developed as proof-of-principle systems, with some now in the late stages of development as genetic control strains. However, advancing the pipeline will require a broader set of validated target genes - both to ensure effectiveness across diverse species and to build redundancy into control strategies, reducing reliance on any single genetic target. In their paper, the authors conduct a systematic review of nine female fertility genes in Drosophila melanogaster to assess their potential as targets for homing-based suppression gene drives. The authors first conduct a thorough bioinformatic review to select candidate target genes before empirically testing candidates through microinjection and subsequent in vivo analyses of drive efficiency, population dynamics, and fitness costs relating to fecundity and fertility. After finalising their results, the authors identify two promising candidate target genes - oct and stl - which both demonstrate high gene conversion rates and, regarding the latter, can successfully suppress a cage population at a high release frequency. However, the manuscript suffers from a lack of in-depth discussion of a key limitation in its experimental design - namely, that the authors utilise a split-drive design to assess population dynamics and fitness effects when such a drive will not reflect release scenarios in the field. The review below highlights some major strengths and weaknesses of the paper, with suggestions for improvement.

Key strengths

The study's most significant strength is in its systematic selection and empirical testing of nine distinct genes as targets for homing-based gene drive, hence providing a valuable resource that substantially expands the pool of potential targets beyond the more commonly studied target genes (e.g. nudel, doublesex, among others). The identification of suitable target genes presents a significant bottleneck in the development of gene drives and the work presented here provides a foundational dataset for future research. The authors bolster the utility of their results by assessing the conservation of candidate genes across a range of pest species, suggesting the potential for broader application. A key finding in the paper is the successful suppression of a cage population using a stl-targeting gene drive (albeit at a high release frequency). This provides a critical proof-of-principal result demonstrating that stl is a viable target for a suppression drive. While in the paper suppression was not possible at lower release frequencies, together, the results provide evidence for complex population dynamics and threshold effects that may govern the success or failure of a gene drive release strategy - hence moving the conversation from a technical perspective ("can it work") to how a gene drive may be implemented. Moreover, the authors also employ a multiplexed gRNA strategy for all their gene drive designs and in particular their population suppressive gene drive targeting stl. This provides further proof-of-principal evidence for multiplexed gRNAs in order to combat the evolution of functional resistance following gene drive deployment. Finally, a further strength of this paper is in the clever dissection of fitness effects resulting from maternal Cas9 deposition. The authors design and perform a robust set of crosses to elucidate the parental source of fitness effects (i.e. maternally, paternally, or biparentally derived Cas9), finding (as they and others have before) that embryonic fitness was significantly reduced when Cas9 was inherited from a maternal source. As discussed, the authors conclude that maternal deposition is particularly pronounced in the context of split drives as opposed to complete drives, with the implication being that a complete drive might succeed where a split-drive has failed; thus providing a key directive for future study.

Concerns

The manuscript's central weakness lies in its interpretation of the results from the cage experiments - namely that a split-drive system was used to "mimic the release of a complete drive". In the study, mosquitoes carrying the drive element (i.e. the gRNA) were introduced into a population homozygous for the Cas9 element over several generations. This design is likely not representative of a real-world scenario and, as the authors state, likely exaggerates fitness costs. This is because the females carrying Cas9 will maternally deposit Cas9 protein into her eggs, with activity spanning several generations. When mated with a drive-carrying male the gRNA will immediately co-exist with maternally deposited Cas9, leading to early somatic cleavage and significant fitness costs (reflected in the author's own fertility crosses). This is fundamentally different to how a complete drive would function in a real-world release, where complete-drive males would mate with wild-type females not carrying Cas9. Their offspring would carry the drive element but would not be exposed to maternally deposited cas9, thus deleterious maternal effects would only begin to appear in the subsequent generation from females carrying the drive. Fitness costs measured from split-drive designs are therefore likely substantially overestimated compared to what would occur during the initial but critical release phase of a complete drive. This flaw weakens the paper's ability to predict the failure or success of the screened targets in a complete drive design, thus weakening the interpretation of the results from the cage trials. As a suggestion for improvement, the authors should explicitly and more prominently discuss the limitations of their split-drive model compared to complete drive models, both in the Results and Discussion. It is also recommended to include a schematic for both strategies that contrasts the experimental setup design (i.e. release of the drive into a Cas9 homozygous background) with a complete-drive release, clearly illustrating differences in maternal deposition pathways. This will not only contextualise the results and support the author's conclusion that observed fitness costs are likely an overestimate but will further strengthen the arguments that the candidate target genes found in this study may still be viable in a complete-drive system.

A second weakness in the manuscript relates to its limited explanation and discussion of key concepts. For example, the manuscript reports a stark difference in outcome of the two stl-targeting drives, where a high initial release in cage 1 led to population elimination versus a failure of the drive to spread in cage 2. The authors attribute this to vague "allele effects" and stochastic factors such as larval competition; however the results appear reminiscent of the Allee effect, which is a well-characterised phenomenon describing the correlation of population size (or density) and individual fitness (or per capita population growth rate). Using their results as an example, is it plausible that the high-frequency initial release in cage 1 imposed enough genetic load to quickly drive the population density below the Allee threshold thus quickly leading to population eradication. In cage 2, the low-frequency at initial release was insufficient to cross the Allee threshold. Omitting mention of this ecological principal greatly weakens the Discussion, and further presents a missed opportunity to discuss one of the more crucial strengths of the paper - that is, in providing a deeper insight into the practical requirements for successful field implementation. In a similar vein, the authors provide only a superficial mechanistic discussion into the fitness costs associated with drives targeting key candidate genes. The paper would benefit from a deeper discussion regarding the specific molecular functions of top-performing genes (stl, oct, nox) and how unintended Cas9 activity could disrupt their activity, integrating known molecular functions with observed fitness costs. For instance, oct encodes a G-protein coupled receptor essential for ovulation and oviduct muscle relaxation, thus disruption to the oct gene would directly impair egg-laying which would account for the observed phenotypic effects. A deeper discussion linking unintended Cas9 activity to the specific, sensitive functions of target genes would elevate the paper from a descriptive screen to a more insightful mechanistic study.

It is curious that the authors chose two genes on the X chromosome as targets. In insects (such as Drosophila here) that have heterogametic sex chromosomes, homing is not possible in the heterogametic sex as there is no chromosome to home to - so there will be no homing in males. On top of that, there is usually some fitness effect in carrier (heterozygous) females, so in a population these are nearly always bad targets for drives - unless there is some other compelling reason to choose that target?

Minor comments

• Enhanced clarity in the Figures and data presentation would greatly improve readability. For example, Figure 5 is critical yet difficult to interpret; consider changing x-axis labels from icons to explicit text (e.g. "biparental Cas9", "maternal cas9", "paternal Cas9"). Similarly, Figure 4 is difficult to read and the y-axis label "population size" is ambiguous; consider adding shapes or dashes (rather than relying solely on colour) and clarifying the y-axis (e.g. no. adults collected) in the legend.
• Expand on or include a schematic to show the differences in construction between the tra-v1 and tra-v2 constructs to better contextualise the discrepancies in results (e.g. inheritance rates of 61%-66% for tra-v1 and 81%-83% for tra-v2 between the two.
• Minor typos e.g.:
  • Line 87: "form" to "from"
  • Line 484: "expended" to "expanded
  • Line 560: "foor" to "for"
  • Line 732: "conversed" to "conserved
• Clarify the split drive system: the authors introduce split drive for the first time in Line 118. They should at least give a clear definition and explanation of split drive and complete drive in the introduction.
• Line 237-238., The fitness evaluation lacks a clear description of controls. How were non-drive flies generated and validated as controls?
• Line 409-412.,line 423.,The high inheritance rates of stl and oct drives are impressive; however, variation in results across Cas9 promoters should be explained further in the discussion.
• Line 414: The CG4415 promoter yielded reduced drive conversion rates in females, yet is still referred to as a promising promoter. This conclusion seems optimistic and should be clarified/more justified.
• Specify the number of flies released, sex ratio, and cage size per generation (Line 466). This is essential for reproducibility.

Significance

Overall the manuscript presents a valuable and timely resource for gene drive research, in particular for its systematic appraisal of potential target genes for population suppression drives and its rigorous assessment of the impact of maternal Cas9 deposition. The value in the generation and empirical testing of a novel multiplexed stl-targeting gene drive that led to population eradication in a cage trial should not be understated. While several key aspects of the discussion of the manuscript should be strengthened, the study presents a meaningful contribution to the field, extending previous work and and outlines important considerations for the design and implementation of effective gene drive systems.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Xu et al. investigated split gene drive systems by targeting multiple female essential genes involved in fertility and viability in Drosophila. The authors evaluate the suppression efficiency through individual corsses and cage trials. Resistance allele formation and fitness costs are explored by examining the sterility and fertility of each line. Overall, the experimental design is sound and methods are feasible. The work is comprehensive, and conclusions are well supported by the data. This work offers informative insights that could guide the design of suppression gene drive systems in other invasive disease vectors or agricultural pests.

However, several points requiring clarification or improvement:

1. Methodological clarity: Some experimental details are indufficiently described, for example, regarding the setup of genetic crosses involving different Cas9 derivatives. In line 197-198, "the mated females, together with females that were mated with Cas9 only males", it is unclear whether the latter group refers to gRNA-females.
2. Regarding the inheritance rates, you included the reverse orientation of CG4415-Cas9, as I understood, it means this component is in reverse orientation with fluorescent marker. Since it is standard to design adjacent components in opposite direction to avoid transcriptional interference, the rationale for including this comparison should be better justified.
3. Embryo resistance is inferred from the percentage of sterile drive females derived from drive mothers. How many female individuals were analysed per line and why deep sequencing was not employed to directly detect resistance alleles.
4. Masculinisation phenotypes were observed upon disruption of tra gene. How strong intersexes were distinguished from males? What molecular markers were used to determine genetic sex. This information should be clearly provided.
5. It would be more appropriate to use "hatchability"rather than "fertility" when referring to egg-to-larva viability.
6. In cage trials, a complete gene drive is mimicked by introducing Cas9 to the background population, but this differs from actual complete gene drive, due to potential effects from separate insertion sites (different chromosome or loci). These difference could impact the system's performance and should be discussed.
7. Given the large amount of data presented, it would improve readability and interpretation if each result section concluded with a concise summary highlighting the key findings and implications.

Significance

The authors evaluate suppression efficiency through individual courses and cage trials. Resistance allele formation and fitness costs are explored by examining the sterility and fertility of each line. Overall, the experimental design is sound and methods are feasible. The work is comprehensive, and conclusions are well supported by the data. This work offers informative insights that could guide the design of suppression gene drive systems in other invasive disease vectors or agricultural pests.

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Reply to the reviewers

• *

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

• *We appreciate the reviewers' assessment of the significance of our work and would like to highlight where we believe the novelty of this study lies. Our findings identify E4BP4 as a key transcription factor that maintains mitochondrial homeostasis by restraining the overactivation of biological pathways - such as de novo ceramide synthesis - that are known to drive mitochondrial oxidative dysfunction in the context of obesity. We fully acknowledge that the link between C16:0 ceramide and mitochondrial fragmentation has been previously established. However, to our knowledge, our study is the first to connect this phenomenon to a transcriptional safeguard mechanism, thereby providing a new layer of understanding of how transcription factors preserve mitochondrial integrity and function in brown adipocytes. We believe this conceptual advance adds significant value to the field by framing E4BP4 as a transcriptional "guardian" of mitochondrial homeostasis.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

• *Reviewer #1 comment:

Figures B: Sample size of EE experiments is too low to draw any meaningful conclusions or to know for certain if the data are reproducible. Small sample sizes, likely coming from one litter and one batch of AAV are prone to type I error.

Response: We agree with reviewer observation that increasing sample size is essential to confirm reproducibility and robustness. We have therefore planned to repeat the EE experiments with a larger number of mice per group, derived from independent litters and AAV preparations, in order to strengthen the statistical power and validate the phenotype observed in the current study.

Reviewer #1 comment:

Figure 3I: Why do cells (none of the groups) show no response to NE stimulation? Please clarify or provide potential mechanistic insight. Perhaps the cells were not differentiated well.

__ ____Response:__ We agree that the absence of a robust NE response in Figure 3I requires further clarification. To address this, we have planned to repeat the in vitro oxygen consumption assay to confirm the phenotype presented in the study.

Reviewer #1 comment: Figures 3I vs 5N. There is a striking discrepancy between these panels. In both, cells were treated with palmitate for 6 h, yet the NE and CCCP responses differ significantly. Are these the same cell types and conditions? Please reconcile the differences.

Response: We would like to clarify that Figures 3I and 5N represent different experimental systems: Figure 3I shows data from primary brown adipocytes with E4bp4 transgene overexpression, whereas Figure 5N shows data from immortalized brown adipocytes with Cas9-mediated mutation of a 65 kb Cers6 enhancer site. Given the distinct cell types and genetic manipulations, a direct comparison between these two panels is not appropriate. Nevertheless, we agree that confirming the consistency of the phenotype across systems is important. To address this, we have planned to repeat oxygen consumption assays in both models to further validate the reproducibility of the observed effects.

Reviewer #2 comment: A key experiment is missing: does adding C16:0 block the mitochondrial benefits of E4BP4-OE?

Response: We thank the reviewer for this excellent suggestion. We agree that a rescue experiment is important to directly test whether C16:0 affects the mitochondrial benefits of E4BP4. To address this, we have planned to perform a co-overexpression of E4bp4 and Cers6 in brown adipocytes. The readouts will include mitochondrial morphology and oxygen consumption, enabling us to determine whether restoration of C16:0 production mitigates the protective mitochondria effects of E4BP4 overexpression. This experiment will provide direct mechanistic confirmation of the proposed model.__ __

__Reviewer #2 comment: __Whether PRDM16-OE mimics the effects of E4BP4 to induce p-Drp1 is not shown.

__Response: __We thank the reviewer for this valuable suggestion. We agree that testing whether PRDM16 overexpression mimics the effects of E4BP4 on p-Drp1 is important to strengthen the mechanistic link between these transcription factors in terms of regulation of mitochondrial fragmentation. To address this, we have planned to include a Western blot analysis of p-Drp1 in the PRDM16-OE in brown adipocytes.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

• *Reviewer #1 comment:

Figure 1F: There is an unexpected dip in gene expression at cold exposure days 3 and 7, followed by a rebound at day 14. Is this fluctuation biologically meaningful or technical?

Response: We thank the reviewer for this thoughtful observation. A previous study demonstrated that E4bp4 (Nfil3) expression displays an early increase (at 2 hours), followed by a decrease in magnitude - while still remaining significantly higher than control - during beige adipocyte differentiation in response to forskolin treatment (DOI: 10.1016/j.molmet.2022.101619). The authors of that study suggested that E4bp4 may contribute to a second wave of cAMP-driven beige adipocyte differentiation. However, in the context of our work, further discussion on whether the fluctuations in BAT E4bp4 expression observed during cold exposure reflect biological regulation would be speculative. Importantly, despite these oscillations across time points, E4bp4 expression remained statistically significant compared with control, supporting the robustness of our findings. We have now introduced this observation in the Results section of the revised manuscript.

Reviewer #1 comment: Figures 2H and 2I (GTT): How was the AUC calculated? The GTT and ITT curves appear largely parallel aside from fasting differences. If total AUC was used instead of incremental AUC, it may overstate group differences. The recommended method is outlined in [DOI: 10.1038/s42255-021-00414-7]. Also, since insulin's half-life is ~10 minutes, later differences in the ITT curve likely reflect counterregulatory responses driven by hepatic gluconeogenesis.

Response: We would like to clarify that in our original manuscript we had already calculated the area of the curve (AOC) rather than the area under the curve (AUC), following the recommended approach (DOI: 10.1038/s42255-021-00414-7). Specifically, the AOC was derived by subtracting the baseline glucose value from each subsequent time point, ensuring that the analysis reflects incremental changes rather than absolute glucose levels. We have now made this description more explicit in the revised version to avoid any ambiguity.

__Reviewer #1 comment: __Figure 4F: How was mitochondrial fragmentation quantified? Please ensure that the ROI boxes shown in zoomed panels match the same region in size and shape - this applies throughout the manuscript.

__ _Response: _We thank the reviewer for this valuable comment. To improve the quality and interpretation of the data, we have now included a quantitative analysis of mitochondrial morphology parameters associated with Figure 4F (Figure S4B)__. Specifically, we analyzed:

• Mitochondrial volume (µm³): reflecting overall mitochondrial size.
• Surface area (µm²): reflecting membrane expansion.
• Sphericity index: indicating morphological rounding, which increases with fragmentation.
• Number of branches and branch junctions per mitochondrion: reflecting mitochondrial networking and fusion. Myriocin treatment preserved mitochondrial volume and surface area, reduced sphericity, and increased both the number of branches and branch junctions, reflecting maintenance of a more interconnected mitochondrial network.

Additionally, we verified that the ROI boxes shown in the zoomed panels are consistent in both size and shape across groups, as requested. We have now introduced this observation in the Methods section of the revised manuscript.

__ ____Reviewer #1 comment: __Figure 3A: The claim that one group contains smaller mitochondria is not convincing. Both small and elongated mitochondria appear in each group. Moreover, it is unclear whether these minor differences are of any physiological relevance or whether they drive phenotypes.

Response: We respectfully disagree with this observation and would like to clarify a few points.

1. We have already demonstrated a statistically significant difference in mitochondrial length between E4bp4-OE and control groups (Figures 3B and 3C). This was based on a random, unbiased analysis, which consistently confirmed longer mitochondria in E4bp4-OE compared with control.

Some degree of variability in mitochondrial length is expected in electron microscopy analyses, particularly because mitochondria from multiple cell types within iBAT are captured. It is important to note that the protective action of E4bp4 against mitochondrial fragmentation occurs specifically in brown adipocytes, where the transgene is expressed under the control of the adiponectin promoter.

To address the potential confounding heterogeneity of iBAT mitochondria, we performed complementary cell-autonomous analyses in vitro, allowing us to directly compare mitochondrial dynamics in E4bp4-OE versus control brown adipocytes. This analysis further confirmed that E4bp4-OE prevents lipid overload - induced mitochondrial fragmentation in brown adipocytes.

Finally, we emphasize that several studies have demonstrated that changes in mitochondrial dynamics, particularly under high-fat diet conditions, disrupt systemic energy homeostasis (DOI: 10.1016/j.cmet.2017.05.010; DOI: 10.1016/j.cell.2019.05.008; DOI: 10.1038/s42255-024-00978-0). Therefore, the differences we report are biologically meaningful in the broader context of mitochondrial dynamics and metabolic disease.

__Reviewer #1 comment: __Figure 3E: The claim that confocal microscopy reveals palmitate-induced mitochondrial fragmentation is difficult to discern. The images lack clear morphological differences.

__ _Response: _We thank the reviewer for this observation. To improve the interpretation of these results, we have now included a quantitative analysis of mitochondrial morphology parameters associated with Figure 3E.__ Specifically, we measured:

• __Mitochondrial volume (µm³): __reflecting overall mitochondrial size.
• __Surface area (µm²): __reflecting membrane expansion.
• __Sphericity index: __indicating morphological rounding, which increases with fragmentation.
• Number of branches and branch junctions per mitochondrion: __reflecting mitochondrial networking and fusion. __ __As shown in the new analysis (Figure S4A)__, palmitate treatment reduced mitochondrial volume, surface area, branches, and branch junctions, while increasing sphericity, consistent with a more fragmented phenotype in control cells. In contrast, these effects were significantly attenuated in E4bp4-OE cells, supporting our conclusion that E4BP4 overexpression protects against lipid overload-induced mitochondrial fragmentation. This text was added in the Results section of the revised manuscript.

We believe this additional analysis strengthens the robustness of our findings and provides clear quantitative evidence for the morphological changes that were less apparent from qualitative image inspection alone.

__Reviewer #1 comment: __Figure 3G: Dendra2-labeled mitochondria appear unaffected by palmitate, raising concern about the robustness of the effect across readouts.

__ _Response: _We respectfully disagree with this observation. As shown in Figure 3G__ (bar graphs), palmitate-treated brown adipocytes exhibited a clear reduction in mitochondrial co-localization, which reflects lower levels of fused mitochondria, in the control group compared with E4bp4-OE. Importantly, no difference in mitochondrial co-localization was observed between the two groups under vehicle-treated conditions. This indicates that E4bp4 overexpression does not promote mitochondrial fusion per se, but rather prevents lipid overload - induced mitochondrial fragmentation. We also note that the representative images presented in Figure 3G are single snapshots taken from a time-lapse assay of mitochondrial dynamics. To further illustrate this effect, we direct the reviewer to the supplementary video accompanying this experiment, which clearly demonstrates the differences in mitochondrial behavior over time.

__ ____Reviewer #1 comment: __Figure 5H: Were E4BP4 expression levels equivalent between WT and mutant cells? Quantification should be shown. Figure 5H: Were E4BP4 expression levels equivalent between WT and mutant cells? Quantification should be shown.

Response: __We thank the reviewer for this important point. We have now added the quantification of E4bp4 mRNA levels in cells transduced with either the non-mutated vector (control) and the vector carrying a mutation in the E4bp4 DNA-binding domain (Figure S5)__. The data show no significant difference in E4bp4 expression between the two groups.

__Reviewer #2 comment: __The evidence of mitochondrial fragmentation is not convincing. In the reviewer's opinion, Figures 3E, 3G, 4F, and 5M demonstrated a decrease in mitochondrial quantity, but not fragmentation.

Response: __We thank the reviewer for this observation. We have already addressed the comments from reviewer #1 (above) regarding Figures 3E, 3G and 4F related to measurements of mitochondria fragmentation. To strengthen the interpretation of these results, we have also performed a quantitative analysis of mitochondrial morphology parameters associated with __Figure 5M. Specifically, we measured:

• __Mitochondrial volume (µm³): __reflecting overall mitochondrial size.
• __Surface area (µm²): __reflecting membrane expansion.
• __Sphericity index: __indicating morphological rounding, which increases with fragmentation.
• Number of branches and branch junctions per mitochondrion: __reflecting mitochondrial networking and fusion. As shown in the new analysis (Figure S4C), palmitate treatment significantly reduced mitochondrial volume, surface area, and branching, while increasing sphericity, consistent with enhanced mitochondrial fragmentation in control cells. Notably, these changes were significantly blunted in the Cers6 enhancer edited cells (EΔ), supporting our conclusion that disruption of Cers6 protects against lipid overload-induced mitochondrial fragmentation. __This text was added in the Results section of the revised manuscript.

Regarding the reviewer's understanding of a "decrease in mitochondrial quantity, but not fragmentation," we respectfully disagree. The analyses performed for Figures 3E, 3G, 4F, and 5M clearly demonstrate that E4bp4 overexpression (E4bp4-OE) prevents lipid overload -induced mitochondrial fragmentation.

In relation to mitochondrial quantity, our data do not support differences in mitochondrial biogenesis between groups. Specifically, the expression of thermogenic and mitochondrial biogenesis genes (Figure S2G) as well as the mitochondrial-to-nuclear DNA ratio (Figure S3D) showed no significant changes, indicating that mitochondrial biogenesis is not altered.

Alternatively, it is possible that E4bp4 prevents mitophagy, as our results (Figure 3H) show that E4bp4-OE protects against lipid overload-induced mitochondrial depolarization. In this regard, previous studies have demonstrated that fragmented and depolarized mitochondria are targeted for degradation through mitophagy (DOI: 10.2337/db07-1781; DOI: 10.1074/jbc.M111.242412). While this explanation is consistent with our findings, we acknowledge that it remains speculative at this stage and, although interesting, is beyond the scope of the current study.

__Reviewer #2 comment: __It is confusing whether the association shown in Figure 1C is a positive or an inverse association.

Response: __We thank the reviewer for pointing out this source of confusion. __Figure 1C represents common variant associations for E4BP4, where the y-axis indicates the strength of association (-log10 p-value) rather than the direction (positive or inverse) of the effect. We have clarified this in the revised manuscript to avoid misinterpretation. The associations indicate that genetic variants in E4bp4 are positively linked with anthropometric traits such as weight, BMI, and waist-hip ratio.

5. Description of analyses that authors prefer not to carry out

*Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. *

This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

• *Reviewer #2 comment:

It would be worthwhile to investigate whether in vivo knockdown of E4BP4 blunts the Cers6-suppressing effects of PRDM16-OE.

Response: We agree that assessing in vivo loss-of-function of E4bp4 in the context of Prdm16 overexpression would be highly informative. At present, this experiment is technically not feasible, as it would require the generation and characterization of complex in vivo models beyond the scope of the current study. Nevertheless, we are actively considering this as a future direction. In the meantime, we believe that the in vitro experiments in brown adipocytes provided here are sufficient to establish the mechanistic relationship between E4BP4 and PRDM16 in the regulation of Cers6 expression.

__Reviewer #2 comment: __Whether E4BP4-OE affects cold tolerance in mice is now shown.

__Response: __We thank the reviewer for this thoughtful comment. In our study, we performed an iBAT-specific E4bp4 gain-of-function assay because we observed a downregulation of E4bp4 expression in the context of obesity. The rationale for this approach was to rescue E4bp4 expression in iBAT and thereby evaluate its systemic and mechanistic effects under obesogenic conditions. We recognize that a gain-of-function assay during cold challenge would further enhance E4bp4 expression and, while interesting, this would more directly address the role of E4bp4 in thermogenic regulation rather than in obesity-related metabolic dysfunction. For this reason, we believe that a detailed investigation of E4bp4 in cold-induced thermogenesis is an important but separate question that lies beyond the scope of the current study.

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Referee #2

Evidence, reproducibility and clarity

Summary: The manuscript by Valdivieso-Rivera et al. investigated the role of a transcription factor, E4BP4, in brown fat functions. Using in vivo AAV gain-of-function studies, in vitro primary cultured brown adipocytes, and transcription regulation studies, authors identified that E4BP4 works together with PRDM16 to suppress Cers6 transcriptions and its derived ceramide C16:0 production. The resulted decreasing C16:0 prevents diet-induced mitochondrial fragmentation within brown adipocytes, thereby promoting brown fat functions. Overall, this study employed state-of-the-art methodologies and the collected evidence generally supported the conclusion. However, there are issues remaining to be addressed.

Major Comments:

1. The evidence of mitochondrial fragmentation is not convincing. In the reviewer's opinion, Figures 3E, 3G, 4F, and 5M demonstrated a decrease in mitochondrial quantity, but not fragmentation.
2. Whether E4BP4-OE affects cold tolerance in mice is now shown.
3. A key experiment is missing: does adding C16:0 block the mitochondrial benefits of E4BP4-OE?
4. Whether PRDM16-OE mimics the effects of E4BP4 to induce p-Drp1 is not shown.

Minor points:

1. It is confusing whether the association shown in Figure 1C is a positive or an inverse association.
2. Results from the PRDM16-OE model were mostly obtained in cultured brown adipocytes. It would be worthwhile to investigate whether in vivo knockdown of E4BP4 blunts the Cers6-suppressing effects of PRDM16-OE.

Cross-commenting

Reviewer #1's comments are all solid, and I agree with all of them.

Significance

Key strengths include state-of-the-art methodologies and detailed mechanistic studies. Key limitations include some unconvincing staining data, lack of key "rescue" experiments, and less novelty in molecular mechanisms (the ceramide-Drp1 pathway).

Overall, this study uncovers a critical role of E4BP4 in maintaining brown adipocyte mitochondrial integrity and function, advancing our understanding of TFs in brown fat biology. This study well fits readers' interests in the adipose biology and metabolism field.

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Referee #1

Evidence, reproducibility and clarity

Summary of the key results:

Valdivieso-Rivera and colleagues present a novel regulatory mechanism by which E4BP4 modulates C16:0 ceramide production in brown adipocytes. Several points warrant clarification or additional data.

Suggested improvements:

1) Figure 1F: There is an unexpected dip in gene expression at cold exposure days 3 and 7, followed by a rebound at day 14. Is this fluctuation biologically meaningful or technical?

2) Figures B: Sample size of EE experiments is too low to draw any meaningful conclusions or to know for certain if the data are reproducible. Small sample sizes, likely coming from one litter and one batch of AAV are prone to type I error.

3) Figures 2H and 2I (GTT): How was the AUC calculated? The GTT and ITT curves appear largely parallel aside from fasting differences. If total AUC was used instead of incremental AUC, it may overstate group differences. The recommended method is outlined in [DOI: 10.1038/s42255-021-00414-7]. Also, since insulin's half-life is ~10 minutes, later differences in the ITT curve likely reflect counterregulatory responses driven by hepatic gluconeogenesis.

4) Figure 3I: Why do cells (none of the groups) show no response to NE stimulation? Please clarify or provide potential mechanistic insight. Perhaps the cells were not differentiated well.

5) Figure 4F: How was mitochondrial fragmentation quantified? Please ensure that the ROI boxes shown in zoomed panels match the same region in size and shape - this applies throughout the manuscript.

5) Figures 3I vs 5N: There is a striking discrepancy between these panels. In both, cells were treated with palmitate for 6 h, yet the NE and CCCP responses differ significantly. Are these the same cell types and conditions? Please reconcile the differences.

6) Figure 3A: The claim that one group contains smaller mitochondria is not convincing. Both small and elongated mitochondria appear in each group. Moreover, it is unclear whether these minor differences are of any physiological relevance or whether they drive phenotypes.

7) Figure 3E: The claim that confocal microscopy reveals palmitate-induced mitochondrial fragmentation is difficult to discern. The images lack clear morphological differences.

8) Figure 3G: Dendra2-labeled mitochondria appear unaffected by palmitate, raising concern about the robustness of the effect across readouts.

9) Figure 5H: Were E4BP4 expression levels equivalent between WT and mutant cells? Quantification should be shown. Figure 5H: Were E4BP4 expression levels equivalent between WT and mutant cells? Quantification should be shown.

Cross-commenting

I agree with R2's points

Significance

This advance is incremental for the basic science community.

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Reply to the reviewers

Manuscript number: RC-2025-03098

Corresponding author: Pedro Escoll

1. General Statements

Our study investigates the interplay between the metabolism of host cells and the intracellular replication of Salmonella enterica serovar Typhimurium (ST). Type III Secretion Systems (T3SSs) are considered essential for ST to replicate within macrophages. However, we found that restricting macrophages to different bioenergetic contexts, such as supplementing them with glycerol, modulates bacterial replication and remarkably, enables a T3SS-deficient ST mutant (ΔprgH/ΔssaV) to replicate intracellularly. This T3SS-independent replication occurs within the Salmonella-containing vacuole (SCV) and is driven by the capacity of the host cell to provide these preferred nutrients, rather than by the host glycolytic activity itself.

2. Description of the planned revisions

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

Summary:

In this manuscript, the authors investigate how host cell metabolic heterogeneity influences the intracellular replication of Salmonella enterica serovar Typhimurium. They use live-cell imaging of infected human primary macrophages to reveal that bacterial replication does not occur uniformly across infected cells. They demonstrate that supplementation with specific carbon sources-used by Salmonella during infection-promotes bacterial replication and increases the proportion of macrophages supporting intracellular growth. These effects are seen even in the absence of functional Type III Secretion Systems (T3SS), using a ΔprgH/ΔssaV double mutant. The authors further suggest that this replication enhancement is not strictly dependent on host glycolytic activity but rather on the host cell's ability to import nutrients. Their findings imply that intracellular Salmonella can exploit host cell metabolism to grow, even without its canonical virulence secretion systems, under nutrient-favorable conditions.

Major Concern:

While the topic is potentially interesting, the novelty is not fully clear. The concept that nutrient availability impacts intracellular Salmonella replication, largely via T3SS2 function, has been addressed previously (e.g., Liss et al., 2017). The finding that added exogenous carbon sources can enhance bacterial growth is thus not unexpected. The key claim-that Salmonella can replicate intracellularly even in the absence of T3SS function-would be significantly strengthened by demonstrating whether this is specific to Salmonella, or whether similar effects are seen with non-intracellular organisms such as E. coli K-12. If the phenomenon is unique to Salmonella, this would suggest a pathogen-specific mechanism beyond general metabolic support.

As acknowledged by the Reviewer, the novelty and key claim of our work is that Salmonella can replicate intracellularly even in the absence of T3SS. To experimentally sustain that claim, we showed evidence that providing macrophages with the preferred carbon sources used by Salmonella during infection, such as glycerol, bypass the requirement of both T3SS by Salmonella to grow, intravacuolarly, inside macrophages.

With respect to the article mentioned by the Reviewer (Liss et al. 2017, ref 36 in the manuscript), there are three important novel insights provided by our work: i) we show that Salmonella can replicate intracellularly in the SCV even in the absence of T3SS if certain carbon sources are provided; ii) we show the preference of Salmonella for certain carbon sources intracellularly such as glycerol and galactose (but not preferentially glucose); and iii) we have extended our observations to primary human macrophages in addition to RAW cells.

We are not convinced that the experiment suggested by the Reviewer to use E. coli K12 (ECK12) is necessary to support our findings for Salmonella, but we propose to add the requested experiment. Briefly, we will infect hMDMs and RAW macrophages with ST-WT-GFP, ST-ΔprgHΔssaV or ECK12-WT-GFP, while culturing macrophages on different carbon sources (glucose, glycerol, galactose, fructose). Then we will monitor intracellular bacterial growth. By comparing bacterial growth of ST double mutant with ECK12-WT-GFP under favorable carbon sources such as glycerol, the results will be definitive to answer whether this phenomenon is unique to Salmonella or not.

Specific Comments:

1. Figure 1H: The effect shown here is not compelling due to inconsistent y-axis scaling. Panels 1B, 1C, and 1D should use a unified axis range with 1H to allow direct visual comparison of growth dynamics.

Thank you, we will change it as suggested.

Figures 1B, 1C, 1G, 1H: The current presentation of individual growth traces makes it difficult to appreciate the population-level trend. A smoothed average line overlaid on these plots could better represent the average dynamics of replicative vs. non-replicative infections. Or alternatively the total fraction of cells that proliferate summarized as a segmented bar plot (possibly binned per time point).

We will plot the results as suggested, the total fraction of infected cells harboring bacteria that proliferate as a segmented bar plot, binned per time point.

Figure 2G: This panel would benefit from including a comparable condition with the SPI-1/SPI-2 double mutant to aid interpretation. Additionally, the authors should explore whether this nutrient-supported replication is seen in non-phagocytic cells such as HeLa or Caco-2, which would help delineate whether the observed phenomenon is macrophage-specific.

The graph asked by Reviewer is Figure S1D. As we are representing ST growth in macrophages supporting Salmonella replication, some of the conditions, such as lactate, cannot be shown in the infection conditions using the double mutant because there are no cells supporting the replication of the double mutant, so there are no cells to plot.

As suggested, we are also going to perform the same experiments in HeLa cells to investigate whether the observed phenomenon is macrophage specific.

Line 117: The sentence stating that the double mutant can undergo "exponential intracellular growth even in the absence of T3SS-dependent secretion" is an overstatement. The data suggest only a modest improvement in growth, restricted to a minority of infected cells. This claim should be revised accordingly, as should similar overstatements in the discussion (e.g., lines 203-204).

We will remove the term 'exponential' and revise the sentence at line 117 and those in the discussion. Line 203-204 will be: 'we demonstrated that providing macrophages with preferred nutrients allows a subpopulation of ST to replicate intracellularly without the need for a functional T3SS'.

Line 162: The authors should clarify that glycerol had the strongest effect in primary macrophages, while multiple alternative carbon sources had notable effects primarily in RAW cells.

We will add this clarification in the text.

Lines 198-201: This relates to the major concern. The authors should assess whether the observed growth enhancement is unique to Salmonella by testing other bacteria not known for intracellular replication. This would clarify whether the effect is due to general nutrient-driven host cell permissivity or a pathogen-specific adaptation.

As outlined above, we will perform the suggested experiment with E. coli K12 to answer whether this phenomenon is unique to Salmonella or not.

RAW 264.7 Observations: The modest intracellular growth of SPI-1/SPI-2 double mutants in RAW cells is consistent with prior observations in the field. The idea that nutrient availability explains this is noteworthy. The authors might consider whether differences in standard culture media (e.g., glucose concentration) influence these outcomes. This could have broader implications for reproducibility in infection models.

Thank you for the suggestion, we will include a paragraph discussing whether differences in standard culture media might influence bacterial replication. Indeed, to answer also a question from Reviewer #2, we will include a new supplementary Figure where we have already compared "no Glucose" (0 mM), "low Glucose" (2 mM) and standard culture media Glucose levels (10 mM). Our results show that differences in Glucose levels in the culture media influence Salmonella intracellular growth in hMDMs and RAW macrophages (see Figure below).

Reviewer #1 (Significance):

This manuscript highlights how host cell metabolism and nutrient availability can influence intracellular Salmonella replication. While the findings are intriguing, the current framing overstates their novelty and impact. Key revisions-such as comparative experiments with non-pathogenic bacteria and non-phagocytic cells, consistent figure scaling, and more measured language-would improve the clarity and significance of the work. If the authors can show Salmonella-specific mechanisms at play, the study could offer important insights into host-pathogen metabolic interactions.

We believe that performing all experiments suggested by the Reviewers, as well as the requested changes in the text to avoid overstatements, will improve the manuscript and will offer readers new insights and details to better understand the metabolic interactions happening between host and pathogens and how they can shape bacterial virulence.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary: In their study titled "Provision of Preferred Nutrients to Macrophages Enables Salmonella to Replicate Intracellularly Without Relying on Type III Secretion Systems", Dr. Garcia-Rodriguez et al. describe the influence of the host cell metabolism on the intracellular proliferation potential of Salmonella during infection. The authors investigate whether the supplementation of the media with different carbon sources has an impact on the intracellular lifestyle of Salmonella. By using single cell tracking in live-cell microscopy, including the use of different reporter strains, they describe that glycerol benefits Salmonella's ability to grow within its vacuolar niche, in part, interestingly, in a Type-3-Secretion System independent manner.

They furthermore highlight the dependence on host background for this observation by showing that effects differ between cells of varying metabolic activity. Throughout their study, they use cutting-edge methodologies, as well as Salmonella strains that could be of versatile use in other investigations. This work, while limited to in vitro models for now, has implications for the better understanding of how pathogens and their host are intertwined. This, in turn, has significance for the development of new anti-infective strategies further down the line. I therefore believe that it should be disseminated to the research community. The following comments summarize ideas how the quality of the study could be improved:

Major comments:

1. Salmonella, especially when cultured to activate the SPI-1 T3SS, introduce rapid cell death in their host - most commonly through activation of the NLRC4 inflammasome and downstream pyroptotic signaling. The authors don't describe the effect of the infection in differently supplemented media on host cell death, yet it would be important to elucidate whether this cellular response is also altered.

We have performed these experiments and tracked host cell death by measuring Annexin-V levels in single cells, during infection in the conditions using the different supplements. We will include these results in the revised version of the manuscript and main text. Please see the Figure below showing that the different carbon sources did not affect macrophages cell death significantly (future Figure S1E and S1F)

The aspect of partially T3SS-independent growth enhancement by glycerol (and depending on the host background glucose) is most curious. The authors quantify this by determining the percentage of cells containing proliferating Salmonella and by tracking individual cells over the time course of the infection. I am missing a general statement on whether the initial infection rate (i.e. timepoint 0) is comparable across conditions and mutants, and whether possible discrepancies in the infection rate could have downstream effects on the statements and claims made in the manuscript. This is, to my mind, also important for the quantification of cytosolic and vacuolar bacteria. There, the authors always speak in "percent of infected cells", so it is relevant whether the number of infected cells varies among conditions (see e.g. Figure 3).

We thank the reviewer for this comment. The initial infection rate at t=0 significantly differs between WT and mutants in RAW 264.7 macrophages, and carbon source supplementation has no effect. However, as we only analyze infected cells, this does not affect the final results. In any case, we are going to add the graphs of % of infected cells at t=0 as supplementary Figures S1G-K.

The authors use a concentration of 10mM for all supplemented alternative carbon sources. It would be useful to discuss the rationale behind this approach, including whether all chemicals have the same ability to be taken up by the cell. A concentration series (at least for some of the tested compounds) may be beneficial to bolster the conclusions that the authors make.

We use 10 mM as this is the concentration of Glucose in standard culture media. By using 10 mM for all the different carbon sources, we can thus compare them keeping concentration constant (10 mM). Indeed, to answer also Reviewer #1, we will include in the manuscript a paragraph discussing whether differences in standard culture media might influence bacterial replication. As this Reviewer suggested, we will include a new supplementary Figure comparing no Glucose (0 mM), low Glucose (2 mM) and standard culture media Glucose levels (10 mM), showing that the concentration of glucose has a gradual effect in supporting the replication of the T3SS-deficient strain in RAW macrophages (see Figure below).

I think it would strengthen the study, if the authors used host cell mutants in certain metabolite transporters, or alternatively Salmonella mutants that are deficient in uptake or metabolism of some of the compounds used in this study. This point is alluded to in the discussion, and I believe if the authors could show that in certain host mutant backgrounds the impact of supplementation with alternative carbon sources can be reversed, it would immensely bolster the strength of the claims.

Following Reviewer's suggestion, we generated ST metabolic mutants unable to metabolize glycerol, galactose or fructose. As seen in the Figures below, during infection, the supplementations with glycerol/galactose does not boost Salmonella replication in metabolic mutants as in WT conditions, demonstrating that supplemented carbon sources indeed arrive to bacteria within the SCV and are used by intracellular Salmonella to grow. This Figures will be now Future Figure 4J-N.

I think it would be useful to include the meaning of this work for other intracellular pathogens in the discussion section: Do the authors believe that this phenotype is Salmonella-specific? If the pathogens are at hand, it might be interesting to infect with other intracellular bacteria, such as Shigella or Francisella to investigate if the boosting of growth by glycerol also holds true for these.

We have performed experiments with Legionella pneumophila and galactose (see figure below), showing that this carbon source is specific of Salmonella (as shown in Figure 4F in the manuscript). We could perform experiments also with L. pneumophila and glycerol to answer the Reviewers question. However, we think that the results with Legionella might be out of the focus of this article and would constitute themselves a new article, as both pathogens have a very different, non-comparable intracellular metabolism. Thus, the experiment suggested by Reviewer #1 using E. coli K12 (ECK12) while culturing macrophages on different carbon sources (glucose, glycerol, galactose, fructose) is in our opinion a better fit. We will monitor intracellular bacterial growth and, by comparing bacterial growth of the ST-ΔprgH/ΔssaV double mutant with ECK12-WT-GFP under favorable carbon sources such as glycerol, the results will be definitive to answer whether this phenomenon is unique to Salmonella or not.

Minor comments:

• Line 41: The authors write "are required for", but given their findings, it might be more accurate to phrase this as "have previously been described to be required for" or "have previously been described essential for".

We will change it.

• Line 86: Is the referencing of Figure S1C correct or should it be S1A?

Yes, thank you, it is S1A, we will change it.

• Lines 119,120: Related to what is displayed in Figure 2G: Are these differences significant?

Glucose, galactose and lactate curves are significantly different compared to control (p

• Lines 126,127: What is the change for glycerol, and is the intracellular growth significantly higher compared to the control?

6,2 {plus minus} 1.9% in glycerol vs. 2 {plus minus} 1% in control, p

• Figure 1E&F: Related to one of the major comments: Would it be possible to quantify this at timepoint 0 to ensure that the initial infection rates are the same across conditions?

As outlined above, we will add the graphs of % of infected cells at t=0 as supplementary Figures S1G-K (Major Comment number 2 from this Reviewer)

• Figure 3E,F: Why does the sum of the curves not add up to 100% (especially in the beginning)? And related to that, why do both the percentage of cytosolic and vacuolar cells grow over time? Since this infection is performed with gentamycin present, re-infection should not be possible.

The localization module of the SINA plasmid relies on transcriptional reporters, whose expression requires time for induction and detection. Therefore, at early time points, infected cells are not classified as vacuolar or cytoplasmic because the reporters have not yet been expressed (as described in PLoS Pathog. 2021;17(4):e1009550, PMID: 33930101).

At later time points, a subset of cells harbors bacteria that do not express any of the reporters. These bacteria are considered dormant, representing about 10% of the population, as detailed in the same article. In addition, a small percentage of infected cells simultaneously contain both STvac and STcyt. Such cells are subclassified as harboring STcyt but also STvac. Consequently, the total proportion of infected cells carrying STvac and STcyt may also exceed 100%.

• Figure S1A: While significance testing is described in the legend, there are no indications of significance in the figure panels.

The Reviewer is right, there is no significant changes between conditions, we will change the significance testing to ns=non-significant.

• Figure S1B: Due to the stark discrepancies between hMDMs and RAW264.7, it might make sense to plot them on two different y-axes. Furthermore, I would clarify the y-axis: In the legend, it seems as CFU counts are shown, while CFU/ml/t2 rather describes a change over time.

We agree. However, we will maintain the scale of the Y-axis as it was required by Reviewer #1 to be consistent with Y-axis. We will change the legend to indicate that we plot CFU/ml/t2.

• Figure S1C: The prgH-mutant seems to outperform the wildtype in intracellular proliferation, while the double mutant underperforms compared to the ssaV-mutant. Could you please discuss/explain how the prgH-deletion has seemingly opposite effects on intracellular proliferation, depending on whether it is introduced in a wildtype or ssaV-KO background?

As T3SS-1 plays a role in inducing macrophage cell death via activation of the NLRC4 inflammasome, macrophages infected with bacteria carrying a functional T3SS-1 (such as WT), are more prone to undergo cell death at late time-points, which disrupts bacterial proliferation and reduces the proportion of infected cells. Thus, these dead cells were not considered in the analysis. Even if cell death of ST-WT-infected RAW macrophages remains below 5%, more ΔprgH-infected cells are considered in the analyses at late time-points, and ST-ΔprgH continue replicating (and growing in ST area).

• Figure S2A: As for the comments related to Figure 3, I am unsure how the sum of STvac and STcyt can deviate from 100. This is especially puzzling for the red curve (glycerol) at e.g. 3hpi, when the sum of the two clearly seems to be larger than 100.

At early time points, no infected cells are classified as vacuolar or cytoplasmic because the reporters have not yet been expressed. At later time points, a subset of cells harbor bacteria that do not express any of the reporters, which are considered dormant (10% of the population). Finally, a small percentage of infected cells simultaneously contain both STvac and STcyt, therefore the total proportion of infected cells carrying STvac and STcyt may also exceed 100%.

**Cross-commenting** I agree in principle with the comments raised by Reviewer #1 - especially when it comes to the enhancement in significance if the authors assess the species specificity. Elucidating whether the growth enhancement is Salmonella-specific, occurs for other intracellular pathogens (e.g. Shigella, Francisella) or also for extracellular bacteria (e.g. E. coli, Yersinia), would definitely strengthen the study.

As said before, for the revision we are going to perform the experiments suggested by Reviewer #1 of using E. coli K12 (ECK12) while culturing macrophages on different carbon sources (glucose, glycerol, galactose, fructose). And to satisfy this Reviewer's curiosity, we are going to perform experiments also with L. pneumophila and glycerol.

Reviewer #2 (Significance):

General assessment:

As the authors write in their discussion, the strength of this study is also it's limitation: Using single cell tracking in microscopy is a very elegant and powerful approach, yet conversely, it limits the scope of the study to in vitro approaches. While it enables assessment of bacterial pathogenicity and host-dependence on a single-cell level, it remains to be investigated whether the conclusion that the authors draw from their work will hold in more complex or physiologically relevant models.

During the preparation of this Revision Plan, we discovered the article published in PLoS Pathogens by Andrew Grant and Pietro Mastroni "Attenuated Salmonella Typhimurium Lacking the Pathogenicity Island-2 Type 3 Secretion System Grow to High Bacterial Numbers inside Phagocytes in Mice" (PLoS Pathog 2012 8(12): e1003070, PMID: 23236281). In this article, authors showed that our main conclusion is also relevant in vivo (Salmonella Typhimurium can replicate within macrophages in the absence of T3SS). This will be addressed in the Discussion of the revised manuscript. Our study provides a metabolic explanation, at the single cell level for those observations.

A further small shortcoming of the study is the heavy focus on the bacterial aspect in this host-pathogen interaction. While the authors do link the proliferative potential of the intracellular bacteria to the metabolic status of the individual host cell, more could be done with respect to host responses in the varying media compositions, including investigating alterations to the cell cycle, induction of cell death, or the ability to activate inflammatory signaling.

We agree, and we are actively investigating how restricting macrophages to specific carbon sources impact other host responses, such as cytokine production. For the revised manuscript, we will add the results on the induction of cell death.

Nonetheless, this study is of large interest to the field and the systematic approach to addressing their hypotheses speaks to the scientific excellence of the investigators.

Thank you.

3. Description of the revisions that have already been incorporated in the transferred manuscript

N/A

• *

4. Description of analyses that authors prefer not to carry out

N/A

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Referee #2

Evidence, reproducibility and clarity

Summary:

In their study titled "Provision of Preferred Nutrients to Macrophages Enables Salmonella to Replicate Intracellularly Without Relying on Type III Secretion Systems", Dr. Garcia-Rodriguez et al. describe the influence of the host cell metabolism on the intracellular proliferation potential of Salmonella during infection. The authors investigate whether the supplementation of the media with different carbon sources has an impact on the intracellular lifestyle of Salmonella. By using single cell tracking in live-cell microscopy, including the use of different reporter strains, they describe that glycerol benefits Salmonella's ability to grow within its vacuolar niche, in part, interestingly, in a Type-3-Secretion System independent manner.

They furthermore highlight the dependence on host background for this observation by showing that effects differ between cells of varying metabolic activity. Throughout their study, they use cutting-edge methodologies, as well as Salmonella strains that could be of versatile use in other investigations. This work, while limited to in vitro models for now, has implications for the better understanding of how pathogens and their host are intertwined. This, in turn, has significance for the development of new anti-infective strategies further down the line. I therefore believe that it should be disseminated to the research community. The following comments summarize ideas how the quality of the study could be improved:

Major comments:

1. Salmonella, especially when cultured to activate the SPI-1 T3SS, introduce rapid cell death in their host - most commonly through activation of the NLRC4 inflammasome and downstream pyroptotic signaling. The authors don't describe the effect of the infection in differently supplemented media on host cell death, yet it would be important to elucidate whether this cellular response is also altered.
2. The aspect of partially T3SS-independent growth enhancement by glycerol (and depending on the host background glucose) is most curious. The authors quantify this by determining the percentage of cells containing proliferating Salmonella and by tracking individual cells over the time course of the infection. I am missing a general statement on whether the initial infection rate (i.e. timepoint 0) is comparable across conditions and mutants, and whether possible discrepancies in the infection rate could have downstream effects on the statements and claims made in the manuscript. This is, to my mind, also important for the quantification of cytosolic and vacuolar bacteria. There, the authors always speak in "percent of infected cells", so it is relevant whether the number of infected cells varies among conditions (see e.g. Figure 3).
3. The authors use a concentration of 10mM for all supplemented alternative carbon sources. It would be useful to discuss the rationale behind this approach, including whether all chemicals have the same ability to be taken up by the cell. A concentration series (at least for some of the tested compounds) may be beneficial to bolster the conclusions that the authors make.
4. I think it would strengthen the study, if the authors used host cell mutants in certain metabolite transporters, or alternatively Salmonella mutants that are deficient in uptake or metabolism of some of the compounds used in this study. This point is alluded to in the discussion, and I believe if the authors could show that in certain host mutant backgrounds the impact of supplementation with alternative carbon sources can be reversed, it would immensely bolster the strength of the claims.
5. I think it would be useful to include the meaning of this work for other intracellular pathogens in the discussion section: Do the authors believe that this phenotype is Salmonella-specific? If the pathogens are at hand, it might be interesting to infect with other intracellular bacteria, such as Shigella or Francisella to investigate if the boosting of growth by glycerol also holds true for these.

Minor comments:

• Line 41: The authors write „are required for", but given their findings, it might be more accurate to phrase this as „have previously been described to be required for" or „have previously been described essential for".
• Line 86: Is the referencing of Figure S1C correct or should it be S1A?
• Lines 119,120: Related to what is displayed in Figure 2G: Are these differences significant?
• Lines 126,127: What is the change for glycerol, and is the intracellular growth significantly higher compared to the control?
• Figure 1E&F: Related to one of the major comments: Would it be possible to quantify this at timepoint 0 to ensure that the initial infection rates are the same across conditions?
• Figure 3E,F: Why does the sum of the curves not add up to 100% (especially in the beginning)? And related to that, why do both the percentage of cytosolic and vacuolar cells grow over time? Since this infection is performed with gentamycin present, re-infection should not be possible.
• Figure S1A: While significance testing is described in the legend, there are no indications of significance in the figure panels.
• Figure S1B: Due to the stark discrepancies between hMDMs and RAW264.7, it might make sense to plot them on two different y-axes. Furthermore, I would clarify the y-axis: In the legend, it seems as CFU counts are shown, while CFU/ml/t2 rather describes a change over time.
• Figure S1C: The prgH-mutant seems to outperform the wildtype in intracellular proliferation, while the double mutant underperforms compared to the ssaV-mutant. Could you please discuss / explain how the prgH-deletion has seemingly opposite effects on intracellular proliferation, depending on whether it is introduced in a wildtype or ssaV-KO background?
• Figure S2A: As for the comments related to Figure 3, I am unsure how the sum of STvac and STcyt can deviate from 100. This is especially puzzling for the red curve (glycerol) at e.g. 3hpi, when the sum of the two clearly seems to be larger than 100.

Cross-commenting

I agree in principle with the comments raised by Reviewer #1 - especially when it comes to the enhancement in significance if the authors assess the species specificity. Elucidating whether the growth enhancement is Salmonella-specific, occurs for other intracellular pathogens (e.g. Shigella, Francisella) or also for extracellular bacteria (e.g. E. coli, Yersinia), would definitely strengthen the study.

Significance

General assessment:

As the authors write in their discussion, the strength of this study is also it's limitation: Using single cell tracking in microscopy is a very elegant and powerful approach, yet conversely, it limits the scope of the study to in vitro approaches. While it enables assessment of bacterial pathogenicity and host-dependence on a single-cell level, it remains to be investigated whether the conclusion that the authors draw from their work will hold in more complex or physiologically relevant models.

A further small shortcoming of the study is the heavy focus on the bacterial aspect in this host-pathogen interaction. While the authors do link the proliferative potential of the intracellular bacteria to the metabolic status of the individual host cell, more could be done with respect to host responses in the varying media compositions, including investigating alterations to the cell cycle, induction of cell death, or the ability to activate inflammatory signaling.

Nonetheless, this study is of large interest to the field and the systematic approach to addressing their hypotheses speaks to the scientific excellence of the investigators.

Advance:

The advance this study makes is rather on the foundational than the applied side - which does not mean that conclusions drawn in this work are not of interest to a wider field. By investigating the intracellular lifestyle on a single-cell level, the authors were able to observe a striking and curious phenotype: that certain alternative carbon sources can enhance intracellular proliferation in a T3SS-independent manner. By further dissecting the reason for this observation, they create a stronger base for their conclusion in what can be described as an overall comprehensive study.

Audience:

As outlined in the description of the main advances, this study will be of largest interest to members of the basic research community in host-pathogen interactions. While the study so far focuses on Salmonella, a well-described and genetically accessible intracellular model pathogen, it could also be of interest to a broader community of researchers investigating bacterial pathogenicity, as well as those that are interested in the host metabolism.

Describe your expertise:

I have a background in bacterial pathogenicity in Salmonella infection, and have since expanded to other pathogens, as well as co-infections with viruses. In addition to investigating the pathogens, I have expertise in dissecting the host response, with a focus on innate immunity, inflammasome activation and host cell death. Overall, I am accustomed to unbiased screening approaches, which are followed by the formulation and assessment of hypotheses to unravel the molecular mechanisms underlying the host-pathogen interface.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors investigate how host cell metabolic heterogeneity influences the intracellular replication of Salmonella enterica serovar Typhimurium. They use live-cell imaging of infected human primary macrophages to reveal that bacterial replication does not occur uniformly across infected cells. They demonstrate that supplementation with specific carbon sources-used by Salmonella during infection-promotes bacterial replication and increases the proportion of macrophages supporting intracellular growth. These effects are seen even in the absence of functional Type III Secretion Systems (T3SS), using a ΔprgH/ΔssaV double mutant. The authors further suggest that this replication enhancement is not strictly dependent on host glycolytic activity but rather on the host cell's ability to import nutrients. Their findings imply that intracellular Salmonella can exploit host cell metabolism to grow, even without its canonical virulence secretion systems, under nutrient-favorable conditions.

Major Concern:

While the topic is potentially interesting, the novelty is not fully clear. The concept that nutrient availability impacts intracellular Salmonella replication, largely via T3SS2 function, has been addressed previously (e.g., Liss et al., 2017). The finding that added exogenous carbon sources can enhance bacterial growth is thus not unexpected. The key claim-that Salmonella can replicate intracellularly even in the absence of T3SS function-would be significantly strengthened by demonstrating whether this is specific to Salmonella, or whether similar effects are seen with non-intracellular organisms such as E. coli K-12. If the phenomenon is unique to Salmonella, this would suggest a pathogen-specific mechanism beyond general metabolic support.

Specific Comments:

1. Figure 1H: The effect shown here is not compelling due to inconsistent y-axis scaling. Panels 1B, 1C, and 1D should use a unified axis range with 1H to allow direct visual comparison of growth dynamics.
2. Figures 1B, 1C, 1G, 1H: The current presentation of individual growth traces makes it difficult to appreciate the population-level trend. A smoothed average line overlaid on these plots could better represent the average dynamics of replicative vs. non-replicative infections. Or alternatively the total fraction of cells that proliferate summarized as a segmented barplot (possibly binned per time point).
3. Figure 2G: This panel would benefit from including a comparable condition with the SPI-1/SPI-2 double mutant to aid interpretation. Additionally, the authors should explore whether this nutrient-supported replication is seen in non-phagocytic cells such as HeLa or Caco-2, which would help delineate whether the observed phenomenon is macrophage-specific.
4. Line 117: The sentence stating that the double mutant can undergo "exponential intracellular growth even in the absence of T3SS-dependent secretion" is an overstatement. The data suggest only a modest improvement in growth, restricted to a minority of infected cells. This claim should be revised accordingly, as should similar overstatements in the discussion (e.g., lines 203-204).
5. Line 162: The authors should clarify that glycerol had the strongest effect in primary macrophages, while multiple alternative carbon sources had notable effects primarily in RAW cells.
6. Lines 198-201: This relates to the major concern. The authors should assess whether the observed growth enhancement is unique to Salmonella by testing other bacteria not known for intracellular replication. This would clarify whether the effect is due to general nutrient-driven host cell permissivity or a pathogen-specific adaptation.
7. RAW 264.7 Observations: The modest intracellular growth of SPI-1/SPI-2 double mutants in RAW cells is consistent with prior observations in the field. The idea that nutrient availability explains this is noteworthy. The authors might consider whether differences in standard culture media (e.g., glucose concentration) influence these outcomes. This could have broader implications for reproducibility in infection models.

Significance

This manuscript highlights how host cell metabolism and nutrient availability can influence intracellular Salmonella replication. While the findings are intriguing, the current framing overstates their novelty and impact. Key revisions-such as comparative experiments with non-pathogenic bacteria and non-phagocytic cells, consistent figure scaling, and more measured language-would improve the clarity and significance of the work. If the authors can show Salmonella-specific mechanisms at play, the study could offer important insights into host-pathogen metabolic interactions.

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Reply to the reviewers

We thank the Reviewers for their kind and constructive comments. We are happy to read that the reviewers found our study methodologically robust and comprehensive in addressing the metabolic heterogeneity of endothelial cells.

Reviewer 1, comment 1: Image quality in sprouting assays - The images presented for the sprouting assays (e.g., Figure 4) are of suboptimal resolution and quality, making it difficult to evaluate the effects of the various compounds on EC behavior. Even under control conditions, clear sprout-like structures are not readily discernible. Improved image resolution-preferably through high-quality bright-field microscopy-and the inclusion of immunofluorescence images of labeled endothelial spheroids are recommended to enhance interpretability.

Response: We appreciate the reviewer’s concern and have revisited the sprouting assay images. Our approach is consistent with established methods in the field (Heiss et al., FASEB J, 2015), where brightfield imaging is routinely used for quantification without additional immunostaining. Hence, we believe that the brightfield images are of sufficient resolution to allow reproducible quantification of normalized total sprout length. All experiments were performed under identical imaging and analysis protocols, and thus we are confident that the quantification reflects true biological differences. We cite the reference in the revised manuscript and clarify it as well in the Methods section.

Reviewer 1, comment 2: Validation of the quiescence model - The current approach to induce quiescence should be further substantiated. Beyond proliferation markers, additional hallmarks of quiescent cells-such as epigenetic signatures, protein quality control mechanisms, and translational activity-should be assessed to confirm that the EC subtypes achieve a bona fide resting state.

Response: We acknowledge the value of proper phenotyping of quiescent cells. However, most studies involving quiescent (endothelial) cells rely on EdU incorporation or similar proliferation markers to confirm entry into a non-proliferative state (Kalucka et al., Cell Metabolism, 2018; Coloff et al., Cell Metabolism, 2016). In our study, we have used EdU staining and FACS analysis to establish cell cycle arrest. Moreover, we find clear proteomic patterns that support the case of a quiescent state. We have also demonstrated the reversibility of quiescence (see Suppl. Fig. 1c) via reseeding and proliferation recovery of all EC types, which is a defining functional hallmark of true quiescence. Together, the EdU, proteomic and reseeding/proliferation data provide strong evidence that our EC subtypes reach a physiologically quiescent, non-senescent state.

Reviewer 1, comment 3: Reversibility of quiescence - It is important to demonstrate that the EC subtypes investigated can re-enter the cell cycle following release from contact inhibition. Without such evidence, the possibility remains that some of the observed metabolic features reflect a transition to senescence rather than reversible quiescence.

Response: This is an excellent suggestion. We have included new data that shows that ECs regain proliferative capacity upon reseeding of quiescent ECs at lower confluency (Suppl. Fig. 1c). The results support the interpretation that the observed metabolic features reflect reversible quiescence rather than senescence.

Reviewer 1, comment 4: Assessment of cell viability - While EC proliferation, migration, and sprouting were examined to infer functional roles of metabolic adaptations, analyses of cell viability and death are also necessary to evaluate potential homeostatic or survival-related functions of the observed metabolic changes.

Response: We appreciate the Reviewer’s concern about cell viability in our experimental setup, and we agree that viability assessment is important. Using trypan blue staining and automated cell counting, we observed that >85% of ECs remained viable from day 1 through day 10 of the quiescence model and included these results in the manuscript (Suppl. Fig. 1b).

Reviewer 1, comment 5: Validation of pharmacological findings - The pharmacological inhibition experiments are informative and constitute a central part of the study. However, given the possibility of off-target effects, key conclusions should be corroborated using alternative loss-of-function approaches, such as RNA interference (e.g., shRNA or siRNA).

Response: We recognize the possibility of side effects for pharmacological inhibitors, but the inhibitors, including the ones that show the strongest different effects in HUVECs and iLECs (succinyl acetone and R162) in our study are well-established, selective inhibitors of glutamate dehydrogenase (Wang et al., Pharmacological Research, 2022) and δ-aminolevulinic acid dehydratase (Nauli et al., J Clin. Biochem. Nutr., 2023), respectively, and have not been reported to exhibit significant off-target activity in endothelial cells. Furthermore, the aim of our study was not to define specific mechanistic pathways, but to highlight phenotype-specific metabolic vulnerabilities in distinct endothelial states. Performing knockdown experiments would go beyond the scope and focus of this manuscript and introduce their own limitations, including off-target effects and, most importantly, timing mismatches relative to our long-term assays (e.g., sprouting assays assessed at day 3 versus transient RNAi effects lasting for only 1-2 days). We hope the Reviewer agrees that our current approach sufficiently supports the study’s conclusions.

__Reviewer 2, comment 1: __it was not clear whether the authors worked with single donor endothelial cells or with mixed donors. This should be clarified as it is important for the statistical analyses (single donor based EC research typically uses n=4, while for the mixed donor, an n=3 is sufficient).

Response: We thank Rreviewer 2 for highlighting that we did not include this information in the Methods section and we did so in the revised manuscript. HDBECs, HDLECs and iLECs are from single donors, HUVECs are from mixed donors. We acknowledge the reviewer’s concern about the power of statistical analyses, but we think that n=3 is sufficient with proper correction for statistical tests. Furthermore, previous in vitro studies with ECs are done with single donor cells and in biological triplicates (Wong et al., 2017; Kalucka et al., 2018; Simões-Faria et al., 2025 and more). Moreover, for sprouting assays, we have n > 3 for most conditions.

Reviewer 2, comment 2: I would like to see a sentence on the importance of shear stress in EC behavior (metabolism) in the introduction. It was recently shown that the in vivo situation of ECs encountering wall shear stress (Faria et al, PMID: 39832080) affects the metabolic behavior switching to glutamine metabolism. This aligns with the research of the authors as well.

Response: We thank Reviewer 2 for drawing our attention to this relevant and interesting study. We mention the study in the introduction and the discussion.

Reviewer 2, comment 3: suggestion for the authors: it could be useful if a figure is introduced to show the "physiological" location of the 4 EC used and that a rationale is provided for this.

Response: We have included this in Supplementary Figure 1 and in the text.

Reviewer 2, comment 4: figures are of low quality, I found it very difficult to see the spheroid/sprouting images. This should be addressed in the final version prior publication.

Response: The new version has higher quality sprouting images in figure 4 and 5. The images can also be found in high quality on BioStudies (Accession: S-BSST1716).

Reviewer 2, comment 5: Fig 2 c: I'm not sure if this panel is very relevant, when looking into detail, opposite pathways are present (glycolysis - gluconeogenesis). As well, I'm not sure if galactose metabolism is truly relevant, unless the author managed to measure distinct hexose and hexose-phosphates? Given the flow injection analysis setup, I doubt this. Would suggest to move this to supplement or to simply leave it out.

Response: The Reviewer is correct; the employed analytics cannot distinguish different hexoses and hexose-phosphates. We have moved figure 2c to supplementary figure 4c.

Reviewer 2, comment 6: Fig 3 b: was there any statistics performed on these data to compare the different setups?

Response: We performed statistical analyses on this data and included it in the figures and figure legends.

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Referee #2

Evidence, reproducibility and clarity

By employing a proteomics and metabolomics approach the authors clarified the molecular landscape of 4 major EC types in quiescent and proliferating conditions. The study is extensive and adds novelty to the EC research

Major comments:

• it was not clear whether the authors worked with single donor endothelial cells or with mixed donors. This should be clarified as it is important for the statistical analyses (single donor based EC research typically uses n=4, while for the mixed donor, an n=3 is sufficient).
• I would like to see a sentence on the importance of shear stress in EC behavior (metabolism) in the introduction. It was recently shown that the in vivo situation of ECs encountering wall shear stress (Faria et al, PMID: 39832080) affects the metabolic behavior switching to glutamine metabolism. This aligns with the research of the authors as well.
• suggestion for the authors: it could be useful if a figure is introduced to show the "physiological" location of the 4 EC used and that a rationale is provided for this.
• figures are of low quality, I found it very difficult to see the spheroid/sprouting images. This should be addressed in the final version prior publication.
• Fig 2 c: I'm not sure if this panel is very relevant, when looking into detail, opposite pathways are present (glycolysis - gluconeogenesis). As well, I'm not sure if galactose metabolism is truly relevant, unless the author managed to measure distinct hexose and hexose-phosphates? Given the flow injection analysis setup, I doubt this. Would suggest to move this to supplement or to simply leave it out.
• Fig 3 b: was there any statistics performed on these data to compare the different setups?

Significance

the study adds insights to the ongoing research on EC molecular behavior.

using different types of ECs in both quiescent and proliferating mode, as well as the validation of pathways by introducing inhibitors combined with the sprouting assays is an asset.

I would like to see stated the biological complexity of EC, it was recently shown that shear stress plays an important role in EC metabolism.

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Referee #1

Evidence, reproducibility and clarity

Summary: 
 The study by Durot and colleagues explores the metabolic heterogeneity of endothelial cells (ECs) across distinct subtypes (blood vs. lymphatic) and growth states (proliferating vs. quiescent). Through integrated proteomic and metabolomic analyses, the authors demonstrate that quiescent ECs are not metabolically inactive but instead undergo subtype-specific metabolic reprogramming. Functional perturbation of key metabolic pathways using chemical inhibitors results in differential phenotypic responses in blood versus lymphatic ECs. Collectively, the findings underscore a critical, context-dependent role of metabolism in maintaining EC function and highlight metabolic specialization as a fundamental feature of endothelial diversity.

General Comments: 
 This manuscript presents a comprehensive and methodologically robust investigation into the metabolic diversity of cultured ECs. By combining proteomic and metabolomic approaches, the authors provide novel insights into the distinct metabolic profiles of blood and lymphatic ECs, and how these profiles shift as ECs transition from a proliferative to a quiescent state. The observation that quiescent ECs exhibit active metabolic reprogramming, rather than simply entering a dormant state, is particularly compelling and challenges existing models of cellular quiescence.

The work is timely, well-written and addresses a significant gap in our understanding of endothelial metabolism. The integration of large-scale omics data with functional perturbation experiments strengthens the overall conclusions and enhances the impact of the study.

Nevertheless, while the data are largely convincing, certain experimental aspects-particularly those related to the in vitro sprouting assays-require further validation to solidify the mechanistic interpretations. Additionally, some findings would benefit from further validation using alternative approaches (e.g., chemical perturbation studies).

Specific Comments:

1. Image quality in sprouting assays - The images presented for the sprouting assays (e.g., Figure 4) are of suboptimal resolution and quality, making it difficult to evaluate the effects of the various compounds on EC behavior. Even under control conditions, clear sprout-like structures are not readily discernible. Improved image resolution-preferably through high-quality bright-field microscopy-and the inclusion of immunofluorescence images of labeled endothelial spheroids are recommended to enhance interpretability.
2. Validation of the quiescence model - The current approach to induce quiescence should be further substantiated. Beyond proliferation markers, additional hallmarks of quiescent cells-such as epigenetic signatures, protein quality control mechanisms, and translational activity-should be assessed to confirm that the EC subtypes achieve a bona fide resting state.
3. Reversibility of quiescence - It is important to demonstrate that the EC subtypes investigated can re-enter the cell cycle following release from contact inhibition. Without such evidence, the possibility remains that some of the observed metabolic features reflect a transition to senescence rather than reversible quiescence.
4. Assessment of cell viability - While EC proliferation, migration, and sprouting were examined to infer functional roles of metabolic adaptations, analyses of cell viability and death are also necessary to evaluate potential homeostatic or survival-related functions of the observed metabolic changes.
5. Validation of pharmacological findings - The pharmacological inhibition experiments are informative and constitute a central part of the study. However, given the possibility of off-target effects, key conclusions should be corroborated using alternative loss-of-function approaches, such as RNA interference (e.g., shRNA or siRNA).

Significance

In summary, this manuscript makes a substantial contribution to the field and is likely to stimulate further research into endothelial metabolic regulation. With additional experimental validation, the study has the potential to serve as a reference in both vascular and metabolic research.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In this paper, the GFP-GBP system for mistargeting protein localization was used in fission yeast cells to discover new protein interactions involved in vesicular trafficking during cytokinesis. This approach uncovered a new association between the F-BAR protein Rga7 and its binding partner Rng10 with the Munc13 protein Ync13 at the cell division site. Additional associations were observed between Rga7-Rng10, Ync13 and the glucan synthases Ags1 and Bgs4, and the vesicle fusion protein Sec1. These interactions identified by the GFP-GBP system were further supported by co-immunoprecipitation experiments and by defining localization dependencies with live cell imaging in a variety of mutant strains. The imaging data are all of high quality and for the most part support the conclusions. However, in my opinion some of the interpretations are overstated, and the manuscript would benefit from providing additional mechanistic information. Major and minor recommendations are outlined below.

Major suggestions 1. The co-IP data are interpreted to suggest that all the above-mentioned proteins form a single "big complex." However, as noted in the manuscript and reflected in the model, the multipass integral membrane proteins Bgs4 and Ags1 are embedded in the vesicle membrane and likely only indirectly associate with the scaffold Rga7-Rng10 via Ync13, without forming a 'complex'. One would expect the entirety of these vesicle contents to co-IP if the model is correct. The first paragraph of page 11 should be revised to more clearly reflect this scenario and to align with the proposed model.

Response: We thank the reviewer for this thoughtful clarification. In the original manuscript, we stated “…indicating these proteins do interact or form big protein complexes… These results suggest that Rga7, Rng10, and Ync13 form a protein complex.” We agree that our initial wording may have unintentionally implied that all proteins detected in co-IP experiments assemble into a single, large physical complex. As the reviewer correctly noticed, the multipass integral membrane proteins Bgs4 and Ags1 are embedded within vesicle membranes and are more likely to associate indirectly with the Rga7-Rng10-Ync13 complex, rather than being part of one unified protein complex. To avoid overinterpretation, we have modified the last sentence of the first paragraph on the original page 11 as below: “These results suggest that Rga7, Rng10, and Ync13 do form a protein complex, although maybe dynamic and not super stable (see Discussion). Our data indicate that Rga7 interacts with both Ync13 and Rng10 to form a module on the plasma membrane for targeting of the vesicles containing cargos such as glucan synthases Bgs4 and Ags1. However, these glucan synthases are multipass integral membrane embedded proteins and likely only indirectly associate with the module Rng10-Rga7-Ync13, without forming a big protein complex.”

Can Ync13 be artificially directed or tethered to the division site independently of Rga7-Rng10 (e.g., via Imp2)? If so, can this rescue the phenotypes of rga7Δ cells? This experiment could clarify whether Ync13 is the key functional effector of the Rga7-Rng10 complex.

Response: We thank the reviewer for suggesting this interesting experiment. We agree that testing whether correctly localized Ync13 is sufficient to execute the division-site function of the Rga7–Rng10 complex would clarify its role. To test this, we artificially targeted Ync13 to the division site independently of Rga7 by tethering it to the scaffold protein Pmo25. Pmo25, an MO25 family protein, localizes to both the plasma membrane at the division site and the spindle pole body (mainly one of the SPBs) during mitosis and cytokinesis, enabling us to mislocalize Ync13 to these structures through GFP–GBP system. We did not use Imp2 because its localization pattern (mainly to the contractile ring [1, 2]) is different from Ync13. Microscopy revealed robust localization of Ync13 at the division site and the SPB in rga7Δ cells, and this tethered Ync13 persisted along the cleavage furrow throughout ring constriction. Importantly, enforced division-site localization of Ync13 significantly rescued the cytokinesis defects and cell lysis of rga7Δ. Consistently, growth assays on Phloxin B (PB) plate showed the elevated lysis/death in rga7Δ cells was rescued by Ync13 tethering to Pmo25-GBP. Together, these findings support that Ync13 is a key functional effector acting downstream of the Rga7–Rng10 scaffold at the division site. We have added these results in the new Figure 6 and associate text in the revised manuscript. We have also updated the model in Figure 8 to reflect this new result.

1. Demeter J, Sazer S. imp2, a new component of the actin ring in the fission yeast Schizosaccharomyces pombe. J Cell Biol. 1998;143(2):415-27. PubMed PMID: 9786952.
2. Martin-Garcia R, Coll PM, Perez P. F-BAR domain protein Rga7 collaborates with Cdc15 and Imp2 to ensure proper cytokinesis in fission yeast. J Cell Sci. 2014;127(Pt 19):4146-58. Epub 2014/07/24. doi: 10.1242/jcs.146233. PubMed PMID: 25052092.
3. The authors should consider structural or computational modeling of the proposed Rga7-Rng10-Ync13 complex. Such analysis could offer insight into how these components interact and strengthen the proposed model. Response: We thank the reviewer for this valuable suggestion. Following the recommendation, we performed structural modeling of the Rga7–Rng10–Ync13 complex using AlphaFold3. Our previous work demonstrated that the F-BAR protein Rga7 forms a stable dimer and its F-BAR domain binds the C-terminal (aa751–1038) region of Rng10 [3]. Based on these findings, we constructed an input model consisting of two full-length Rga7 subunits, two Rng10(751–1038) subunits, and one full-length Ync13. The predicted structure revealed a modular organization in which Rng10(751–1038) associated strongly with the F-BAR domain of the Rga7 dimer, consistent with our prior biochemical data [3]. In addition, the model suggested that Ync13 interacted with the GAP domain of Rga7, positioning Ync13 in close proximity to the Rga7–Rng10 interface (Fig. S5, A, B, D and F). Further domain specific predictions confirmed the interactions between Rga7-GAP and Ync13 N-terminus (pTM: 0.63, ipTM: 0.64), two Rga7 F-BARs (pTM: 0.74, ipTM: 0.71), as well as Rga7 F-BAR and Rng10(751–1038) (pTM: 0.56, ipTM: 0.78) (Fig. S5, C-F). Overlay analyses revealed that the interacting domains align well with the structure of whole complex as the root mean square differences (RMSDs) are Liu Y, McDonald NA, Naegele SM, Gould KL, Wu J-Q. The F-BAR domain of Rga7 relies on a cooperative mechanism of membrane binding with a partner protein during fission yeast cytokinesis. Cell Rep. 2019;26(10):2540-8.e4. doi: 10.1016/j.celrep.2019.01.112. PubMed PMID: 30840879; PubMed Central PMCID: PMCPMC6425953.

Minor text edits 1. Define "SIN" in the discussion section for clarity.

Response: We defined the SIN pathway in the Discussion section as suggested: “At low restrictive temperatures, the lethality of mutant sid2, the most downstream kinase in the Septation Initiation Network, is partially rescued by upregulating Rho1. Thus, it has been suggested that the Septation Initiation Network activates Rho1, which in turn activates the glucan synthases [4].”

Alcaide-Gavilán M, Lahoz A, Daga RR, Jimenez J. Feedback regulation of SIN by Etd1 and Rho1 in fission yeast. Genetics. 2014;196(2):455-70. Epub 2013/12/18. doi: 10.1534/genetics.113.155218. PubMed PMID: 24336750; PubMed Central PMCID: PMCPMC3914619.

Figure S3, the protein schematics should start at residue "1" and not "0".

Response: We apologize for the mistake. The schematics in revised figure (now Figure S4A) have been corrected to start at residue 1.

Mass spectrometry data referenced in the text are not provided in the manuscript.

__Response: __We apologize for the omission. The mass spectrometry data are now shown in Table S1. __

__

In Figure 4A. The Ags1 rim localization does not appear decreased as the authors claim.

__Response: __After examining the data again, we agree with the reviewer’s assessment. So, we reworded the sentence as the following: “We also found that in ync13Δ cells, the Bgs4 intensity at the rim of the septum was much lower than in WT after ring constriction (Fig. 4B).”

On page 13: "both Rga7 and Rng10 can mistarget Trs120 to mitochondria."

Response: Thank you. The typo “mistargeting” has been corrected to “mistarget”.

Minor figure edits 1. Consider inverting single-channel images to display fluorescence on a white background, which would improve visual clarity.

Response: We appreciate the reviewer’s suggestion. However, we have chosen to retain the original display format with fluorescence shown in a black background, to be consistent with our (and some others’) previous publications. We believe this format preserves clarity while allowing easier comparison with the previously published works.

The Figure 1 legend should describe the experimental setup rather than restating conclusions.

Response: We thank the reviewer for this helpful suggestion. The Figure 1 legend has been revised to describe the experimental setup and imaging conditions rather than summarizing conclusions as the following:

Fig. 1. Physical interactions among the key cytokinetic proteins in plasma membrane deposition and septum formation revealed by ectopic mistargeting to mitochondria by Tom20-GBP. __Arrowheads mark examples of colocalization at mitochondria. (A) Ync13 colocalizes with Rga7 and Rng10 at cell tips and the division site. (B-F) Tom20-GBP can ectopically mistarget Rga7/Rng10-mEGFP and their interacting partners tagged with tdTomato/RFP/mCherry to mitochondria. Tom20–GBP was used to recruit mEGFP-tagged Rga7 or Rng10 to mitochondria, and colocalization was assessed with tdTomato/RFP/mCherry-tagged candidate binding partners. Cells were grown at 25ºC in YE5S + 1.2 M sorbitol medium for ~36 to 48 h and then were washed with YE5S without sorbitol and grown in YE5S for 4 h before imaging. (B) Rga7/Rng10-Ync13. (C) Rga7/Rng10-Trs120. (D) Rga7/Rng10-Bgs4. (E) Rga7/Rng10-Ags1. (F)__ Rga7-Smi1. Bars, 5 μm.

Reduce the number of arrows indicating co-localization in microscopy images; highlighting 1-2 representative examples is sufficient and less visually cluttered.

Response: We appreciate the reviewer’s suggestion. We have revised the micrographs to reduce the number of arrowheads, highlighting several representative examples of co-localization per image. This improves clarity and reduces visual clutter while still guiding the reader to the key observations.

Figure 3F, the scale bar is listed as 5 μm in the legend but it appears to my eye to be 2 μm.

Response: We thank the reviewer for noticing this error. After rechecking the original imaging data, we have added a new 5 μm scale bar.

The orientation of Bgs4/Smi1 should be inverted in the schematic within vesicles so that Smi1 is always on the cytoplasmic side.

Response: We thank the reviewer for pointing out this error. The schematic has been corrected so that Bgs4 and Smi1 are oriented appropriately, with Smi1 consistently placed on the cytoplasmic side of vesicles because it does not have a transmembrane domain. The revised schematic is included in the updated Figure 8.

6. Also in the schematic, Mid1 is not at the constricting CR and therefore needs to be removed.

__Response: __Thank you for the suggestion. Mid1 has been removed from the model figure.

Reviewer #1 (Significance (Required): From the data presented in the manuscript, it is proposed that Rga7 and Rng10 form a scaffold at the division site for delivery of exocytic vesicles marked by the TRAPPII complex but not the exocyst complex. Further, it is proposed that these vesicles deliver specifically the glucan synthases necessary for septation. Overall, this study builds on previous work from the Wu lab to clarify how the TRAPPII-decorated vesicles are specifically delivered to the cell division site, adding some new information about vesicle trafficking regulation during cytokinesis. It also provides new insight into the role of a F-BAR scaffold protein.

This paper will be of interest to those studying cytokinesis and also those studying mechanisms of intracellular trafficking.

Reviewer expertise: Cell division, signaling, membrane biology

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

Summary:

This paper provides a comprehensive analysis of the roles of Rng10, Rga7, and Ync13 in cytokinesis using fission yeast as a model system. The authors demonstrate that Ync13/Rna7/Rng10 not only interact with each other but also associate with components of glucan synthases, which are essential for secondary septum formation but not for the primary septum. They further show that Ync13 is involved in exocytosis through its interaction with Sec1 and plays a role in membrane trafficking via interaction with the TRAPP-II complex. Collectively, their findings reveal a coordinated mechanism that ensures the timely formation of the secondary septum during cytokinesis, as deletion of these proteins disrupts septum formation and leads to cell lysis.

The conclusions drawn in this paper are well-supported by the data, with a clear methodology and robust statistical analyses that enhance reproducibility. However, I have the following major and minor comments:

Major Comments - 1) The authors propose that Ync13, Rng10, and Rga7 interact to form a protein complex, supported by their mislocalization studies. While these findings are suggestive, additional co-immunoprecipitation (co-IP) data specifically demonstrating a direct interaction between Ync13 and Rng10 would strengthen the claim.

Response: We thank the reviewer for this suggestion. The direct interaction between Rga7 with Rng10 has been already established and published by our group [3, 5]. Here we found that Rga7 and Ync13 directly interact by in vitro binding assay (Figure 2, D and E). While our current data do not suggest a direct physical interaction between Ync13 and Rng10, our mislocalization results and other data do provide strong support for their functional association. In particular, ectopic tethering of Ync13 to mitochondria recruits Rng10 to the same sites and vice versa (Figures. 1B and S2A). Additionally, division-site tethering of Ync13 by Pmo25-GBP rescues both the growth and cell-lysis phenotype of rga7Δ (Figure 6), consistent with the idea that Ync13 functions downstream of Rga7-Rng10 because Rga7 localization depends on Rng10 (Figure 8). Furthermore, our AlphaFold3 modeling predicts that Rng10 binds the BAR domain of Rga7, whereas Ync13 binds the GAP domain of Rga7, suggesting that Rng10 and Ync13 are positioned within the same complex through Rga7 without direct interaction (Figure S5).

        The predicted lack of direct interaction between Ync13 and Rng10(751–1038) is supported by the experiment mentioned below to answer the minor question from the Reviewer 3. We tested the mistargeting of mECitrine-Rng10(751–1038) in *rga7Δ tom20-GBP* cells and found that Ync13-tdTomato could not be recruited to mitochondria (Figure S4H). This indicates that Ync13 cannot interact with Rng10(751–1038) independently of Rga7, supporting our proposed model that Rga7 interacts with Rng10 through the BAR domain while with Ync13 through the GAP domain. We have added these clarifications to the revised manuscript (Results and Discussion) to better contextualize the evidence for the Rga7–Rng10–Ync13 assembly.

Liu Y, McDonald NA, Naegele SM, Gould KL, Wu J-Q. The F-BAR Domain of Rga7 Relies on a Cooperative Mechanism of Membrane Binding with a Partner Protein during Fission Yeast Cytokinesis. Cell Rep. 2019;26(10):2540-8.e4. doi: 10.1016/j.celrep.2019.01.112. PubMed PMID: 30840879; PubMed Central PMCID: PMCPMC6425953. Liu Y, Lee I-J, Sun M, Lower CA, Runge KW, Ma J, et al. Roles of the novel coiled-coil protein Rng10 in septum formation during fission yeast cytokinesis. Mol Biol Cell. 2016;27(16):2528-41. Epub 2016/07/08. doi: 10.1091/mbc.E16-03-0156. PubMed PMID: 27385337; PubMed Central PMCID: PMCPMC4985255.

2) It remains unclear whether Ync13 directly interacts with components of the glucan synthase complex (Bgs4/Ags1), or if this association is mediated through other factors (Rng10, Rga7). Clarifying the nature of this interaction would significantly enhance the mechanistic insight.

Response: We thank the reviewer for this thoughtful clarification. As pointed out by Reviewer 1 in major comment 1, the multipass integral membrane proteins Bgs4 and Ags1 are embedded within vesicle membranes and are more likely to associate indirectly with the Rga7–Rng10-Ync13 complex rather than being part of one unified protein complex, although Rga7 Co-IPs with Bgs4 and its binding partner Smi1 (Figure 1, A-C). We would like to make it clear that our model or manuscript does not claim direct interactions between the Ync13-Rga7-Rng10 module and the glucan synthase complexes but suggest that the module aids in selection of vesicle targeting sites on the plasma membrane. To clarify, we have revised the text to more clearly state that our co-IP and in vitro binding results demonstrate that Rga7 physically associates with Ync13 and Rng10, and that vesicle-associated proteins such as Bgs4 and Ags1 are likely recruited through indirect interactions.

__Minor comments: __1) The manuscript refers to mass spectrometry-based interaction data, but the corresponding dataset is not included. Providing this would enhance transparency and reproducibility.

__Response: __We apologize for the omission. The mass spectrometry data are now shown in Table S1.

2) In Figure 2D, the MBP-6x pull-down lane shows a faint band around 76 kDa. The authors should clarify what this band represents and whether it has any relevance to the study.

Response: We thank the reviewer for noticing this faint band. The weak ~76 kDa band in the MBP-6x pull-down lane is non-specific background binding of MBP and Rga7. We added a note in the figure legend to clarify this point.

3) A quantification graph corresponding to the data in Figure 3G would aid in better interpreting the results and assessing their significance.

Response: We thank the reviewer for this suggestion. We have now added two quantification graphs corresponding to Figure 3G, showing the measured Rng10 signal intensities across the division site. Statistical analysis shows the full width at half maximum (FWHM) is significantly different between WT and ync13D cells, and the figure legend and text have been updated accordingly in the revised manuscript.

4) Figure 4D appears to be missing time legends, which are essential for interpreting the dynamics of the experiment.

Response: We thank the reviewer for noticing this. We apology for making this confusing statement in figure legend. We would like to clarify that the full width at half maximum (FWHM) was calculated from line scans using single time point images from cells at the end of contractile-ring constriction. Those line scans were fitted with the Gaussian distribution to calculate the mean and standard deviation of FWHM. We have updated the figure legend to make it clearer in the revised manuscript.

Reviewer #2 (Significance (Required)):

Nature and Significance of the Advance This study provides a conceptual and mechanistic advance in understanding the spatial and temporal regulation of membrane trafficking during cytokinesis. It identifies a conserved module-Ync13-Rga7-Rng10-that directs the selective tethering and fusion of secretory vesicles at the division site, functioning independently of the exocyst complex. This finding challenges the prevailing model that the exocyst is universally required for vesicle tethering during cytokinesis. While previous work has underscored the roles of TRAPP-II and vesicle trafficking in septum formation (Wang et al., 2016; Arellano et al., 1997; Gerien and Wu, 2018), the precise mechanism targeting vesicles to the division site remained unclear. This study fills that gap by elucidating how Ync13 and Rga7 coordinate vesicle delivery and glucan synthase localization (Liu et al., 2016; Zhu et al., 2018), thereby extending our understanding of septum biogenesis and membrane remodeling beyond actomyosin ring dynamics.

Relevant Audience: This work is relevant to: • Cell biologists investigating cytokinesis, membrane trafficking, or vesicle fusion. • Yeast geneticists interested in conserved cell division pathways. • Researchers focused on SNARE-mediated membrane dynamics and trafficking regulation. • Biomedical scientists exploring analogous processes in mammalian systems, particularly those studying cell division defects linked to disease. The findings have implications across both basic and translational research in cell biology and membrane dynamics.

My Expertise: My research focuses on membrane fusion, specifically the SNARE-mediated fusion process. I study the spatio-temporal regulation of fusion events and the coordinated action of regulatory proteins in determining the structural and functional outcomes of membrane fusion. This background provides me with the framework to critically evaluate studies investigating cytokinesis and trafficking mechanisms at the molecular level.

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

Zhang et al. elucidate key roles of a conserved module the Ync13-Rga7-Rng10 complex in coordinating selective tethering, docking, and fusion of glucan synthases containing vesicles with the plasma membrane, a process crucial for cell wall synthesis and survival of fission yeast at division. Using methods including mistargeting proteins to mitochondria, co-immunoprecipitation, in vitro binding assays, genetic and cellular methods, electron microscopy, and live-cell confocal microscopy, the authors demonstrate that this module controls a vesicle targeting pathway mediated by the TRAPP-II complex and SM protein Sec1, which ensures glucan synthases Bgs4 and Ags1 are deposited at the division site in a spatiotemporal manner.

Major comments: The authors report aberrant accumulation of Bgs4 and Ags1 in the center of the septum after actomyosin ring constriction in ync13del cells and detect no overall defects in Bgs1 distribution there (Figure 4). When similar experiments were analyzed in this paper ( https://pmc.ncbi.nlm.nih.gov/articles/PMC6249806/), Bgs1 distribution and level did change in cells lacking Ync13, although these phenotypes of Bgs1 appeared later that that of Bgs4. I wonder whether there could exist a second wave of Bgs1 arrival in ync13del cells at later time points after ring fully constricts. Could this late recruitment of Bgs1 depends on Rng7 and Rng10, since these protein complexes are enriched in the middle of septum of ync13del cells? Or as the authors mentioned in the Discussion, could Rho GTPase regulated by Rga7 GAP also play a role in Bgs1 accumulation or fusion with the septum in the above scenario, if no obvious accumulation of vesicles is observed in ync13del cells with electron microscopy? How does Bgs1 localize in ync13-19 rng10del double?

Response: We thank the reviewer for this insightful observation. We repeated the experiment to observe the localization of Bgs1 in WT and ync13Δ cells. We confirmed our earlier observation reported in this manuscript that the localization of Bgs1 at rim of the division site and its distribution along the division plane in ync13Δ is not very different from WT, although its intensity is higher and has more variation in ync13Δ cells (Figure above) . As suggested by the reviewer, we did microscopy to test Bgs1 localization in ync13-19 temperature sensitive mutant, rng10Δ, ync13-19 rng10Δ, and WT (Fig. S7). While line scan curves for Bgs1 localization at the division site steep for ync13-19 rng10Δ double mutant, it has no statistically significant difference in FWHM as compared to control WT (Fig. S7). Please note that we used different confocal systems, cameras, and laser powers for Fig. 4, C and E (PerkinElmer UltraVIEW Vox CSUX1) and Fig. S7 (Nikon W1+SoRa), so the FWHMs are not comparable between the two figures.

To test if there is any second wave of Bgs1 localization at the division site, we tracked the fluorescence intensity of Bgs1 throughout 2 h long movies and plotted the Bgs1 intensity profile at the division site over time. The data clearly show only one peak of Bgs1 and no later accumulation at the division site, although Bgs1 intensity has more variation in ync13-19 and ync13-19 rng10Δ cells and the intensity is higher in ync13-19 rng10Δ cells. All these experiments conclude that Ync13-Rga7-Rng10 module impacts the localization of glucan synthases essential for the secondary septum (Bgs4 and Ags1) but not the primary (Bgs1).

Assessments of protein abundance by Western blotting (Figure 3C and 3D) can benefit from some quantifications.

Response: We thank the reviewer for this suggestion. We have now quantified the Western blot bands in Figures 3C and 3D, which have been added as supplementary figures along with the Western blot for Rng10 (Fig. S6, A-C) in the revised figures.

Minor comments: Based on a series of experiments in which mistargeting Rga7 and Rng10 truncations drive Ync13-tdTomato to mitochondria, the authors suggest that Rga7, Rng10, and Ync13 have multivalent interactions with each other. Previous study (https://pmc.ncbi.nlm.nih.gov/articles/PMC6425953/) demonstrated that in cells co-expressing Tom20-GBP mECitrine-Rng10(751-950), Rga7 was efficiently mistargeted to mitochondria. This raises a possibility that Ync13 mistargeted by mECitrine-Rng10(751-1038) could come from Rga7 that strongly associated with Rng10(751-1038) on mitochondria. I wonder whether the authors could compare some of their truncation mistargeting experiments in the original manuscript and the ones in which either Rga7 or Rng10 is deleted, e.g. Tom20-GBP mECitrine-Rng10(751-1038) experiments in rga7del cells, if cells are still viable in this genetic background.

Response: We thank the reviewer for this insightful suggestion. We tested the mistargeting of mECitrine-Rng10(751–1038) in rga7Δ tom20-GBP cells and found that Ync13-tdTomato could not be recruited to mitochondria. This indicates that Ync13 cannot interact with Rng10 C-terminus independently of Rga7, supporting the Alphafold3 modeling and our proposed model that Rga7 interacts with Rng10 through the BAR domain while with Ync13 through the GAP domain. We have added the new data to the revised manuscript (Fig. S4H and associate text) and included a brief discussion highlighting that Rga7 is required for the Rng10–Ync13 interaction. We removed the mentioning of multivalent interactions in the manuscript to minimize confusion.

It is interesting that rga7del rng10del double mutants can survive better in EMM or YES with sorbitol. I wonder this would allow the authors to test whether the interaction between Ync13 and Sec1 is modulated by the presence of Rga7 and Rng10 or even the entire vesicle? Does mistargeted Ync13 overexpressed using the 3nmt1 promoter is still capable of driving Sec1 to mitochondria in rga7del rng10del cells.

Response: We thank the reviewer for this suggestion. While we did not succeed in constructing the pentamutant deleting both rga7 and rng10 and mislocalizing Ync13 to mitochondria, we were able to make a quadruple mutant deleting rng10 and mislocalizing Ync13 to mitochondria. We tested whether mistargeted Ync13 overexpressed using the 3nmt1 promoter can recruit Sec1 to mitochondria in rng10Δ cells. Our results show that overexpressed Ync13 is still able to drive Sec1 localization to mitochondria without Rng10 (Fig. S2G). This suggests that Rng10 (together with Rga7) primarily functions to recruit and position Ync13 at the division site rather than being strictly required for the interaction between Ync13 and Sec1. This is also consistent with our Pmo25-GBP mislocalization experiments where we found that rga7Δ 3nmt1-mECitrine-ync13 cells even under the repressed condition for the 3nmt1 promoter can partially rescue the lysis phenotype of rga7Δ cells (Figure 6).

The endogenous level of Ync13 is not particular high. Is this low level of Ync13 crucial for its function? Does mildly elevated level of Ync1 promote vesicle fusion at the closing septum?

Response: We thank the reviewer for this insightful question. To test if there is a correlation between Ync13 levels and vesicle fusion at the division site, we mildly overexpressed Ync13 from the 3nmt1 promoter in YE5S rich medium without additionally added thiamine to obtain cells with different Ync13 levels (the rich medium has some residual amount of thiamine, which partially represses the nmt1 promoter) and then tracked the Rab11 GTPase Ypt3 labeled vesicles. This resulted in increased levels of Ync13 as well as Ypt3 at the division site (Fig. S8B). We measured the Ync13 intensity at division site and counted the number of Ypt3 vesicles reaching the division site in 2-minute continuous movie at the middle focal plane. We observed that increasing Ync13 level promoted the tethering and accumulation of Ypt3 vesicles at the division site until it reached a plateau (Fig. S8B). Thus, the Ync13 level is important for vesicle fusion at the division site. Collectively, Ync13, working with Rga7 and Rng10, plays an important role in vesicle targeting and fusion on the plasma membrane at the division site during cytokinesis. This is consistent with our results that overexpressed Ync13 can mislocalize Sec1 to mitochondria in rng10Δ (Fig. S2G) and can rescue the rga7Δ (Fig. 6).

Reviewer #3 (Significance (Required)):

Most of conclusions are well supported by a combination of methods. Out of curiosity, I wonder how much of Bgs4 or Smi1 detected in Co-IP experiments exist in the vesicle-bound form. The authors propose a very interesting working model that addresses several key challenges in achieving vesicle targeting specificity when timely delivery of various enzymes to their respective spatial locations along the primary and secondary septum must be orchestrated. I think this manuscript will be of interest to a broad audience.

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Referee #3

Evidence, reproducibility and clarity

Zhang et al. elucidate key roles of a conserved module the Ync13-Rga7-Rng10 complex in coordinating selective tethering, docking, and fusion of glucan synthases containing vesicles with the plasma membrane, a process crucial for cell wall synthesis and survival of fission yeast at division. Using methods including mistargeting proteins to mitochondria, co-immunoprecipitation, in vitro binding assays, genetic and cellular methods, electron microscopy, and live-cell confocal microscopy, the authors demonstrate that this module controls a vesicle targeting pathway mediated by the TRAPP-II complex and SM protein Sec1, which ensures glucan synthases Bgs4 and Ags1 are deposited at the division site in a spatiotemporal manner.

Major comments:

The authors report aberrant accumulation of Bgs4 and Ags1 in the center of the septum after actomyosin ring constriction in ync13del cells and detect no overall defects in Bgs1 distribution there (Figure 4). When similar experiments were analyzed in this paper ( https://pmc.ncbi.nlm.nih.gov/articles/PMC6249806/), Bgs1 distribution and level did change in cells lacking Ync13, although these phenotypes of Bgs1 appeared later that that of Bgs4. I wonder whether there could exist a second wave of Bgs1 arrival in ync13del cells at later time points after ring fully constricts. Could this late recruitment of Bgs1 depends on Rng7 and Rng10, since these protein complexes are enriched in the middle of septum of ync13del cells? Or as the authors mentioned in the Discussion, could Rho GTPase regulated by Rga7 GAP also play a role in Bgs1 accumulation or fusion with the septum in the above scenario, if no obvious accumulation of vesicles is observed in ync13del cells with electron microscopy? How does Bgs1 localize in ync13-19 rng10del double?

Assessments of protein abundance by Western blotting (Figure 3C and 3D) can benefit from some quantifications.

Minor comments:

Based on a series of experiments in which mistargeting Rga7 and Rng10 truncations drive Ync13-tdTomato to mitochondria, the authors suggest that Rga7, Rng10, and Ync13 have multivalent interactions with each other. Previous study (https://pmc.ncbi.nlm.nih.gov/articles/PMC6425953/) demonstrated that in cells co-expressing Tom20-GBP mECitrine-Rng10(751-950), Rga7 was efficiently mistargeted to mitochondria. This raises a possibility that Ync13 mistargeted by mECitrine-Rng10(751-1038) could come from Rga7 that strongly associated with Rng10(751-1038) on mitochondria. I wonder whether the authors could compare some of their truncation mistargeting experiments in the original manuscript and the ones in which either Rga7 or Rng10 is deleted, e.g. Tom20-GBP mECitrine-Rng10(751-1038) experiments in rga7del cells, if cells are still viable in this genetic background.

It is interesting that rga7del rng10del double mutants can survive better in EMM or YES with sorbitol. I wonder this would allow the authors to test whether the interaction between Ync13 and Sec1 is modulated by the presence of Rga7 and Rng10 or even the entire vesicle? Does mistargeted Ync13 overexpressed using the 3nmt1 promoter is still capable of driving Sec1 to mitochondria in rga7del rng10del cells.

The endogenous level of Ync13 is not particular high. Is this low level of Ync13 crucial for its function? Does mildly elevated level of Ync1 promote vesicle fusion at the closing septum?

Significance

Most of conclusions are well supported by a combination of methods. Out of curiosity, I wonder how much of Bgs4 or Smi1 detected in Co-IP experiments exist in the vesicle-bound form. The authors propose a very interesting working model that addresses several key challenges in achieving vesicle targeting specificity when timely delivery of various enzymes to their respective spatial locations along the primary and secondary septum must be orchestrated. I think this manuscript will be of interest to a broad audience.

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

This paper provides a comprehensive analysis of the roles of Rng10, Rga7, and Ync13 in cytokinesis using fission yeast as a model system. The authors demonstrate that Ync13/Rna7/Rng10 not only interact with each other but also associate with components of glucan synthases, which are essential for secondary septum formation but not for the primary septum. They further show that Ync13 is involved in exocytosis through its interaction with Sec1 and plays a role in membrane trafficking via interaction with the TRAPP-II complex. Collectively, their findings reveal a coordinated mechanism that ensures the timely formation of the secondary septum during cytokinesis, as deletion of these proteins disrupts septum formation and leads to cell lysis.

The conclusions drawn in this paper are well-supported by the data, with a clear methodology and robust statistical analyses that enhance reproducibility. However, I have the following major and minor comments:

Major Comments

1. The authors propose that Ync13, Rng10, and Rga7 interact to form a protein complex, supported by their mislocalization studies. While these findings are suggestive, additional co-immunoprecipitation (co-IP) data specifically demonstrating a direct interaction between Ync13 and Rng10 would strengthen the claim.
2. It remains unclear whether Ync13 directly interacts with components of the glucan synthase complex (Bgs4/Ags1), or if this association is mediated through other factors (Rng10, Rga7). Clarifying the nature of this interaction would significantly enhance the mechanistic insight.

Minor comments:

1. The manuscript refers to mass spectrometry-based interaction data, but the corresponding dataset is not included. Providing this would enhance transparency and reproducibility.
2. In Figure 2D, the MBP-6x pull-down lane shows a faint band around 76 kDa. The authors should clarify what this band represents and whether it has any relevance to the study.
3. A quantification graph corresponding to the data in Figure 3G would aid in better interpreting the results and assessing their significance.
4. Figure 4D appears to be missing time legends, which are essential for interpreting the dynamics of the experiment.

Significance

Nature and Significance of the Advance

This study provides a conceptual and mechanistic advance in understanding the spatial and temporal regulation of membrane trafficking during cytokinesis. It identifies a conserved module-Ync13-Rga7-Rng10-that directs the selective tethering and fusion of secretory vesicles at the division site, functioning independently of the exocyst complex. This finding challenges the prevailing model that the exocyst is universally required for vesicle tethering during cytokinesis. While previous work has underscored the roles of TRAPP-II and vesicle trafficking in septum formation (Wang et al., 2016; Arellano et al., 1997; Gerien and Wu, 2018), the precise mechanism targeting vesicles to the division site remained unclear. This study fills that gap by elucidating how Ync13 and Rga7 coordinate vesicle delivery and glucan synthase localization (Liu et al., 2016; Zhu et al., 2018), thereby extending our understanding of septum biogenesis and membrane remodeling beyond actomyosin ring dynamics.

Relevant Audience:

This work is relevant to:

• Cell biologists investigating cytokinesis, membrane trafficking, or vesicle fusion.
• Yeast geneticists interested in conserved cell division pathways.
• Researchers focused on SNARE-mediated membrane dynamics and trafficking regulation.
• Biomedical scientists exploring analogous processes in mammalian systems, particularly those studying cell division defects linked to disease. The findings have implications across both basic and translational research in cell biology and membrane dynamics.

My Expertise:

My research focuses on membrane fusion, specifically the SNARE-mediated fusion process. I study the spatio-temporal regulation of fusion events and the coordinated action of regulatory proteins in determining the structural and functional outcomes of membrane fusion. This background provides me with the framework to critically evaluate studies investigating cytokinesis and trafficking mechanisms at the molecular level.

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

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Referee #1

Evidence, reproducibility and clarity

In this paper, the GFP-GBP system for mistargeting protein localization was used in fission yeast cells to discover new protein interactions involved in vesicular trafficking during cytokinesis. This approach uncovered a new association between the F-BAR protein Rga7 and its binding partner Rng10 with the Munc13 protein Ync13 at the cell division site. Additional associations were observed between Rga7-Rng10, Ync13 and the glucan synthases Ags1 and Bgs4, and the vesicle fusion protein Sec1. These interactions identified by the GFP-GBP system were further supported by co-immunoprecipitation experiments and by defining localization dependencies with live cell imaging in a variety of mutant strains. The imaging data are all of high quality and for the most part support the conclusions. However, in my opinion some of the interpretations are overstated, and the manuscript would benefit from providing additional mechanistic information. Major and minor recommendations are outlined below.

Major suggestions

1. The co-IP data are interpreted to suggest that all the above-mentioned proteins form a single "big complex." However, as noted in the manuscript and reflected in the model, the multipass integral membrane proteins Bgs4 and Ags1 are embedded in the vesicle membrane and likely only indirectly associate with the scaffold Rga7-Rng10 via Ync13, without forming a 'complex'. One would expect the entirety of these vesicle contents to co-IP if the model is correct. The first paragraph of page 11 should be revised to more clearly reflect this scenario and to align with the proposed model.
2. Can Ync13 be artificially directed or tethered to the division site independently of Rga7-Rng10 (e.g., via Imp2)? If so, can this rescue the phenotypes of rga7Δ cells? This experiment could clarify whether Ync13 is the key functional effector of the Rga7-Rng10 complex.
3. The authors should consider structural or computational modeling of the proposed Rga7-Rng10-Ync13 complex. Such analysis could offer insight into how these components interact and strengthen the proposed model.

Minor text edits

1. Define "SIN" in the discussion section for clarity.
2. Figure S3, the protein schematics should start at residue "1" and not "0".
3. Mass spectrometry data referenced in the text are not provided in the manuscript.
4. In Figure 4A. The Ags1 rim localization does not appear decreased as the authors claim.
5. On page 13: "both Rga7 and Rng10 can mistarget Trs120 to mitochondria."

Minor figure edits

1. Consider inverting single-channel images to display fluorescence on a white background, which would improve visual clarity.
2. The Figure 1 legend should describe the experimental setup rather than restating conclusions.
3. Reduce the number of arrows indicating co-localization in microscopy images; highlighting 1-2 representative examples is sufficient and less visually cluttered.
4. Figure 3F, the scale bar is listed as 5 μm in the legend but it appears to my eye to be 2 μm.
5. The orientation of Bgs4/Smi1 should be inverted in the schematic within vesicles so that Smi1 is always on the cytoplasmic side.
6. Also in the schematic, Mid1 is not at the constricting CR and therefore needs to be removed.

Significance

From the data presented in the manuscript, it is proposed that Rga7 and Rng10 form a scaffold at the division site for delivery of exocytic vesicles marked by the TRAPPII complex but not the exocyst complex. Further, it is proposed that these vesicles deliver specifically the glucan synthases necessary for septation. Overall, this study builds on previous work from the Wu lab to clarify how the TRAPPII-decorated vesicles are specifically delivered to the cell division site, adding some new information about vesicle trafficking regulation during cytokinesis. It also provides new insight into the role of a F-BAR scaffold protein.

This paper will be of interest to those studying cytokinesis and also those studying mechanisms of intracellular trafficking.

Reviewer expertise: Cell division, signaling, membrane biology

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Reply to the reviewers

Manuscript number: RC-2025-03094

Corresponding author(s): Saurabh S. Kulkarni

1. General Statements

We thank the reviewers for their strong praise of the manuscript, highlighting its rigor, depth, and conceptual importance. They consistently described the study as a beautiful, fascinating, and conceptually strong piece of work that addresses a timely question in multiciliated cells. They also noted the high quality of the data, careful quantification, and the use of multiple genetic and pharmacological approaches, all of which improve the reproducibility and credibility of the findings. Importantly, they emphasized the novelty of discovering a direct mechanistic link between Piezo1-mediated mechanotransduction and Foxj1-driven transcriptional control of multiciliation, representing a significant breakthrough for both the cilia field and mechanobiology more broadly. Collectively, these strengths highlight the manuscript’s wide impact and make it highly suitable for publication in a high-impact journal.

2. Description of the planned revisions

Reviewer #1:

There are two experiments that would significantly strengthen these claims.

• First if their model is correct then even short term treatment with Yoda1 should induce the pathway and effect centriole numbers. While I appreciate the challenge of long term Yoda1 treatment its not clear to me why it would be needed if short term treatment is setting off the transcriptional cascade. Yoda is used throughout the paper to induce all the pathways but we don't know if it actually induces the phenotype. I think this should be addressed with either short term treatments or a dose response to find a dose that does not lead to skin pealing. It is hard to ignore this obvious deficiency.
• Second, the model predicts that all of this is to regulate Foxj1 levels to regulate the subtle balance between cell size and centriole number. If this is correct, then the overexpression of Foxj1 should have a profound effect on centriole number in multiciliated cells. This is such an easy experiment that would validate many of the claims. RESPONSE:

We recognize that the reviewer is asking us to test the sufficiency of the pathway with these comments: “If their model is correct, then they should be able to activate the pathway in one way or another to stimulate centriole number. This is a significant limitation to their overall model.” And “If this is correct, then the overexpression of Foxj1 should have a profound effect on centriole number in multiciliated cells.”

To address reviewers’ suggestions, we will perform the following experiments.

1. A brief exposure (15 and 30 mins) to Yoda1 and wait for 3 hours to examine changes in centriole amplification. This will avoid skin peeling from long-term exposure.
2. A brief exposure to Yoda1 (15 mins) followed by a 30-minute wait period, and the cycle repeats a total of 4 times for a total of 3 hours to examine centriole amplification.
3. The above two experiments will also be done in a constitutively active-Yap background to increase the probability that synergistic activation can lead to centriole amplification.
4. Although Foxj1 is essential for multiciliogenesis, it is not sufficient to induce multiciliogenesis, as shown by multiple previous studies. Therefore, we do not expect overexpression of Foxj1 to have a profound effect on centriole number. While we will conduct the experiments because we truly want to address the suggestions and gain insight into the answers ourselves, we respectfully ask the Reviewer to consider the following responses to their concern.

Yoda1 sufficiency: We agree that testing whether acute Yoda1 treatment can induce centriole amplification is an important question. We will conduct experiments with short-pulse and cyclic Yoda1 exposure, including in a constitutively active-YAP background (listed above), to address this possibility. However, several challenges complicate interpretation: (i) PIEZO1 adapts and desensitizes upon activation, (ii) transient signaling may be sufficient to cause secondary signaling but insufficient to drive stable transcriptional programs required for amplification, and (iii) centriole number is inherently variable, making modest effects difficult to resolve. However, we must recognize that failure to observe sufficiency under these conditions would not invalidate the model for two reasons: 1) absence of evidence is not evidence of absence, and thus, we may not have found the right experimental design. 2) PIEZO1–YAP is a necessary input but not sufficient on its own, as elaborated below. For both reasons, we are very careful about the interpretation of results in the manuscript, which shows that this pathway is necessary for centriole amplification using loss-of-function approaches.

Foxj1 overexpression: Foxj1 is a well-established regulator essential for motile and multiciliogenesis across species (Xenopus, zebrafish, mouse). Loss of Foxj1 reduces cilia number in MCCs, but its activation alone does not have a profound effect on ciliogenesis/cilia number in MCCs. This is because Foxj1 is a part of a larger network essential for multiciliogenesis. This parallels the behavior of other transcriptional regulators, such as Myb, where loss of function impairs centriole amplification, but overexpression does not drive the formation of supernumerary centrioles. Both studies are seminal discoveries in the field of ciliogenesis, but they did not demonstrate the sufficiency of these molecules/pathways. Thus, our results, demonstrating that Foxj1 is necessary to induce tension-dependent centriole amplification, are significant, as the reviewer mentioned. The lack of Foxj1 sufficiency to induce centriole amplification is not a deficiency of the study, but rather evidence that Foxj1 is a part of a larger network essential for tension-dependent centriole amplification.

Necessity versus sufficiency: We respectfully emphasize that sufficiency is not a prerequisite for demonstrating the significance of a pathway. Mechanochemical signaling is inherently complex, involving many mechanosensitive proteins and pathways. In our case, mechanical stretch increases centriole amplification, with PIEZO1–YAP signaling identified as a key mediator. However, we do not claim that PIEZO1–YAP alone is sufficient. Other pathways, including cadherin-mediated junctions, F-actin–myosin contractility, integrin–focal adhesion signaling, and nuclear mechanotransduction, likely contribute and may regulate unique downstream effectors that collectively promote centriole amplification. Therefore, PIEZO1–YAP should be regarded as one essential component within a larger network.

__TIMELINE: __We will perform these additional proposed experiments. Since the first author, a postdoctoral researcher on this manuscript, has started a new job and will be coming in on weekends to complete the experiments, we estimate it will take approximately 2-3 months to finish them.

Reviewer #2:

1. Considering the Yap-piezo mechanism of action, the authors' logic for the selection of myb, foxj, plk4 and ccno as transcriptional targets is clear, but the HCR-derived signal and the differences seen in the yap morphants are not very strong, notwithstanding the statistical significance. There appear to be distinct subgroups within the treated populations (in Figure S6B, although these data seem quite different in Fig. 7H, so a comment on the technical differences might be helpful), so that the extent to which Yap1 regulates (Myb-)Foxj1 expression in MCCs is not clearly demonstrated by this experiment. Related to this point, it is unclear why 20-25% of the yap1/ piezo1 MO-treated embryos do not show a decline in FOXj1 in Fig. 6, given the qualitative nature of the scoring. Assuming the KD penetrance would vary on a cell-to-cell basis, rather than an embryo-to-embryo basis, this may suggest that there are additional relevant targets (some of which are discussed by the authors). Single-cell analysis might be a way to address this; however, this is not a trivial experiment, it might be sufficient to include a caveat in the text. Furthermore, the conclusion that Foxj1 regulates centriole amplification in a tension-dependent manner is well-supported by the data.

RESPONSE: We appreciate the reviewer’s thoughtful observation. Differences in the expression of Foxj1 from experiment to experiment are possible due to a combination of factors, including heterogeneity in MCC development across embryos, slightly different embryonic stages, differences in embryo quality between fertilizations, and variability in morpholino delivery and knockdown penetrance, which can occur both across embryos and on a cell-to-cell basis within an embryo. We also note that technical aspects of HCR RNA-FISH, such as proteinase K treatment and washing steps, can affect signal intensity, potentially contributing to the appearance of distinct subgroups within treated populations.

We agree that single-cell analysis would be a powerful way to dissect these differences, but as the reviewer notes, this is not a trivial experiment and is beyond the scope of the present study. We have therefore added clarifications in the text and discussion to acknowledge these sources of variability and to highlight the possibility of parallel pathways regulating foxj1 expression.

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Controls for the knockdowns by the various MOs should be provided.

RESPONSE: We appreciate the reviewer’s comment. The piezo1 MO has been previously established in Kulkarni et al. (2021). Additionally, the current manuscript includes MO control experiments for both erk2 and yap1, through KD at the 1-cell stage using the MO oligonucleotide, followed by mosaic-rescue with the respective WT RNA constructs (mCherry-ERK2 and yap1-GFP) and a nuclear tracer molecule such as H2B-RFP (Fig. 5, E-H, Fig. S5, C&D, Fig. 3, D-F). The mosaic-rescue is a robust experiment that provides an internal control within the same embryo, thereby avoiding differences that may arise due to embryo-to-embryo variability, embryo quality, or differences in fertilization batches. This approach also serves as a valuable tool for detecting cell-autonomous effects, providing a clear readout against uninjected neighboring cells, as the injected cells are labeled with a tracer. We will perform a similar mosaic-rescue experiment for the foxj1 MO.

TIMELINE: We will conduct mosaic-rescue experiments for the foxj1 MO. We will need 1 month to complete the experiment.

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__Minor comments:

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Autocorrection of ERK1/2 or MEK1/2 pathways to 1/2 should be avoided. – We are unclear on this comment. Can reviewer please clarify what they mean.

Reviewer # 3

Major concerns

1- The presented data do not yet establish a specific, direct pathway linking mechanotransduction to centriole number, because the molecular players tested (PIEZO1, Ca²⁺, PKC, ERK, YAP, Foxj1) are highly pleiotropic. As such, the observed centriole number phenotypes, and some of the major conclusions, could be indirect. It is therefore critical to test the specificity and causality of the proposed pathway. This could be done with the authors' own strategies and/or with the following potential approaches:

• Genetic dependency and sufficiency tests: It could be shown that Yoda1 has no effect in PIEZO1 loss-of-function MCCs, and that wild-type PIEZO1, but not conductance-ad PIEZO1 pore mutants restores Yoda1 responsiveness across centriole number, pERK, and YAP readouts. For example, PIEZO1 C terminus was shown to govern Ca²⁺ influx and ERK1/2 activation. Comparing full length PIEZO1 with a C terminal deletion in MCC restricted rescue; loss of rescue of centriole amplification and ERK/YAP activation with the C terminal deletion can provide a genetics anchored specificity test beyond broad inhibitors.

RESPONSE:

• To address the reviewer’s concern, we will test whether Yoda1 affects ERK and Yap activation when Piezo1 is depleted. We appreciate the reviewer’s thoughtful suggestion to employ genetic rescue experiments with Piezo1 mutants. Unfortunately, these are not technically feasible in Xenopus, as the Piezo1 coding sequence is exceptionally large (~7.5 kb)____, and repeated attempts by our group to generate and express stable, translatable transcripts have been unsuccessful. To address genetic dependency and specificity despite these technical barriers, we have employed a combination of orthogonal strategies that together provide strong genetic and mechanistic evidence:

• Mosaic loss-of-function experiments (Fig. 1) demonstrate that Piezo1 regulates centriole number in a cell-autonomous manner, ruling out global epithelial or indirect tissue-wide effects.

• Pharmacological activation/inhibition with Piezo1-specific agonist (Yoda1) and inhibitors (GSMTx4, gadolinium) produced consistent phenotypes, including activation of downstream ERK and YAP readouts. Notably, Yoda1 is a Piezo-specific agonist, not a broad pharmacological agent.
• Downstream pathway dissection (calcium chelation, PKC inhibition, ERK2 depletion, and YAP1 knockdown/rescue) consistently converges on the same phenotypes, reduced centriole amplification and altered Foxj1 expression, providing multiple independent lines of evidence that the Piezo1–Ca²⁺–PKC–ERK–YAP axis specifically controls centriole number.

• Positive feedback regulation of Piezo1 expression by YAP/Foxj1 (Fig. 7) further strengthens the argument for a pathway-specific role rather than pleiotropic, indirect effects. Taken together, while full-length Piezo1 rescue experiments are technically not possible in Xenopus due to gene size constraints, our data employ state-of-the-art genetic, pharmacological, and orthogonal functional assays to rigorously test pathway specificity. These complementary approaches provide compelling evidence for the causal role of Piezo1-mediated mechanotransduction in centriole number control in MCCs.

• Downstream bypass/rescue experiments: In PIEZO1 loss-of-function or BAPTA conditions, can enforcing MEK/ERK activation or YAP rescue centriole number defect? Conversely, can MEK inhibitors block Yoda1-induced effects.

RESPONSE: We appreciate the reviewer’s insightful questions.

• We will express CA Yap in the Piezo1 KD background to assess if we can rescue centriole number. We also note that the converse experiment has already been performed in our study: 1) PKC inhibition abolishes Yoda1-induced ERK phosphorylation and nuclear localization (Fig. 2), 2) both MEK inhibition and ERK2 depletion block Yoda1-induced Yap activation and nuclear entry (Figs. 4, S2). Thus, we have directly demonstrated that MEK inhibition prevents Yoda1-induced effects, satisfying this aspect of the reviewer’s concern.

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2- Image quantification and analysis must be described in greater detail in the Methods section, as they are central to the major conclusions of the manuscript. For example, the authors should explain how nuclear, cytoplasmic, and centriole segmentation were performed, and how relative protein levels in the nucleus versus the cytoplasm (e.g., YAP, volume- or area-based) were quantified. Specifically, the thresholds and segmentation criteria applied to different cellular structures under various conditions, as well as the use of Imaris and other software, should be clearly detailed.

RESPONSE: We will describe the methods in greater detail.

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3- PIEZO1 mRNA was shown to incrase in a Foxj1 linked feedback loop. Does this increase translate into an increase in total protein levels?

RESPONSE: If the reviewer is referring to Figure 7B, that is the Piezo1 antibody, so yes, the Piezo1 protein levels have increased.

If the reviewer is referring to Figure 7C and D, we show that loss of Foxj1 leads to a reduction in Piezo1 mRNA expression.

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4- Is the proposed signaling cascade active in mammalian multiciliated cells (e.g., airway epithelium). If possible, testing this by using one of the major players of the pathway as a readout such as as ERK phosphorylation, YAP nuclear localization in mammalian MCCs will reveal whether regulation of centriole number through this pathway is conserved and would strengthen the generality.

RESPONSE: We agree with the reviewer that testing conservation of this pathway in mammalian MCCs is of great interest. Indeed, another group is currently investigating the role of Yap in the mammalian airway epithelium; in their temporally controlled Yap knockout model (the global Yap KO being embryonic lethal), they observed that Yap loss led to a reduction in centriole number. To avoid overlap and direct competition with this ongoing work, we chose to focus our efforts on Xenopus.

Importantly, Xenopus has become a widely recognized and powerful system for MCC biology, enabling mechanistic dissection of centriole amplification and ciliogenesis. Several key discoveries in the field, including the identification of MCIDAS as a master regulator of MCC fate, were first made in Xenopus before being validated in mammals. Similarly, our study provides a mechanistic framework in Xenopus that can inform and guide ongoing studies in the mammalian airway.

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5- Throughout the results section, there are multiple times where authors raised specific hypothesis about their data (e.g. foxj1 regulation of number control, apical actin/YAP). However, they have not tested them. These hypothesis are very exciting and if possible, testing experimentally, would strengthen the conclusions associated with them.

RESPONSE: We are not sure what the reviewer means here by “authors raised specific hypothesis about their data (e.g., foxj1 regulation of number control, apical actin/YAP). However, they have not tested them”,

BECAUSE:

• Foxj1 regulation of centriole number: We demonstrate a clear reduction in centriole number upon Foxj1 depletion, and importantly, we extend this finding by showing that the reduction is tension-dependent (Fig. 6). We will perform a rescue assay to demonstrate the specificity.
• Foxj1 and YAP: We never claimed that Foxj1 regulates YAP expression, and this is not part of our proposed model. Instead, our data show that Piezo1–ERK–YAP signaling regulates Foxj1
• Foxj1 and apical actin: Foxj1 regulation of apical F-actin has already been established in prior work, and in our study, we clearly observe reduced apical actin intensity in Foxj1-depleted MCCs (Fig. 6). To further strengthen this conclusion, we will provide a quantitative analysis of apical actin intensity in Foxj1 morphants. ********************************************

__TIMELINE: __We will perform these additional proposed experiments. Since the first author, a postdoc on this manuscript, has started a new job and will be coming in on weekends to finish the experiments, we estimate it will take approximately 2-3 months to complete them.

Minor comments

MCC vs non MCC identification (Fig. 1): Clarify how non MCCs were distinguished from MCCs (e.g. markers/criteria). – Can the reviewer please clarify which panel or panels? Or provide more specific text that needs to be changed.

Add the Kintner group reference linking motile cilia number and centriole number in Xenopus MCCs.– Can the reviewer clarify where and which reference? Thank you.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

Reviewer 2

Major comments:

1. It should be clarified whether the immunoblots and the related quantitations in Figs. 2 and S2 are all from separate blots/ exposures. If so, they are not useful as controls, and these blots should be repeated with the relevant samples analyzed in parallel. Size markers and labels should be included (2B, 2G; S2B and S2G). An increase in total ERK would alter the interpretation of the increase in nuclear pERK in the IF experiments. RESPONSE: We thank the reviewer for raising this important point regarding clarification of the immunoblots. All experimental groups were analyzed in parallel with their corresponding controls. Because the primary antibodies for pERK and ERK were both raised in rabbit, we optimized our workflow to prevent protein loss during stripping and to ensure accurate visualization. Specifically, lysates from each experimental group were loaded in duplicate on the same gel, separated by a molecular weight ladder that served as a reference point. After transfer, the blot was cut along the ladder, and the two halves were processed in parallel: one probed with anti-pERK and the other with anti-ERK. This strategy ensured that all samples from a single experiment (e.g., Control and Yoda1-treated groups) were analyzed under identical conditions, with staining and imaging performed together at the same exposure. To enhance clarity, we have provided this data as __uncut, full-length __as Supplemental Figure 7 (Figure S7) in the revised revision.

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Minor comments:

1. Reference list should be checked for completeness; some citations lack journal/ volume/ page/ year details. – We have corrected the references.
2. An 'overexposed' version of the image selected for centrioles in Figure 5F might be included with the Chibby-BFP at the same level as in the other figures. At present, the Yap KD cell in the image appears to have normal centrioles; this is potentially confusing, even though the authors clearly explain the matter in the text. – __We have added a new panel to Fig. 5F to avoid confusion.

__ 3. It might be clearer to present injected/ uninjected in the same orientation in Fig. 6A and B. – __Unfortunately, that is not possible because the injected and uninjected sides are left and right, and they cannot be in the same orientation.

__ 4. Figure 7B lacks the schematic described in the figure legend. – We have removed the Schematic sentence from the figure legend. That was an error on our side. Thank you for catching it.

Reviewer 3

1. Abstract: "how MCCs regulate centriole/cilia numbers remains a major knowledge gap" overstates the field; please soften to reflect recent advances (mechanics/apical area scaling; PIEZO1 implication). – We changed the text to “incompletely understood”.
2. GsMTx4 rationale: State that GsMTx4 is a spider venom peptide that inhibits cationic mechanosensitive channels (including PIEZO1) and justify its use alongside Yoda1.– GsMTx4 was used in the previous manuscript, and its use was justified there. Here, we are only comparing the results. However, we have added a sentence describing what GSMTx4 is. We have also included a sentence explaining the use of Yoda1. “GsMTx4, a spider venom peptide used in our previous study, inhibits cationic mechanosensitive channels, including Piezo1.”

“For this experiment, we used the Piezo1 channel-specific chemical agonist, Yoda1, to increase the sensitivity of Piezo1 and upregulate calcium entry into cells”

Timeline statement: "Centriole amplification to migration and apical docking takes ~4-5 h (personal observation)" is not appropriate; either cite time lapse literature or include your own time lapse data.– We have added a reference that showed imaging for 2 hours, but it was not enough to capture the entire process from intercalation to maturation, so we also kept “personal observation” still in the manuscript. We are unaware of any study that has done time-lapse imaging for 4 hours to capture the entire process of centriole amplification.

Redundancy: The description of Yoda1 as a channel specific agonist is repeated; keep only once.- Removed

"WT yap1 GFP construct previously used by Dr. Lance Davidson ..." should move construct description to Methods and keep only the citation in Results.– We moved it to Methods.

"(Unpublished data; Dr. Mahjoub)" should be removed unless data are shown.- Removed

Replace "as shown previously in our eLife paper" with "as we previously showed or shown previously (Kulkarni et al., 2021)".– We have made the change.

The two hypotheses for how Foxj1 could regulate number under tension (actin remodeling vs. transcriptional control of amplification genes) belong in the Discussion unless tested. Moreover, the part on the discussion on yap sequestration by apical actin and the two possibilities presented also should go do discussion. – We have moved both to the discussion section.

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Reviewer 3

1- The hypothesis about the centriole pool of Piezo as the mechnosensor for centriole number regulation is very exciting and novel. Can localization controlled variants be used to test whether a centriole associated pool directly senses tension for number control (for example, centrosome targeted PIEZO1 via a PACT tag). Alternatively, broad cellular Ca sensors (GcaMP) or centrosome proximal Ca sensors (e.g., PACT GCaMP) can be used detect local calcium microdomains during tethering or Yoda1 treatment.

RESPONSE: We appreciate the reviewer's curiosity and excitement; however, these experiments will not alter the conclusion of this paper and will be part of the next study, which aims to delve deeper into how different pools of Piezo1 at centrioles versus cell junctions function in MCCs. To that point, we had thought about these experiments. As mentioned earlier, the Piezo1 coding sequence is exceptionally large (~7.5 kb)____, and repeated attempts by our group to generate and express stable, translatable transcripts have been unsuccessful. Thus, the idea of centrosome-targeted PIEZO1 via a PACT is very exciting; however, it is not technically feasible. Beyond size, PIEZO1 is a trimeric, large plasma-membrane mechanosensitive channel that requires proper ER processing and bilayer incorporation. PACT localizes cargo to the centriole/pericentriolar material, not a membrane compartment; thus, a PACT-anchored PIEZO1 would be membrane-mismatched and almost certainly nonfunctional even if expressed/

Second, Centrosome-proximal GCaMP (PACT-GCaMP) would show correlation, not causation. This experiment does not address the question “centriole pool of Piezo as the mechanosensor for centriole number regulation”. It will only show if the Ca2+ influx is happening at the basal bodies, but not whether and how that Ca2+ is essential for centriole amplification. For this purpose, we will need to find a way to block Ca2+ influx specifically at basal bodies, rather than junctions, which will require extensive controls.

We do not claim that any specific Piezo1 or Ca2+ pool is critical for controlling centriole number and thus the suggested experiment would not alter the manuscript's conclusions. We therefore view the above as exciting future directions rather than prerequisites.

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2- Because the proposed pathway is tension-sensing and YAP pathway is tightly linked to the actin cytoskeleton, the role of actin cysoskeleton in the proposed pathway should be tested directly. The authors mention different hypothesis around actin but has not tested them in the manuscript. For example, actin-depedent sequestration of Yap at the apical surface is intriguing. Does actin polymerization induced by drugs release Yap from the apical surface?

RESPONSE: We would like to thank the reviewer for their suggestion. As per the reviewers' suggestion, we have moved this section to discussion, stating that “In the future, we plan to address this question by examining how Yap is sequestered by apical actin.”.

However, we appreciate the reviewer’s enthusiasm and would like to share some experiments we are thinking/planning of to test the hypothesis.

We plan to examine if the actin polymerization or contractility is responsible for Yap sequestration/release from the apical surface with the following experiments: 1) if the Yap is displaced by Jasplakinolide treatment, which stabilizes filamentous actin, 2) use of ROCK inhibitor to decrease contractility in the absence or presence of Yoda1, 3) Use genetic constructs such as Shroom3 to increase ROCK-mediated contractility to observe changes in Yap localization and dynamics.

Although these experiments are interesting, they do not alter the conclusion of the current manuscript, and they represent future directions for our research.

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Referee #3

Evidence, reproducibility and clarity

This manuscript investigates how mechanical tension is transduced into centriole amplification in Xenopus multiciliated cells (MCCs). Building on prior work that centriole number scales with MCC apical area and that this scaling depends on PIEZO1, the study proposes that MCCs repurpose a canonical mechanochemical axis-PIEZO1 → Ca²⁺/PKC → ERK1/2 → YAP → Foxj1-to regulate centriole number rather than mitosis. The authors use tethered vs. untetheredanimal cap explants to modulate tissue tension, combine pharmacologic perturbations with genetic loss of function and rescue, quantititative image analysis and present a model in which tension gated PIEZO1 activates ERK/YAP, influences Foxj1, and tunes centriole number in MCCs.

The manuscript tackles an important and timely problem with clear disease relevance. It major advance is their presented model that posits that post mitotic MCCs repurpose a canonical mechanotransduction module to regulate organelle number rather than proliferation. It is a conceptually strong study addressing an important problem with a clean mechanical paradigm. However, to support the central claim that centriole number control is a specific, direct consequence of the PIEZO1-Ca²⁺-ERK/YAP pathway within MCCs, the revision should establish specificity and causality and provide experimental data for some of the major conclusions as detailed below. Addressing these points are critical to support the mechanistic conclusions and impact.

Major concerns:

1) The presented data do not yet establish a specific, direct pathway linking mechanotransduction to centriole number, because the molecular players tested (PIEZO1, Ca²⁺, PKC, ERK, YAP, Foxj1) are highly pleiotropic. As such, the observed centriole number phenotypes, and some of the major conclusions, could be indirect. It is therefore critical to test the specificity and causality of the proposed pathway. This could be done with the authors' own strategies and/or with the following potential approaches:

• Genetic dependency and sufficiency tests: It could be shown that Yoda1 has no effect in PIEZO1 loss-of-function MCCs, and that wild-type PIEZO1, but not conductance-dead PIEZO1 pore mutants restores Yoda1 responsiveness across centriole number, pERK, and YAP readouts. For example, PIEZO1 C terminus was shown to govern Ca²⁺ influx and ERK1/2 activation. Comparing full length PIEZO1 with a C terminal deletion in MCC restricted rescue; loss of rescue of centriole amplification and ERK/YAP activation with the C terminal deletion can provide a genetics anchored specificity test beyond broad inhibitors.

• Downstream bypass/rescue experiments: In PIEZO1 loss-of-function or BAPTA conditions, can enforcing MEK/ERK activation or YAP rescue centriole number defect? Conversely, can MEK inhibitors block Yoda1-induced effects.

2) The hypothesis about the centriole pool of Piezo as the mechnosensor for centriole number regulation is very exciting and novel. Can localization controlled variants be used to test whether a centriole associated pool directly senses tension for number control (for example, centrosome targeted PIEZO1 via a PACT tag). Alternatively, broad cellular Ca sensors (GcaMP) or centrosome proximal Ca sensors (e.g., PACT GCaMP) can be used detect local calcium microdomains during tethering or Yoda1 treatment.

3) Because the proposed pathway is tension-sensing and YAP pathway is tightly linked to the actin cytoskeleton, the role of actin cysoskeleton in the proposed pathway should be tested directly. The authors mention different hypothesis around actin but has not tested them in the manuscript. For example, actin-depedent sequestration of Yap at the apical surface is intriguing. Does actin polymerization induced by drugs release Yap from the apical surface?

4) Image quantification and analysis must be described in greater detail in the Methods section, as they are central to the major conclusions of the manuscript. For example, the authors should explain how nuclear, cytoplasmic, and centriole segmentation were performed, and how relative protein levels in the nucleus versus the cytoplasm (e.g., YAP, volume- or area-based) were quantified. Specifically, the thresholds and segmentation criteria applied to different cellular structures under various conditions, as well as the use of Imaris and other software, should be clearly detailed.

5) PIEZO1 mRNA was shown to incrase in a Foxj1 linked feedback loop. Does this increase translate into an increase in total protein levels?

6) Is the proposed signaling cascade active in mammalian multiciliated cells (e.g., airway epithelium). If possible, testing this by using one of the major players of the pathway as a readout such as as ERK phosphorylation, YAP nuclear localization in mammalian MCCs will reveal whether regulation of centriole number through this pathway is conserved and would strengthen the generality.

7) Throughout the results section, there are multiple times where authors raised specific hypothesis about their data (e.g. foxj1 regulation of number control, apical actin/YAP). However, they have not tested them. These hypothesis are very exciting and if possible, testing experimentally, would strengthen the conclusions associated with them.

Minor concerns:

1) Abstract: "how MCCs regulate centriole/cilia numbers remains a major knowledge gap" overstates the field; please soften to reflect recent advances (mechanics/apical area scaling; PIEZO1 implication).

2) MCC vs non MCC identification (Fig. 1): Clarify how non MCCs were distinguished from MCCs (e.g. markers/criteria).

3) GsMTx4 rationale: State that GsMTx4 is a spider venom peptide that inhibits cationic mechanosensitive channels (including PIEZO1) and justify its use alongside Yoda1.

4) Timeline statement: "Centriole amplification to migration and apical docking takes ~4-5 h (personal observation)" is not appropriate; either cite time lapse literature or include your own time lapse data.

5) Redundancy: The description of Yoda1 as a channel specific agonist is repeated; keep only once.

6) "WT yap1 GFP construct previously used by Dr. Lance Davidson ..." should move construct description to Methods and keep only the citation in Results.

7) "(Unpublished data; Dr. Mahjoub)" should be removed unless data are shown.

8) Add the Kintner group reference linking motile cilia number and centriole number in Xenopus MCCs.

9) Replace "as shown previously in our eLife paper" with "as we previously showed or shown previously (Kulkarni et al., 2021)".

10) The two hypotheses for how Foxj1 could regulate number under tension (actin remodeling vs. transcriptional control of amplification genes) belong in the Discussion unless tested. Moreover, the part on the discussion on yap sequestration by apical actin and the two possibilities presented also should go do discussion.

Significance

This manuscirpt dissects Piezo1-mediated mechanotransduction to regulation of centriole number in Xenopus multiciliated cells (MCCs) via Ca²⁺, ERK/YAP, and Foxj1. While Piezo1 and its downstream effectors have been implicated broadly in mechanosensation, cellular tension responses, and transcriptional regulation, their specific role in centriole nubmer control in MCCs has been unknown By integrating pharmacological manipulation, genetic perturbation, and functional readouts, the authors demonstrate that this pathway directly influences centriole number.

The findings extend published knowledge in two main ways:

(1) they connect a mechanosensitive ion channel to the transcriptional program governing Foxj1 expression and multiciliation, a mechanistic link not previously defined, and

(2) they highlight the pleiotropic yet coordinated nature of Piezo1 signaling in organelle biogenesis. This work will be of broad interest to cell and developmental biologists studying ciliogenesis, epithelial differentiation, and mechanotransduction, as well as to biomedical researchers interested in multicilaited cells and ciliopathies. By situating a well-studied mechanosensor within the context of MCC biology, the study opens new directions for understanding how tissue-level forces shape organelle number control and function.

At the same time, the impact of the study is weakened by concerns regarding the causability and specificity of the pathway, since the signaling components examined are highly pleiotropic and it remains challenging to separate direct effects on centriole number from broader cellular consequences. The causal relationships among Piezo1 activity, downstream signaling, and Foxj1 expression require stronger substantiation, and the extent to which this pathway operates in mammalian multiciliated cells remains an open question. Addressing these limitations would strengthen the robustness, generality, and translational relevance of the conclusions.

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Referee #2

Evidence, reproducibility and clarity

Narayanan, Kulkami and colleagues here examine how the Piezo-Erk-Yap pathway is involved in centriole numerical control in multiciliated cells (MCCs). Using reverse genetic and pharmacological methods in Xenopus embryos, they show that Piezo-mediated ERK signalling through to Yap regulates tension-sensitive centriole number, through a mechanism that involves Foxj1, very likely acting as a transcription factor. The data are carefully controlled, robustly analysed and well presented. Statistical analyses are notably thorough.

Main points:

1. It should be clarified whether the immunoblots and the related quantitations in Figs. 2 and S2 are all from separate blots/ exposures. If so, they are not useful as controls, and these blots should be repeated with the relevant samples analysed in parallel. Size markers and labels should be included (2B, 2G; S2B and S2G). An increase in total ERK would alter the interpretation of the increase in nuclear pERK in the IF experiments.

2. Considering the Yap-piezo mechanism of action, the authors' logic for the selection of myb, foxj, plk4 and ccno as transcriptional targets is clear, but the HCR-derived signal and the differences seen in the yap morphants are not very strong, notwithstanding the statistical significance. There appear to be distinct subgroups within the treated populations (in Figure S6B, although these data seem quite different in Fig. 7H, so a comment on the technical differences might be helpful), so that the extent to which Yap1 regulates (Myb-)Foxj1 expression in MCCs is not clearly demonstrated by this experiment. Related to this point, it is unclear why 20-25% of the yap1/ piezo1 MO -treated embryos do not show a decline in FOXj1 in Fig. 6, given the qualitative nature of the scoring. Assuming the KD penetrance would vary on a cell-to-cell basis, rather than an embryo-to-embryo basis, this may suggest that there are additional relevant targets (some of which are discussed by the authors). Single-cell analysis might be a way to address this; however, this is not a trivial experiment, it might be sufficient to include a caveat in the text. Furthermore, the conclusion that Foxj1 regulates centriole amplification in a tension-dependent manner is well-supported by the data.

3. Controls for the knockdowns by the various MOs should be provided.

Minor points:

1. Autocorrection of ERK1/2 or MEK1/2 pathways to 1/2 should be avoided.

2. Reference list should be checked for completeness; some citations lack journal/ volume/ page/ year details.

3. An 'overexposed' version of the image selected for centrioles in Figure 5F might be included with the Chibby-BFP at the same level as in the other figures. At present, the Yap KD cell in the image appears to have the normal centrioles; this is potentially confusing, even though the authors clearly explain matters in the text.

4. It might be clearer to present injected/ uninjected in the same orientation in Fig. 6A and B.

5. Figure 7B lacks the schematic described in the figure legend.

Significance

This study presents novel insight into the developmentally important process of ciliogenesis in multiciliated cells that will be of specific interest to the fields of cilium biology and mechanobiology, with additional general interest in calcium signalling and cell biology.

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Referee #1

Evidence, reproducibility and clarity

The manuscript from Narayanan addresses the fascinating question of how Multiciliated cells regulate centriole number to scale with cell size. They have generated a tremendous amount of high quality data that supports a model in which mechanosensitive signaling via piezo1 leads to an increase in intracellular Ca++ that leads to an activation of the Erk pathway which in turn activates the Yap pathway that in turn regulates FoxJ1 levels which they propose regulates centriole number. This is complicated but they have strong quantifiable data that supports most of the claims. I think this is a beautiful study that adds significantly to the field. There is a lot of evidence that disrupting these pathways has a negative consequence on centriole number. What is lacking is a positive connection showing a role of these processes in fine tuning the centriole number as the title suggests. Several key experiments would significantly strengthen their claims.

• The data is presented in a way that proposes that the ultimate role of these pathways is to regulate Foxj1 levels to fine tune centriole number based on the level of tension. There are two experiments that would significantly strengthen these claims. First if their model is correct then even short term treatment with Yoda1 should induce the pathway and effect centriole numbers. While I appreciate the challenge of long term Yoda1 treatment its not clear to me why it would be needed if short term treatment is setting off the transcriptional cascade. Yoda is used throughout the paper to induce all the pathways but we don't know if it actually induces the phenotype. I think this should be addressed with either short term treatments or a dose response to find a dose that does not lead to skin pealing. It is hard to ignore this obvious deficiency. Second, the model predicts that all of this is to regulate Foxj1 levels to regulate the subtle balance between cell size and centriole number. If this is correct, then the overexpression of Foxj1 should have a profound effect on centriole number in multiciliated cells. This is such an easy experiment that would validate many of the claims.

Minor issues:

• The authors attempt to measure an effect of plk4 and ccno in the Yap MO experiment. However, the fact that they could not be scored means the experiment wasn't really performed. I think it is more appropriate to leave out rather than risk giving the impression that these genes were unaffected.

• The authors indicate that the foxj1 result suggests two alternatives, one that foxj1 regulates actin (pan 2007) and the other that it is a transcription factor. I think the evidence for foxj1 being a transcription factor is extremely well established and while it is possible for it to have an additional unrelated role my interpretation of the Pan paper is that the failed apical docking leads to disrupted actin which is also well established. I don't think there is a lot of evidence for foxj1 being anything other than a TF.

Significance

• This is a really beautiful paper that will be well appreciated by the cilia community but also should be appreciated by the broader cell biology community.

• The strengths of this paper are a high level of rigor in which they perform detailed quantification of a wide range of processes. For many experiments they have multiple methods for disrupting function which again adds to the rigor. They have successfully linked Piezo1, Erk, Yap and FoxJ1 function to proper centriole biogenesis, which is a significant advance.

• The limitation is that all their perturbations negatively effect centriole number which could be indirect. If their model is correct then they should be able to activate the pathway in one way or another to stimulate centriole number. This is a significant limitation to their overall model.

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Reply to the reviewers

Reviewer #1

Summary: The authors have previously published Mass-spectrometry data that demonstrates a physical interaction between Sall4 and the BAF chromatin complex in iPSC derived neurectodermal cells that are a precursor cell state to neural crest cells. The authors sought to understand the basis of this interaction and investigate the role of Sall4 and the BAF chromatin remodelling complex during neural crest cell specification. The authors first validate this interaction with a co-IP between ARID1B subunit and Sall4 confirming the mass spec data. The authors then utilise in silico modelling to identify the specific interaction between the BAF complex and Sall4, suggesting that this contact is mediated through the BAF complex member DPF2. To functionally validate the role of Sall4 during neural crest specification, the authors utilsie CRISPR-Cas9 to introduce a premature stop codon on one allele of Sall4 to generate iPSCs that are haploinsufficient for Sall4. Due to the reports of Sall4's role in pluripotency, the authors confirm that this model doesn't disrupt pluripotent stem cells and is viable to model the role of Sall4 during neural crest induction. The authors expand this assessment of Sall4 function further during their differentiation model to cranial neural crest cells, assessing Sall4 binding with Cut+Run sequencing, revealing that Sall4 binds to motifs that correspond to key genes in neural crest differentiation. Moreover, reduction in Sall4 expression also reduces the binding of the BAF complex, through Cut and Run for BRG1. Overall, the authors then propose a model by which Sall4 and BRG1 bind to and open enhancer regions in neurectodermal cells that enable complete differentiation to cranial neural crest cells.

Overall, the data is clear and reproducible and offers a unique insight into the role of chromatin remodellers during cell fate specification.

We thank the Reviewer for the nice words of appreciation of our manuscript.

However, I have some minor comments.

1- Using AlphaFold in silico modelling, he authors propose the interaction between the BAF complex with Sall4 is mediated by DPF2, but don't test it. Does a knockout, or knockdown of DPF2 prevent the interaction?

We agree with the Reviewer that we are not functionally validating our computational prediction that DPF2 is the specific BAF subunit directly linking SALL4 with BAF. We chose not to perform the validation experiment for two main reasons:

1) This would be outside of the scope of the paper. In fact, from a mechanistic point of view, we have confirmed via both Mass-spectrometry and co-IP with ARID1B that SALL4 and BAF interact in our system. Moreover, mechanistically we also extensively demonstrate that the interaction with SALL4 is required to recruit BAF at the neural crest induction enhancers and we further demonstrate that depletion of SALL4 impairs this. In our view, this was the focus of the manuscript. On the other hand, detecting with certainty which BAF subunit mediates the interaction with SALL4 would be outside the scope of the paper.

2) Moreover, after careful consideration, we don’t think that even a knock-out of DPF2 would provide a definite answer to which exact BAF subunit mediates the interaction with SALL4. In fact, knock out of DPF2 could potentially disrupt BAF assembly or stability, and this could result in a disruption of the interaction with SALL4 even if DPF2 is not the very subunit mediating it (in other words the experiment could provide a false positive result). In our opinion, the only effective experiment would be mutating the DPF2 residues that we computationally predicted as responsible for the interaction with SALL4, but again this would be very laborious and out of the scope.

That being said, we agree with the Reviewer that while the SALL4-BAF interaction was experimentally validated with robust approaches, the role of DPF2 in the interaction was only computationally predicted, which comes as a limitation of the study. We have now added a dedicated paragraph in the discussion to acknowledge such limitation.

2- OPTIONAL: Does knockout of DPF2 phenocopy the Sall4 ko? This would be very interesting to include in the manuscript, but it would perhaps be a larger body of work.

See point-1.

3- Figure 1, the day of IP is not clearly described until later in the test. please outline during in the figure.

We thank the Reviewer for pointing this out. This has been fixed.

3- What is the expression of Sall1 (and other Sall paralogs) during differentiation. The same with the protein levels of Sall4, does this remain at the below 50%, or is this just during pluripotency?

As Recommend by the Reviewer, we have performed time-course WB of SALL1 and SALL4. These experiments revealed that SALL1 remains very lowly expressed in wild-type conditions across time points and all the way through differentiation until CNCC (See updated supplementary Fig. S9). This is consistent with previous studies that demonstrated that SALL4, but not SALL1, is required for early mammalian development (see for example Miller et al. 2016, Development, and Koulle et al. 2025, Biorxiv). We performed the same time-course WB for SALL4 which revealed that SALL4 expression progressively decreases after day-5 (as expected) and it’s very low at CNCC stage (day-14), therefore we would expect the KO to remain at even lower level at this stage.

4- The authors hypothesise that Sall4 binds to enhancers- with the criteria for an enhancer being that these peaks > 1KB from the TSS are enhancers. Can this be reinforced by overlaying with other ChIP tracks that would give more confidence in this? There are several datasets from Joanna Wysocka's lab that also utilise this protocol which can give you more evidence to reinforce the claim and provide further detail as to the role of Sall4.

We thank the Reviewer for this great suggestion. As recommended, we have used publicly available ChIP-seq data generated by the Wysocka lab (H3K4me1, H3K4m3) and also generated new H3K27ac CHIP-seq data as well. These experiments and analyses confirmed that these regions are putative CNCC enhancers (and a minority of them putative promoters), decorated with H3K4me1 and with progressive increase in H3K27ac after CNCC induction (day-5). See new Supplementary Figure S6.

5- The authors state that cells fail to become cranial neural crest cells, however they do not propose what the cells do instead. do they become neural? Or they stay at pluriopotent, which is one option given the higher expression of Nanog, OCT4 and OTX2 that are all expressed in pluripotent stem cells.

We think that it is likely a mix of both. There is a mixed bag of expression of pluripotency markers, but also high expression of neuroectodermal markers. This suggests that most cells safely reach the neuroectodermal stage but fail to go beyond that, while some of the cells simply do not differentiate or regress back to pluripotency. We would rather refrain on overinterpreting what the KO-cells become, as it is likely an aberrant cell type, but following the Reviewer’s indication we have added a paragraph in the discussion to speculate on this.

6- In general, I would like to see the gating strategy and controls for the flow cytometry in a supplemental figure.

As Recommended by the Reviewer, we have added the gating strategy in the Supplementary Fig. S4.

7- For supplementary figure 1- please include the gene names in the main image panels rather than just the germ layer.

Done. The figure is now Supplementary Figure S3 since two supplementary figures were added before.

Reviewer #2

Summary In this manuscript, the authors build on their previous work (Pagliaroli et al., 2021) where they identified an interaction between the transcription factor SALL4 and the BAF chromatin remodeling complex at Day-5 of an iPSC to CNCC differentiation protocol. In their current work, the authors begin by exploring this interaction further, leveraging AlphaFold to predict interaction surfaces between SALL4 and BAF complex members, considering both SALL4 splice isoforms: a longer SALL4A (associated with developmental processes) and a shorter SALL4B (associated with pluripotency). They propose that SALL4A may interact with DPF2, a BAF complex member, in an isoform-dependent manner. The authors next explore the role of SALL4 in craniofacial development, motivated by patient heterozygous loss of function mutations, leveraging iPSC cells with an engineered SALL4 frameshift mutation (SALL4-het-KO). Using this model, the authors first demonstrate that a reduced expression of SALL4 does not impact the iPSC identity, perhaps due to compensation via upregulation of SALL1. Upon differentiation to neuroectoderm, SALL4 haploinsufficiency causes a reduction in newly accessible sites which are associated with a reduction in SALL4 binding and therefore a loss of BAF complex recruitment. Interestingly, however, there were few transcriptional changes at this stage. Later in the CNCC differentiation at Day-14 when the wildtype cells have switched expression of CNCC markers, the SALL4-het-KO cells fail to switch cadherin expression associated with a transition from epithelial to mesenchymal state, and fail to induce CNCC specification and post-migratory markers. Together the authors propose that SALL4 recruits BAF to CNCC enhancers as early as the neuroectodermal stage, and failure of BAF recruitment in SALL4-het-KO lines results in a loss of open chromatin at regulatory regions required later for induction of the CNCC programme. The failure of the later differentiation is compelling in the light of the early stages of the differentiation progressing normally, and the authors outline an interesting proposed mechanism whereby SALL4 recruits BAF to remodel chromatin ahead of CNCC enhancer activation, a model that can be tested further in future work. The link between SALL4 DNA binding and BAF recruitment is nicely argued, and very interesting as altered chromatin accessibility at Day 5 in the neuroectodermal stage is associated with only few changes in gene expression, while gene expression is greatly impacted later in the CNCC stage at Day 14. The in silico predictions of SALL4-BAF interaction interfaces are perhaps less convincing, requiring experimental follow-up outside the scope of this paper. Some of the associated figures could perhaps be moved to the supplement to enhance the focus on the later functional genomics experiments.

We thank the Reviewer for the nice words of appreciation of our manuscript.

Major comments

1. A lot of emphasis is placed on the AlphaFold predictions in Figure 1, however the predictions in Figure 1B appear to be mostly low or very low confidence scores (coloured yellow and orange). It is unclear how much weight can be placed on these predictions without functional follow-up, e.g. mutating certain residues and showing impact on the interaction by co-IP. The latter parts of the manuscript are much better supported experimentally, and therefore perhaps some of the Figure 1 could move to a Supplemental Figure (e.g. the right-hand part of 1B, and the lower part of Figure 1C showing SALL4B predicted interactions). The limitations of AlphaFold predictions should be acknowledged and the authors should discuss how these predicted interactions could be experimentally explored further in the future.

As recommended by the Reviewer, we have moved part of the AlphaFold predictions to Supplementary Figure S1, and we added a paragraph in the discussion to acknowledge the limitations of AlphaFold.

The authors only show data for one heterozygous knockout clone for SALL4. It is usual to have more than one clone to mitigate potential clonal effects. The authors should comment why they only have one clone and include any data for a second clone for key experiments if they already have this. Alternatively, the authors could provide any quality control information generated during production of this line, for example if any additional genotyping was performed.

We apologize for the confusion and for our lack of clarify on this. We have used two clones (one generated with a 11 bp deletion, one with a 19 bp deletion, both in exon-1, see also the point 6 of your minor points). The two clones were used as biological replicates, so for example the two ATAC-seq replicates performed in each time point were performed with the two different clones, and the three RNA-seq replicates were performed with two technical replicates of the clone with the 11bp deletion and one replicate with the clone with 19 bp deletion. We have clarified this in the methods section of the manuscript and added a Supplementary Figure (S2) showing the editing strategy for the two clones. Thank you for catching it.

The authors show all genomics data (ATAC-seq, CUT&RUN and ChIP-seq) as heatmaps and average profiles. It would be valuable to see some representative loci for the ATAC seq (perhaps along with SALL4 and BRG1 recruitment) at some representative and interesting loci.

As recommended by the Reviewer, we have added Genome Browser screenshots of representative loci in Fig. 6.

Figure 4A. The schematic could be improved by including brightfield or immunofluorescent images at the three stages of the differentiation. Are the iPS cells seeded as single cells, or passaged as colonies before starting the differentiation. Further details are required in the methods to clarify how the differentiation is performed, for example at what Day are the differentiating cells passaged, this is not shown on the schematic in Figure 4A.

As recommended, we added IF images in the Fig. 4A schematic, and added more details in the methods.

There is likely some heterogeneity of cell types in the differentiation at Day 5 and Day 14. Can the authors comment on this from previous publications or perhaps conduct some IF for markers to demonstrate what proportions of cells are neuroectoderm at Day 5 and CNCCs at Day 14.

The differentiation starts with single cells that aggregate to form neuroectodermal clusters, as per original protocol. The CNCCs that we obtain with this protocol homogeneously express CNCC markers, as shown by IF of SOX9 in Fig. 4A. For the day-5, as recommended we have added IF for PAX6 also showing homogeneous expression (Fig. 4A).

For the motif analysis for Day 5-specific SALL4 binding sites (Figure 4E), was de novo motif calling performed? Were any binding sites reminiscent of a SALL4 binding site observed (e.g. an AT-rich motif)? Could the authors comment on this in the text - if there is no SALL4 binding motif, does this suggest SALL4 is recruited indirectly to these sites via interaction with another transcription factor for example?

Similar to SALL4, SALL1 also recognizes AT-rich motifs. However, while we found AT-rich motifs as enriched in our day-5 motif analysis (in the regions that gain SALL4 binding upon differentiation), the enrichment is not particularly strong, and several other motifs are significantly more enriched, suggesting that, like the Reviewer mentioned, SALL4 might be recruited indirectly at these sites by other factors. We have added a paragraph on this in the discussion.

Does SALL1 remain upregulated at Day-5 and Day-14 of the differentiation for the SALL4-het-KO line? Are binding sites known for this TF and were they detected in the motif analysis performed? Further discussion of the impact of the overexpression of SALL1 on the phenotypes observed is warranted - e.g. for Figure 5F, could the sites associated with a gain of BRG1 peaks upon loss of SALL4 be associated with SALL1 being upregulated and 'hijacking' BAF recruitment to distinct sites associated with nervous system development? Is SALL1 still upregulated at Day 5?

As mentioned above, SALL1 also recognizes AT-rich motifs but similar to SALL4 also binds unspecifically, likely in cooperation with other TFs. Like the Reviewer suggested, it is certainly possible that some of the sites associated with a gain of BRG1 peaks upon loss of SALL4 could be associated with SALL1 being upregulated and 'hijacking' BAF recruitment to distinct sites. While this is speculative, we have added a paragraph on this in the discussion.

Related to the point above, SALL4A is proposed to have an isoform-specific interaction with the BAF complex. It would be valuable to plot SALL4A and SALL4B expression from the available RNA-seq data at Day 0, 5 and 14 to explore whether stage-specific isoform expression matches with the proposed role of SALL4A to interact with BAF at Day 5. It could be valuable to also look at expression of SALL1, 2 and 3 across the time course to see whether additional compensation mechanisms are at play during the differentiation.

Thanks for suggesting this. We performed a time course analysis of isoform specific gene expression, which showed that SALL4B expression remains low throughout differentiation, while SALLA4A expression increases upon differentiation cues and it remains at high levels until the end. We have added this to supplementary Fig. S9. Moreover, we have performed an additional experiment, using pomalidomide, which is a thalidomide derivative that selectively degrades SALL4A but not SALL4B. Notably, SALL4A degradation recapitulated the main findings obtained with the CRISPR-KO of SALL4, further supporting that SALL4A is the isoform involved in CNCC induction (see new Fig. 8).

At line 264, The authors state "SALL4 recruits the BAF complex at CNCC developmental enhancers to increase chromatin accessibility". Given that this analysis is performed at Day 5 of the differentiation, which is labelled as neuroectoderm what evidence do the authors have that these are specifically CNCC enhancers? Statements relating to enhancers should generally be re-phrased to putative enhancers (as no functional evidence is provided for enhancer activity), and further evidence could be provided to support that these are CNCC-specific regulatory elements, e.g. showing representative gene loci from CNCC-specific genes. Discussion of the RNA-seq presented in Supplementary Figure 2B may also be appropriate to introduce here given that large numbers of accessible chromatin sites are detected while the expression of very few genes is impacted, suggesting these sites may become active enhancers at a later developmental stage.

As also recommended by the other Reviewer, to further characterize these sites, we have used publicly available histone modification CHIP-seq data (H3K4me1, H3K4me3) generated by the Wysocka lab (H3K4me1, H3K4m3) and also generated new H3K27ac CHIP-seq data as well. These experiments and analyses confirmed that these regions are putative CNCC enhancers (and a minority of them putative promoters), all decorated with H3K4me1, and all showing progressive increase in H3K27ac after CNCC induction (day-5). See new Supplementary Figure S6.

1. Do any of the putative CNCC enhancers detected at Day 5 as being sensitive to SALL4 downregulation and loss of BAF recruitment overlap with previously tested VISTA enhancers (https://enhancer.lbl.gov/vista/)?

Yes, we have found examples of overlap and have included two of them in the updated Figure 6 as Genome Browser screenshots.

Minor comments

1. The authors are missing references in the introduction "a subpopulation of neural crest cells that migrate dorsolaterally to give rise to the cartilage and bones of the face and anterior skull, as well as cranial neurons and glia".

Fixed, thank you.

The discussion of congenital malformations associated with SALL4 haploinsufficiency is brief in the introduction. From OMIM, SALL4 heterozygous mutations are implicated with the condition Duane-radial ray syndrome (DRRS) with "upper limb anomalies, ocular anomalies, and, in some cases, renal anomalies... The ocular anomalies usually include Duane anomaly". That Duane anomaly is one phenotype among a number for patients with SALL4 haploinsufficiency could be clarified in the introduction. Of note, this is stated more clearly in the discussion but needs re-wording in the introduction.

Done, thank you.

The statements "show that the SALL4A isoform directly interacts with the BAF complex subunit DPF2 through its zinc-finger-3 domain" and "this interaction occurs between the zinc-finger-cluster-3 (ZFC3) domain of SALL4A and the plant homeodomains (PHDs) of DPF2" in the introduction appear overstated and should be toned down. To show this the authors would need to mutate or delete the proposed important zinc-finger domains from SALL4A, which is outside the scope of this work. Notably, this is less strongly-stated elsewhere in the manuscript, e.g "predict that this interaction is mediated by the BAF subunit DPF2", Line 162.

Done, thank you.

Could the authors clarify why 3 Alphafold output models are shown for SALL4B in Figure 1C, and only one output model for SALL4A?

AlphaFold3 produces five separate predicted models per protein combination (e.g., Model_1 … Model_4), each derived from slightly different network parameters or initializations. The final output prioritizes the model with the highest confidence score. This multi-model strategy enables the identification of the most robust conformation while providing a measure of structural uncertainty (as per GitHub documentation for AlphaFold3). wE have conducted the same analysis for SALL4A as we did for SALL4B. Specifically, SALL4A interacts with the AT-rich DNA in models 0, 1, and 2, therefore models 3 and 4 were excluded. When analysing models 1 and 2, we found a higher number of residues involved in the interaction (>800 instead of 396). Similarly to model 0, only the interactions between residues belonging to an annotated functional domain (ZFs and PHDs) were considered.

In Model 1: SALL4A and DPF2 interact mainly through ZF6 and 7, and not 5 as Model 0.

In Model 2: SALL4A and DPF2 interact mainly through ZF5 and 6, and not 7 as Models 0. In contrast, this model shows an interaction with ZF1 not shown in the other two models, but with a higher PAE (31 average compared to 25 to 27 average of the other two ZFs.

Therefore, we considered Model 0 as it is the model with higher confidence and representative of all significant models (includes ZF5, 6, and 7).

Line 121. The authors state "DPF2, a broadly expressed BAF subunit,", but don't show expression during their CNCC differentiation. It would be good to include expression of DPF2 in Figure 1E.

Done, thank you.

The text states "a 11 bp deletion within the 3'-terminus of exon 1 of SALL4", while the figure legend states, "Sanger sequencing confirming the 19 bp deletion in one allele of SALL4 is displayed". The authors should clarify this disparity and experimentally confirm the deletion, e.g. by TA-cloning the two alleles and sequencing these separately to show that one allele is wildtype and the other has a frameshift deletion.

We apologize for the confusion. As stated above (point-2 of the major comments), we have used two clones (one generated with a 11 bp deletion, one with a 19 bp deletion, both in exon-1, see also the point 6 of your minor points). The two clones were used as biological replicates (see response above for details). The deletion for both clones was experimentally confirmed by Sanger sequencing by the company that generated the lines for us (Synthego). The strategy for the two clones is now shown also in Supplementary Fig. S2.

The authors generate an 11-bp (or 19-bp?) deletion in exon-1 - it would be valuable to include a discussion whether patients have been identified with deletions and frame-shift mutations in this region of SALL4 exon-1. And also clarify, if not clearly stated in the text, that both SALL4A and SALL4B will be impacted by this mutation. Are there examples of patient mutations which only impact SALL4A?

As requested, we have added a discussion paragraph to discuss this. And, yes, both SALL4A and SALL4B are impacted by both deletions in both clones (11 bp and 19 bp deletion).

Regarding patient variants on exon-1 and patient variants that only impact SALL4A. We could only find one published pathogenic 170bp deletion in exon 1 (VCV000642045.7). The majority of the pathogenic or likely pathogenic variances are located on exon2. In particular, of the 63 reported pathogenic (or likely pathogenic) clinical variants, 42 were located on exon 2. Among these, 28 are located in the portion shared by both SALL4A and SALL4B, while the remaining 14 were SALL4A specific.

For the SALL4 blots in Figure 2B, is the antibody expected to detect both isoforms (SALL4A and SALL4B), and which isoform is shown? If two isoforms are detected, they should both be presented in the figure.

Yes, the antibody detects both isoforms, and we now present both in the figure 2, as recommended.

SALL4 expression should be shown for Figure 2C to see whether the >50% down-regulation of SALL4 at the protein level may be partially driven by transcriptional changes.

Done, thank you. As expected, we observed the SALL4 mRNA expression in the KO line is comparable to wild-type conditions, but still this results in a significant decrease of the SALL4 protein level likely because of autoregulatory mechanisms coupled with non-sense mediated decay of the mutated allele. Also, we note that SALL4 usually makes homodimers, therefore lack of sufficient amount of protein could also lead to degradation of the monomers.

The number of experimental replicates should be indicated in all figure legends where relevant. Raw data points should be plotted visibly over the violin plots (e.g. Figure 2C).

Done, thank you.

For Figure 3A, the images of the DAPI and NANOG/OCT4 staining should be shown separately in addition to the overlay.

Done, thank you.

The metric 'Corrected Total Cell Fluorescence (CTCF)' should be described in the methods. The number of images used for the quantification in Figure 3A should be

Done, thank you.

Figure 3C - what are the 114 differentially expressed genes? Some interesting genes could be labelled on the plot and the data used to generate this plot should be included as a Supplementary Table. Supplementary Tables should similarly be provided for Figure 6C, Day 14 and Supplementary Figure 2B, Day 5.

As recommended, we have highlighted some interesting genes in the volcano plot and also included all the expression data for all genes in Supplementary Table S3.

Figure 4B. The shared peaks are not shown. For completeness, it would be ideal to show these sites also.

Done, thank you.

Figure 4C is difficult to interpret. Why is the plot asymmetric to the left versus right? What does the axis represent - % of binding sites?

The asymmetry is due to the fact that there is a larger number of peaks that are downstream of the TSS than peaks that are upstream of TSS. This is consistent with the fact that many SALL4 peaks are in introns, likely representing intronic enhancers.

Line 224-225. What do n= 3,729 and n= 6,860 refer to? There appear to be many more binding sites indicated in Figure 4B, therefore these numbers cannot represent 86% and 97% of sites?

Thank you for pointing this out, we should have specified in the text. Those numbers refer to the genes whose TSS is closest to each SALL4 peak. Notably, multiple peaks can share the same closest TSS, hence the discrepancy between # of peaks and # of nearest genes.

Raw numbers:

• Day-0 RAW = 6,104 (peaks = 6,114);
• Day-5 RAW = 17,131 (peaks = 17,137). Now raw data reported in Supplementary Table 4.

Figure 4E. Several TFs mentioned in the text (Line 243) are not shown in the figure, it would be good to show all TFs motifs mentioned in the text in this figure. Again, there is no mention of whether a sequence-specific motif is detected for SALL4 (e.g. an AT-rich sequence) from this motif analysis.

Done, thank you. An AT-rich sequence, resembling the SALL4 motif, was detected in a small minority of sites (this is now shown in Supplementary Figure S5), suggesting that SALL4 engages chromatin in a broad manner, going beyond its preferred motif, possibly in cooperation with other TFs. This is consistent with many studies that in mESCs have shown that SALL4 binds at OCT4/NANOG/SOX2 target motifs. This is now discussed in a dedicated paragraph in the discussion.

Figure 4G. How was the ATAC-seq data normalized for the WT and SALL4-het-KO lines for this comparison? The background levels of accessibility seem quite different in Replicate 1.

The bigwigs used to make the heatmaps are normalized by sequencing depth using the Deeptools Suite (normalization by RPKM).

Figures 5B-C could be exchanged to flow better with the text. A Venn diagram could be included to show the overlap between the sites losing BRG1 in SALL4-het-KO (13,505 sites) and the Day5-specific SALL4 sites (17,137 sites).

Done, thank you.

At Day 5, the authors suggest a shift towards neural differentiation. It could be interesting for the authors to perform qRT-PCR at Day 5 for some neural markers or look in the Day 14 data for markers of neural differentiation at the expense of CNCC markers.

See updated Supplementary Fig. S8, where we show timecourse expression of several genes, including neural markers.

Is the data used to plot Figure 5D the same as Figure 4G. If so, why is only one replicate shown in Figure 5D?

Only one replicate was shown in the main figure purely for lack of space, but the experiment was replicated twice (with the two different clones), and the results were exactly the same. See plots below for your convenience:

Figure 6A. How many replicates are shown? If n=2, boxplots are not an appropriate to represent the distribution of the data. Please include n= X in the figure legend and plot the raw data points also.

Done, thank you, and as suggested we are no longer using boxplots for this panel.

Figure 6B. What is the significance of CD99 for CNCC differentiation?

Figure 6F. No error bars are shown, how many replicates were performed for this time couse? The linear regression line does not appear to add much value and could be removed.

As suggested, we have removed these plots and replaced them with individual genes plots, which include error bars. See updated Supplementary Figure S8.

At line 304, the authors state "while SALL4-het-KO showed a significant downregulation of these genes". Perhaps 'failed to induce these genes' may be more accurate unless they were expressed at Day 5 and downregulated at Day 14.

Done, thank you.

Lines 332-335. The genes selected for pluripotency, neural plate border, CNCC specification could be plotted separately in the Supplement to show individual gene expression dynamics.

Done, thank you, see point 24.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors build on their previous work (Pagliaroli et al., 2021) where they identified an interaction between the transcription factor SALL4 and the BAF chromatin remodeling complex at Day-5 of an iPSC to CNCC differentiation protocol. In their current work, the authors begin by exploring this interaction further, leveraging AlphaFold to predict interaction surfaces between SALL4 and BAF complex members, considering both SALL4 splice isoforms: a longer SALL4A (associated with developmental processes) and a shorter SALL4B (associated with pluripotency). They propose that SALL4A may interact with DPF2, a BAF complex member, in an isoform-dependent manner. The authors next explore the role of SALL4 in craniofacial development, motivated by patient heterozygous loss of function mutations, leveraging iPSC cells with an engineered SALL4 frameshift mutation (SALL4-het-KO). Using this model, the authors first demonstrate that a reduced expression of SALL4 does not impact the iPSC identity, perhaps due to compensation via upregulation of SALL1. Upon differentiation to neuroectoderm, SALL4 haploinsufficiency causes a reduction in newly accessible sites which are associated with a reduction in SALL4 binding and therefore a loss of BAF complex recruitment. Interestingly, however, there were few transcriptional changes at this stage. Later in the CNCC differentiation at Day-14 when the wildtype cells have switched expression of CNCC markers, the SALL4-het-KO cells fail to switch cadherin expression associated with a transition from epithelial to mesenchymal state, and fail to induce CNCC specification and post-migratory markers. Together the authors propose that SALL4 recruits BAF to CNCC enhancers as early as the neuroectodermal stage, and failure of BAF recruitment in SALL4-het-KO lines results in a loss of open chromatin at regulatory regions required later for induction of the CNCC programme. The failure of the later differentiation is compelling in the light of the early stages of the differentiation progressing normally, and the authors outline an interesting proposed mechanism whereby SALL4 recruits BAF to remodel chromatin ahead of CNCC enhancer activation, a model that can be tested further in future work.

Major comments

The link between SALL4 DNA binding and BAF recruitment is nicely argued, and very interesting as altered chromatin accessibility at Day 5 in the neuroectodermal stage is associated with only few changes in gene expression, while gene expression is greatly impacted later in the CNCC stage at Day 14. The in silico predictions of SALL4-BAF interaction interfaces are perhaps less convincing, requiring experimental follow-up outside the scope of this paper. Some of the associated figures could perhaps be moved to the supplement to enhance the focus on the later functional genomics experiments.

1. A lot of emphasis is placed on the AlphaFold predictions in Figure 1, however the predictions in Figure 1B appear to be mostly low or very low confidence scores (coloured yellow and orange). It is unclear how much weight can be placed on these predictions without functional follow-up, e.g. mutating certain residues and showing impact on the interaction by co-IP. The latter parts of the manuscript are much better supported experimentally, and therefore perhaps some of the Figure 1 could move to a Supplemental Figure (e.g. the right-hand part of 1B, and the lower part of Figure 1C showing SALL4B predicted interactions). The limitations of AlphaFold predictions should be acknowledged and the authors should discuss how these predicted interactions could be experimentally explored further in the future.
2. The authors only show data for one heterozygous knockout clone for SALL4. It is usual to have more than one clone to mitigate potential clonal effects. The authors should comment why they only have one clone and include any data for a second clone for key experiments if they already have this. Alternatively, the authors could provide any quality control information generated during production of this line, for example if any additional genotyping was performed.
3. The authors show all genomics data (ATAC-seq, CUT&RUN and ChIP-seq) as heatmaps and average profiles. It would be valuable to see some representative loci for the ATAC seq (perhaps along with SALL4 and BRG1 recruitment) at some representative and interesting loci.
4. Figure 4A. The schematic could be improved by including brightfield or immunofluorescent images at the three stages of the differentiation. Are the iPS cells seeded as single cells, or passaged as colonies before starting the differentiation. Further details are required in the methods to clarify how the differentiation is performed, for example at what Day are the differentiating cells passaged, this is not shown on the schematic in Figure 4A.
5. There is likely some heterogeneity of cell types in the differentiation at Day 5 and Day 14. Can the authors comment on this from previous publications or perhaps conduct some IF for markers to demonstrate what proportions of cells are neuroectoderm at Day 5 and CNCCs at Day 14.
6. For the motif analysis for Day 5-specific SALL4 binding sites (Figure 4E), was de novo motif calling performed? Were any binding sites reminiscent of a SALL4 binding site observed (e.g. an AT-rich motif)? Could the authors comment on this in the text - if there is no SALL4 binding motif, does this suggest SALL4 is recruited indirectly to these sites via interaction with another transcription factor for example?
7. Does SALL1 remain upregulated at Day-5 and Day-14 of the differentiation for the SALL4-het-KO line? Are binding sites known for this TF and were they detected in the motif analysis performed? Further discussion of the impact of the overexpression of SALL1 on the phenotypes observed is warranted - e.g. for Figure 5F, could the sites associated with a gain of BRG1 peaks upon loss of SALL4 be associated with SALL1 being upregulated and 'hijacking' BAF recruitment to distinct sites associated with nervous system development? Is SALL1 still upregulated at Day 5?
8. Related to the point above, SALL4A is proposed to have an isoform-specific interaction with the BAF complex. It would be valuable to plot SALL4A and SALL4B expression from the available RNA-seq data at Day 0, 5 and 14 to explore whether stage-specific isoform expression matches with the proposed role of SALL4A to interact with BAF at Day 5. It could be valuable to also look at expression of SALL1, 2 and 3 across the time course to see whether additional compensation mechanisms are at play during the differentiation.
9. At line 264, The authors state "SALL4 recruits the BAF complex at CNCC developmental enhancers to increase chromatin accessibility". Given that this analysis is performed at Day 5 of the differentiation, which is labelled as neuroectoderm what evidence do the authors have that these are specifically CNCC enhancers? Statements relating to enhancers should generally be re-phrased to putative enhancers (as no functional evidence is provided for enhancer activity), and further evidence could be provided to support that these are CNCC-specific regulatory elements, e.g. showing representative gene loci from CNCC-specific genes. Discussion of the RNA-seq presented in Supplementary Figure 2B may also be appropriate to introduce here given that large numbers of accessible chromatin sites are detected while the expression of very few genes is impacted, suggesting these sites may become active enhancers at a later developmental stage.
10. Do any of the putative CNCC enhancers detected at Day 5 as being sensitive to SALL4 downregulation and loss of BAF recruitment overlap with previously tested VISTA enhancers (https://enhancer.lbl.gov/vista/)?

Minor comments

1. The authors are missing references in the introduction "a subpopulation of neural crest cells that migrate dorsolaterally to give rise to the cartilage and bones of the face and anterior skull, as well as cranial neurons and glia".
2. The discussion of congenital malformations associated with SALL4 haploinsufficiency is brief in the introduction. From OMIM, SALL4 heterozygous mutations are implicated with the condition Duane-radial ray syndrome (DRRS) with "upper limb anomalies, ocular anomalies, and, in some cases, renal anomalies... The ocular anomalies usually include Duane anomaly". That Duane anomaly is one phenotype among a number for patients with SALL4 haploinsufficiency could be clarified in the introduction. Of note, this is stated more clearly in the discussion but needs re-wording in the introduction.
3. The statements "show that the SALL4A isoform directly interacts with the BAF complex subunit DPF2 through its zinc-finger-3 domain" and "this interaction occurs between the zinc-finger-cluster-3 (ZFC3) domain of SALL4A and the plant homeodomains (PHDs) of DPF2" in the introduction appear overstated and should be toned down. To show this the authors would need to mutate or delete the proposed important zinc-finger domains from SALL4A, which is outside the scope of this work. Notably, this is less strongly-stated elsewhere in the manuscript, e.g "predict that this interaction is mediated by the BAF subunit DPF2", Line 162.
4. Could the authors clarify why 3 Alphafold output models are shown for SALL4B in Figure 1C, and only one output model for SALL4A?
5. Line 121. The authors state "DPF2, a broadly expressed BAF subunit,", but don't show expression during their CNCC differentiation. It would be good to include expression of DPF2 in Figure 1E.
6. The text states "a 11 bp deletion within the 3'-terminus of exon 1 of SALL4", while the figure legend states, "Sanger sequencing confirming the 19 bp deletion in one allele of SALL4 is displayed". The authors should clarify this disparity and experimentally confirm the deletion, e.g. by TA-cloning the two alleles and sequencing these separately to show that one allele is wildtype and the other has a frameshift deletion.
7. The authors generate an 11-bp (or 19-bp?) deletion in exon-1 - it would be valuable to include a discussion whether patients have been identified with deletions and frame-shift mutations in this region of SALL4 exon-1. And also clarify, if not clearly stated in the text, that both SALL4A and SALL4B will be impacted by this mutation. Are there examples of patient mutations which only impact SALL4A?
8. For the SALL4 blots in Figure 2B, is the antibody expected to detect both isoforms (SALL4A and SALL4B), and which isoform is shown? If two isoforms are detected, they should both be presented in the figure.
9. SALL4 expression should be shown for Figure 2C to see whether the >50% down-regulation of SALL4 at the protein level may be partially driven by transcriptional changes.
10. The number of experimental replicates should be indicated in all figure legends where relevant. Raw data points should be plotted visibly over the violin plots (e.g. Figure 2C).
11. For Figure 3A, the images of the DAPI and NANOG/OCT4 staining should be shown separately in addition to the overlay.
12. The metric 'Corrected Total Cell Fluorescence (CTCF)' should be described in the methods. The number of images used for the quantification in Figure 3A should be indicated in the legend, and error bars included if multiple images were quantified.
13. Figure 3C - what are the 114 differentially expressed genes? Some interesting genes could be labelled on the plot and the data used to generate this plot should be included as a Supplementary Table. Supplementary Tables should similarly be provided for Figure 6C, Day 14 and Supplementary Figure 2B, Day 5.
14. Figure 4B. The shared peaks are not shown. For completeness, it would be ideal to show these sites also.
15. Figure 4C is difficult to interpret. Why is the plot asymmetric to the left versus right? What does the axis represent - % of binding sites?
16. Line 224-225. What do n= 3,729 and n= 6,860 refer to? There appear to be many more binding sites indicated in Figure 4B, therefore these numbers cannot represent 86% and 97% of sites?
17. Figure 4E. Several TFs mentioned in the text (Line 243) are not shown in the figure, it would be good to show all TFs motifs mentioned in the text in this figure. Again, there is no mention of whether a sequence-specific motif is detected for SALL4 (e.g. an AT-rich sequence) from this motif analysis.
18. Figure 4G. How was the ATAC-seq data normalized for the WT and SALL4-het-KO lines for this comparison? The background levels of accessibility seem quite different in Replicate 1.
19. Figures 5B-C could be exchanged to flow better with the text. A Venn diagram could be included to show the overlap between the sites losing BRG1 in SALL4-het-KO (13,505 sites) and the Day5-specific SALL4 sites (17,137 sites).
20. At Day 5, the authors suggest a shift towards neural differentiation. It could be interesting for the authors to perform qRT-PCR at Day 5 for some neural markers or look in the Day 14 data for markers of neural differentiation at the expense of CNCC markers.
21. Is the data used to plot Figure 5D the same as Figure 4G. If so, why is only one replicate shown in Figure 5D?
22. Figure 6A. How many replicates are shown? If n=2, boxplots are not an appropriate to represent the distribution of the data. Please include n= X in the figure legend and plot the raw data points also.
23. Figure 6B. What is the significance of CD99 for CNCC differentiation?
24. Figure 6F. No error bars are shown, how many replicates were performed for this time couse? The linear regression line does not appear to add much value and could be removed.
25. At line 304, the authors state "while SALL4-het-KO showed a significant downregulation of these genes". Perhaps 'failed to induce these genes' may be more accurate unless they were expressed at Day 5 and downregulated at Day 14.
26. Lines 332-335. The genes selected for pluripotency, neural plate border, CNCC specification could be plotted separately in the Supplement to show individual gene expression dynamics.

Significance

This work provides a conceptual advance in understanding the aetiology of human SALL4-mediated craniofacial malformations in a cell-type specific manner. Leveraging an in vitro differentiation system, the authors define development timepoints and cell types impacted by altered SALL4 dosage. Additionally, the authors provide interesting mechanistic insights how the teratogen thalidomide may impact craniofacial development through proteasomal targeting and degradation of SALL4, and subsequent impact on neural crest differentiation progression.

Several audiences will be interested in this work: stem cell and developmental biologists (especially those interested in neural crest and facial development), and researchers interested in enhancer regulation, chromatin biology or gene regulatory mechanisms. Clinician scientists and geneticists will be interested in the proposed implications for mechanisms of disease.

Field of expertise: We have expertise in mechanisms of gene regulation and in vitro models of early development. We are not experts in modeling protein interactions in silico.

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Referee #1

Evidence, reproducibility and clarity

Summary: The authors have previously published Mass-spectrometry data that demonstrates a physical interaction between Sall4 and the BAF chromatin complex in iPSC derived neurectodermal cells that are a precursor cell state to neural crest cells. The authors sought to understand the basis of this interaction and investigate the role of Sall4 and the BAF chromatin remodelling complex during neural crest cell specification. The authors first validate this interaction with a co-IP between ARID1B subunit and Sall4 confirming the mass spec data. The authors then utilise in silico modelling to identify the specific interaction between the BAF complex and Sall4, suggesting that this contact is mediated through the BAF complex member DPF2. To functionally validate the role of Sall4 during neural crest specification, the authors utilsie CRISPR-Cas9 to introduce a premature stop codon on one allele of Sall4 to generate iPSCs that are haploinsufficient for Sall4. Due to the reports of Sall4's role in pluripotency, the authors confirm that this model doesn't disrupt pluripotent stem cells and is viable to model the role of Sall4 during neural crest induction. The authors expand this assessment of Sall4 function further during their differentiation model to cranial neural crest cells, assessing Sall4 binding with Cut+Run sequencing, revealing that Sall4 binds to motifs that correspond to key genes in neural crest differentiation. Moreover, reduction in Sall4 expression also reduces the binding of the BAF complex, through Cut and Run for BRG1. Overall, the authors then propose a model by which Sall4 and BRG1 bind to and open enhancer regions in neurectodermal cells that enable complete differentiation to cranial neural crest cells.

Overall, the data is clear and reproducible and offers a unique insight into the role of chromatin remodellers during cell fate specification.

However, I have some minor comments.

1. Using AlphaFold in silico modelling, he authors propose the interaction between the BAF complex with Sall4 is mediated by DPF2, but don't test it. Does a knockout, or knockdown of DPF2 prevent the interaction?
2. OPTIONAL: Does knockout of DPF2 phenocopy the Sall4 ko? This would be very interesting to include in the manuscript, but it would perhaps be a larger body of work.
3. Figure 1, the day of IP is not clearly described until later in the test. please outline during in the figure

3- What is the expression of Sal1 (and other Sall paralogs) during differentiation. The same with the protein levels of Sall4, does this remain at the below 50%, or is this just during pluripotency? 4. The authors hypothesise that Sall4 binds to enhancers- with the criteria for an enhancer being that these peaks > 1KB from the TSS are enhancers. Can this be reinforced by overlaying with other ChIP tracks that would give more confidence in this? There are several datasets from Joanna Wysocka's lab that also utilise this protocol which can give you more evidence to reinforce the claim and provide further detail as to the role of Sall4 5. The authors state that cells fail to become cranial neural crest cells, however they do not propose what the cells do instead. do they become neural? Or they stay at pluriopotent, which is one option given the higher expression of Nanog, OCT4 and OTX2 that are all expressed in pluripotent stem cells. 6. In general, I would like to see the gating strategy and controls for the flow cytometry in a supplemental figure. 7. For supplementary figure 1- please include the gene names in the main image panels rather than just the germ layer.

Significance

The strength of this study lies in its well-designed and clearly presented experiments and datasets. In particular, identifying the specific SALL4 isoform that interacts with the BAF complex-and further exploring the implications of this interaction-is a major highlight. The authors also make effective use of in silico modelling with AlphaFold, offering valuable mechanistic insight into how this interaction is mediated.

The topic should have appeal to researchers in developmental biology and epigenetics. This study represents a significant step forward in validating the interaction between SALL4 and the BAF complex, and it highlights the requirement of SALL4 for BAF-mediated chromatin remodelling during neural crest specification. These findings are likely to be of interest to those studying the gene regulatory mechanisms underlying craniofacial development.

However, while the authors outline the roles of SALL4 and the BAF complex in chromatin remodeling during neural crest development, the downstream effects on cell fate specification could be more thoroughly examined. Currently, Gene Ontology analysis is the primary method used to interpret these consequences, and additional functional validation would strengthen the conclusions.

Intended audience: Basic research, epigenetics in pluripotency and neural crest development.

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Reply to the reviewers

Response to reviewers

We thank the reviewers for their constructive feedback, which has greatly improved the clarity and rigor of our manuscript. We have carefully addressed each comment below, indicating changes made to the text, figures, or supplementary material where appropriate. References to line numbers correspond to the revised version of the manuscript.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

* In this paper, the authors focus on the role of Reticulon-1C in concert with Spastin in response to axonal injury. In data mining, they find axonal mRNAs encoding for ER-associated proteins including Rtn-1. They establish a knockdown targeting both Rtn-1 isoforms Rtn-1A and Rtn-1C. They observe decreased beta-3-Tubulin levels in the soma while axonal protein levels are unchanged. In microfluidic devices, they characterise the effect of a compartment-specific Rtn-1 KD on axonal outgrowth in the axonal compartment. The authors quantify axonal outgrowth, seeing increased outgrowth in an axonal compartment-specific Rtn-1 KD, while the effect seems to be reversed when applying the KD construct in the somatic compartment. When focussing on the axonal growth cone, they find the Rtn-1 KD shows differences in several morphological features of the growth cone. They find an increase in Tubulin levels in an axonal compartment-specific, but a decrease in a somatic compartment-specific Rtn-1 KD. Colocalisation of Rtn-1C and Spastin is shown to be monolaterally increased following axotomy. Combining axotomy with the Rtn-1 KD shows increases in dynamic microtubule growth rates and track lengths. In another model system, neuron balls, they show Rtn1-C, but not Rtn1-A to be present in the axon. In a puro-PLA assay they also show it can be synthesised in the axonal compartment. To investigate the mechanism enabling the cooperation between Spastin and Rtn-1C, they move to a cell line model in which they see a correlating distribution between Spastin and Rtn-1C but not Rtn-1A. Finally, they use in silico modelling to speculate on binding between Spastin domains and Rtn-1 isoforms.*

Major comment:

The rationale behind the work is convincing, however some interpretations are presented as more robust than some data allow. Most notably, while the interaction between Rtn-1 and Spastin has been shown prior to this study, it is only presented here through in silico analysis. In figure 5, an increase in the growth rate of dynamic microtubules is observed in either a Rtn-1C KD or by using a Spastin-inhibitor. Due to a described increase in colocalisation between Rtn-1C and Spastin (5A), the increase in growth rate is displayed as caused by Rtn-1 promoting Spastin's severing ability. This result might however be correlative. Further in the injured samples, Spastin-levels seemingly increase (in the representative images) and it is thus not surprising that the level of Rtn-1C colocalising with Spastin increases as well. This might not be indicative of a cooperation and further experimental evidence are required.

R: We thank the reviewer for this thoughtful comment. We agree that our interpretation should be more cautious, and we have revised the Title, Results and Discussion sections accordingly. In particular:

1. Following yours and other reviewer comments, we have analyzed a new set of experiments regarding the STED images of non-injured and injured axons. To eliminate the risk of artifactual descriptions, we have avoided deconvolution and worked directly with raw STED images (Figure 5A). Under these conditions, the distribution of Spastin and its intensity in distal axons are not modified by injury, nor those of Rtn-1C and Spastin (Supplementary figure 4). We emphasize in the revised text that the in silico modeling we present is supportive, but not definitive, of a direct interaction. To address this concern, we clarify that our study builds on prior evidence of biochemical interaction between Rtn-1C and Spastin (Mannan et al., 2006), and that our own data demonstrate: i) compatible subcellular distribution in axons by super-resolution (STED microscopy, Figure 5A);ii) a potential functional interplay in axons (rescue of β3-tubulin levels by Spastin inhibition, Figure 5B), and iii) isoform-specific co-distribution with Spastin in heterologous cells that is associated with changes on microtubule integrity (see improved Figure 7). Together, these results go beyond correlative localization, but we acknowledge that they do not directly demonstrate a molecular complex in axons. Thus, we now indicate that "Although we did not directly test their molecular association, these results are consistent with Rtn-1C and Spastin sharing a similar subcellular localization, potentially enabling their functional interaction in distal axons" (lines 285-287)

We would like to clarify a possible misunderstanding: in our experiments, the increase in microtubule growth rate was observed after axonal Rtn-1 KD. Spastazoline (SPTZ) only prevented the reduction in β3-tubulin levels induced by Rtn-1 KD, while leaving the KD-driven increase in growth rate and track length unaffected (Figures 5B-E). Thus, our interpretation is that axonal Rtn-1 KD correlates with increased Spastin function. (lines 307-309)

Other comments:

• Generally, graphs would benefit from individual values plotted as well as the summary. Font sizes and types (but rarely) are sometimes inconsistent. Proteins should be consistently written (capitalised or not).

__R: __ We agree with the reviewer and thank for taking the time for noticing these inconsistencies as it significantly affects the quality of the work. We have improved several figures and added graphs plotting individual values (Figures: 2 C, 2E; 4 (A-E); 5E; 6D). We have reviewed the Font size and types more carefully and capitalized the proteins accordingly.

• *Table 1 and figure 1 present data collected from a vast amount of resources. It should be highlighted that datasets from which data was obtained includes many different models, different DIVs and neuronal cell types. Figure 1B may benefit from a different colour scheme. "Ex-vivo" should be "Ex vivo". For "ER mRNAs are a relevant category" it is not described what "relevant" would mean in this context. The title might remove this small part or describe it in the text. It should be described how it is decided that mRNAs are "common". *

• *

__R: __We have now highlighted in the result section the diverse origins of the analyzed samples; We removed the indicated part from the text and explained that common mRNAs were chosen based on the Benjamini-Hochberg (Ben) analysis. (Page 33, lines 1299-1304).

* - Figure 2: add description to y-axis to describe what fold change is displayed, applies to multiple figures. Will improve readability of the figures. In 2C, the ROI showing neuronal somata should be increased to show part of the axon and not cut off the soma.*

• *

__R: __We thank the reviewer for taking the time to highlight this. We have included this modification in figure 2 and throughout the article. We have also enlarged the indicated ROIs in figure 2C as requested. (Page 34)

• *Figure 3: Three out of four axonal compartments seem to be comprised of dying or damaged axons. Especially the axonal KD scrambled image. It should be ensured that neuronal cultures are healthy. *

• *

__R: __We completely agree with the reviewer that the selected images were not describing the general good health of axons which has been accredited by the lack of fragmentation and functional responsiveness shown in (Figure 4 and 5 B, C, E). Thus, we have now replaced the previous axonal fields by more representative ones (Figure 3). (page 36)

• *

Typo in "intersections". The schematic of 3B is a great addition to explain the graphs above. Perhaps it could be a bit refined as it is currently hard to see whether this is a neuron or a growth cone without context. Maybe show where the axon connects to the depicted growth cones and change the third icon which looks like it was crossed out. Small formatting issues: remove additional space bar before "Figure 3." And add after "Bar"

__R: __Many thanks for these great suggestions. We have now improved the figures as suggested and changed the indicated formatting issues. (page 36)

- Figure 4: If not misunderstanding what is depicted, in 4A and B, different lookup tables are used to depict the same signal. Only one of each images is necessary. Do the axons have more tiny branches in the Rtn-1 KD condition in 4A? Unclear why Rtn-1 levels are increased in the Rtn-1 KD (4C), please clarify.

• *

__R: __We thank the reviewer for these observations. The reviewer is correct that different lookup tables were initially applied to the same image. Our intention was to highlight the fine distribution of axonal Rtn-1, but since this aspect is already clearly shown in previous figures, we now retain only a single lookup table. The appearance of tiny branches in the Rtn-1 KD condition represents an isolated observation and does not reflect a consistent or robust phenotype associated with Rtn-1 KD.

As the reviewer points out, the increase of Rtn-1 in the cell bodies of injured neurons following axonal KD was initially surprising to us. However, this was a consistent phenomenon, as shown in the improved Figure 4. Of note, previous studies have reported that total Rtn-1C (but not Rtn-1A) levels increase in response to injury in cortical neurons(Fan et al., 2018). In our case, we interpret this as a compensatory somatic response triggered by the local reduction of Rtn-1 in injured axons. This interpretation is also consistent with the apparent lack of effect of siRNA on distal axonal Rtn-1 levels when applied locally after injury (while somatic application of the same siRNA does reduce axonal Rtn-1). Thus, after 24 hours of KD, the somatic upregulation of Rtn-1 may partially compensate for its expected local synthesis decrease. We have clarified this assumption in the revised text. (lines 247-251)

- Figure 5: It may be easier to understand what "axotomy" samples are if just referred to as "injured" as later in the same figure. The procedure could also very briefly be explained in the results. 5C should depict AUC in µm2 not µm. 5D Spastin is barely visible, brightness and contrast should be adjusted to enhance visibility.

• *

__R: __We thank the reviewer for these helpful suggestions and have implemented the requested changes in Figure 5. Specifically:

We now consistently refer to "axotomy" samples as "injured" throughout the figure and article. In addition, a brief explanation of the axotomy procedure has been added before Figure 2 and before figure 5, also the description has been clarified in Materials and methods. (lines 191-192) and (lines 289-290) and (lines 779-787)

To improve the reproducibility of our outgrowth measurements, we revised this analysis approach. Based on previous work from a co-autor (McCurdy et al., 2019), instead of reporting the "relative number of intersections," we now present the total counts obtained from Sholl analysis of binarized axons (see Methods). To this end, we took advantage of the NeuroAnatomy plugin of FIJI, which more precisely tracks axon trajectories and makes the measurement more independent of axon width. Also, this new approach avoids the conflict we had with what we considered the "first line" after the groove ends, which was a bit of arbitrary. Accordingly, the correct term is now "summation of intersections (sum.)" at different distance bins, as reflected in Figure 5D. (page 40)

For the former Figure 5D (now Figure 5B), we have improved the acquisition of representative images and applied a different set of lookup tables to enhance visibility. (page 40)

- Figure 6: It should be made clear why it is necessary to switch to another model system just for 6A, please indicate this in the text. PCR bands seem very pixelated, check the quality. It is unclear why soma genes/proteins were only tested with either PCR or WB others with both. Rtn-1C and Rtn1-A should be presented in the same order in the PCR and WB panel. Correct "Rtn1-1A" typo. In 6D, 1.5 dots per soma seems like a low number. When normalized to the area the soma vs the axon occupies, the compartmentalization does not work? Maybe it makes sense to refine analysis or apply puromycin in the somatic compartment and analyze the axonal compartment as comparison?

__R: __Many thanks for these observations. We have now included the following clarification in the text: "We sought to characterize the isoform expression of Rtn-1 mRNA and protein in both axons and cell bodies. Because microfluidic chambers yield only limited cellular material, we adopted an alternative culture approach using 'neuronballs.' This method enables the segregation of an axon-enriched fraction by mechanically separating axons from somato-dendritic structures" (lines 375-376).

The resolution of PCR bands has been improved in the revised figure. Note that because the amount of cellular material is relatively scarce, we did not obtain too strong bands.

The difference in the genes/proteins used for characterizing RNA and protein samples reflects our intention to treat both approaches as complementary. The PCR markers were primarily included to confirm sample purity, which also applies to the WB samples since they derive from the same preparation. In both assays, we used MAP2 as a dendritic marker to demonstrate axonal purity. While we acknowledge that the same genes could have been tested by both methods, we believe the results as presented adequately demonstrate the effective isolation of axons.

We have switched the order of Rtn-1C/1A for consistency across PCR and WB panels and corrected the indicated typo in Figure 6A.

We agree with the reviewer that an average of 1.5 puncta per soma initially appeared low. We have identified at least three reasons for this:

First, the signal derives from only a 15-minute puromycin pulse, which is a very short labeling window. Second, our puro-PLA assay is particularly stringent, as ligation relies directly on puromycin- and Rtn-1C-labeled primary antibodies, without the additional spacing normally introduced by secondary antibodies. In standard PLA, the critical distance for amplification is ~30-40 nm, whereas in our assay this distance is even more restrictive. Third, in our initial analysis we applied an overly cautious threshold to define "true" amplification. We have now refined this threshold using a baseline defined by the absence of puromycin stimulation. With this improved criterion, we now quantify an average of ~5 puncta per soma and ~10 puncta per 1000 µm² of axonal area (Figure 6D and Supplementary Figure 3D). Assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in soma. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value, which is compatible with the idea thar cell bodies dominate neuronal protein synthesis.

Following the reviewer's valuable suggestion, we performed additional quantifications in which puromycin was applied exclusively to the somatic compartment. Under these conditions, we still observed amplification in axons (~5 puncta per 1000 µm²), although this value was significantly lower than when puromycin was applied directly to axons. This analysis provided a novel appreciation of the puro-PLA technique in neurons: at least half of the signal originates in the axonal compartment, while a portion may reflect proteins synthesized in soma and transported anterogradely to the axon through yet-unknown mechanisms (potentially involving rapid anterograde transport) (Figure 6D). (page 42)

• Figure 7: 7A shows two images depicting the same information that may not be needed. Can probably be removed. In 7B there is no negative (or any) correlation between Spastin levels and Tubulin, however later it is mentioned that Rtn-1C transports Spastin thus causing a decrease in Tubulin at certain locations? It is nclear if Spastin levels vary intensely between different samples. Mean intensity of the somatic area may be beneficial to rule this out. 7B Tubulin on the right top panel seems to have a decrease in Tubulin levels which is not visible due to the Y axis of Tubulin being set to a different range than the middle and lower panel. The average of line scans from multiple cells may be helpful to determine whether there is indeed no colocalization between Rtn-1A and Spastin. The provided representative images seem to show similar degrees of colocalization between Spastin and Rtn-1A/C.

• *

__R: __We thank the reviewer for these valuable observations and acknowledge that Figure 7 may have caused confusion. We have eliminated the fluorescence line-scan traces, as they can be biased depending on the region of the cell analyzed. Although this may not have been sufficiently emphasized in the text, we had already performed a quantitative colocalization analysis across multiple cells and independent experiments, using Mander's coefficients (Figure 7B). These analyses showed higher colocalization between Rtn-1C and Spastin compared to Rtn-1A. Regarding the concerns about variability in Spastin levels or possible bias from Y-axis scaling, we have eliminated those traces by the risk of bias. Also, we had already quantified the total tubulin fluorescence intensity across all the z-stacks and from multiple cells from independent experiments as shown in Figure 7C. To further rule out artifacts caused by variable transfection efficiency, we quantified total fluorescence intensity in both RFP and GFP channels across conditions. As shown in Supplementary Figure 6, no significant differences were observed, suggesting that the changes in tubulin reflect specific effects of Spastin/Rtn-1C co-expression rather than variability in expression levels.

Results: - It would be helpful to reiterate the hypothesis at the start to ease the reading flow.

__ R: __Many thanks, we have introduced a line reiterating the hypothesis as suggested (lines 117-118)

- There seems to be minor redundancy in lines 132-138.

• *

__R: __Indeed, we have now removed the indicated phrase.

• There are several spellings, proof-reading is recommended. For example, in line 136 should be "promotes". 160 "localla", 192 should be "the actin cytoskeleton".,194 should be "we first examined", 195 should be "Different", 223 "using", 259 "axons".

__R: __We apologize for the spellings; we have now performed a careful proof-reading and introduced these corrections.

- 154-155: Unclear, why the lower MW Rtn-1C was seen as more important.

__R: __We apologize for not being clear enough. It is not necessarily more important, but we just took the Rtn-1C molecular weight as reference for the analysis considering that this isoform is the predominant in axons. In any case we have found a significant effect for both isoforms at least on siRNA 2 (data not shown), which is now expressed in the text (line 165-169) : "We also examined the 180 kDa band and found that siRNA 1 reduced expression to a mean of 0.41 relative to Scr, showing a strong trend that did not reach statistical significance (p = 0.05; N = 3; Wilcoxon test compared to 1, data not shown). In contrast, siRNA 2 further reduced expression to a mean of 0.29, which was statistically significant (p = 0.04; N = 3; Wilcoxon test compared to 1, data not shown)."

- 167 results of 2E not stated before interpreting them.

• *

__R: __We have corrected this mistake.

- 181 would suggest "outline" instead of "perimeter".

• *

__R: __We have considered this suggestion and included "outline", nevertheless the morphometric parameter is defined as perimeter, so we retained the term, but with the suggested clarification.

• *

- 183-184 "longest shortest path" is a confusing term.

__R: __We agree that it is a confusing term, thus have now introduced multiple clarifications for the term in the leyend of figure 3 (page 36), and with more detail in a new section of Materials and methods (lines 697-699).

• figure 4B should be referenced earlier in the sentence.

__R: __We have corrected the sentence in the text.

- 243-244 may be correlation. Rtn-1 and Spastin do not necessarily interact so that this result is achieved.

• *

__R: __Thanks for the clarification, we are aware that so far in the manuscript the conclusion is not correct, thus now we have stated at the end of the paragraph: "Together, these observations suggest that axonal Rtn-1 KD correlates with higher Spastin microtubule severing" (lines 307-309)

- 246: In figure 1 the KD seemed to influence both Rtn-1 isoforms, why not here anymore? 259 "axons". 284 "counteract" instead of "suppress"?

• *

__R: __We acknowledge the confusion at this point of the article because of measuring a specific isoform. We now indicate that we will focus on Rtn-1C because of previous evidence of the literature pointing to an interaction of Rtn-1C with Spastin (line 264-267). Later we show that Rtn-1C is the predominant isoform in axons (Figure 6). We have corrected all the suggestions in the manuscripts.

- 485: rephrase as the interaction between Rtn-1C with Spastin has not been shown directly in these experiments.

__R: __Many thanks for the relevant clarification. Now, we have corrected:" Here, we have described an emerging mechanism relating Rtn-1C with the activity of Spastin, which is the most frequently mutated isoform in HSP (Hazan et al., 1999; Mannan et al., 2006)." (line 632-634). * Methods: 535 "in PBS". 543 citation error. 689-699 is it necessary to add a gaussian blur?*

• *

__R: __We have corrected the words and removed the wrong reference. Regarding the use of Gaussian blur, it is a very important point. We used this approach because, in our experimental conditions, it was critical to highlight moving particles that otherwise would go unnoticed by the noise. This was particularly manifest for the seemingly more "unorganized" movements of axonal microtubules after injury.

References: Mannan, A U et al. appears twice in the citation list (36 and 44).

* *R: Many thanks for the observation. Now we have corrected it.

Reviewer #1 (Significance (Required)):

Overall, this manuscript describes novel fundings which will be interesting to the neuronal cell biology community and scientists working on the field of neuronal injury and regeneration. It is well structured, and the data are mostly well presented but sometimes conclusions are over-interpreted. However, several points need to be addressed in a more convincing way.

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

Axonal mRNA localization and localized translation support many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

Major concerns:

2. In figure 1, the authors provide an analysis of overlapping axonal mRNAs. There are more axonal transcriptome studies and a recent study by von Kugelgen and Chekulaeva (2020; doi: 10.1002/wrna.1590) already performed such an analysis, which included more studies. It would be good to mention this. It can be perceived that studies were now chosen to get the outcome that Rtn-1 is present in all studies. For example, von Kugelgen finds mRNA coding for RTN3, another ER structural protein, as present in 16 out of 20 studies analyzed. That said, the authors present more reasons to look at Rtn-1, so the selection to continue with this protein remains valid but can be written up differently so not to present it as the 'sole' ER-shaping protein consistently present in axonal transcriptomes. __R: __We appreciate this important observation to enrich the article; we are aware that the transcriptome data can be even further expanded to more recent studies. Thus, we have now included this reference in the main text and highlighted the relevant finding of RTN3. However, Kugelgen and Chekulaeva used data from dendrites/axons (neurites). Thus, we indicate that "...On a similar approach, but combining data from dendrites and axons, it was found that Reticulon-3 *mRNA is present in 16 out of 20 studies, further suggesting a wider presence of other mRNAs coding for ER structural proteins in axons " (line 128-131)

3. The description of methods is currently insufficient and incomplete and does not allow for reproducibility of this study. For example, different Rtn-1 antibodies seem to be used in this study. Is the same antibody used for staining and WB? There is no listing of any of the antibodies used in the study and which one is used for which technique/experiment. This should be clarified and should be easy to do so in the methods section (antibody name, origin/company, dilution used) to enhance reproducibility of this study. This is not limited to primary antibodies and any information on secondary antibodies, including what was used for STED is completely missing.*

4. *

__R: __Thanks for these critical comments. First, we apologize for the former method version which was mistakenly not as accurate as it should. We have now revisited it and improved several points throughout this section. Regarding the use of primary and secondary antibodies, plasmids, siRNAs, and general reagents, they are all indicated in the Supplementary material, including company and dilution ("Reagent tables").

• The timeline of KD experiments in Figures 2 and 3 are unclear. For the Western blot KD is performed at DIV7 and collected 48 hours later. However, this is not specified for the stainings done in Figure 2C-E. Is this also at DIV7 and then for 48 hours? In figure 3 the siRNA is added at DIV8 (together with axotomy) and outgrowth is measured 24 hours later. Is 24 hours sufficient to achieve knockdown? Is this also what was done for stainings? Later on in Figure 5B, 48 hours of KD is again used. It is unclear what the rationale of these differing timepoints is. Why was this chosen? Is the timeline also the reason for the difference in segment lengths chosen? In Figure 3, there is a significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5.*

__R: __We regret the confusion, now all this information is explicitly clarified in the main text (lines 297-299) and the corresponding figure legends. We have strong reasons to have used these different time points. Figure 2 A-B is aimed at validating the siRNA against Rtn-1 thus we treated 7 DIV cultures for 48 hours to be sure of revealing a global effect by WB. In figure 2 C-D, we used the same 7 DIV cultures, but only for 24 hours. The reason for this is that, once the RNAi was validated, we explored its control on local synthesis in a shorter period based in previous literature supporting that axonal KD for 24 hours is sufficient for regulating axonal transcripts (Batista et al., 2017; Gracias et al., 2014; Lucci et al., 2020). We are also confident of using this time point based in the new supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD.

In figure 3, we performed axotomy thus we had to wait a longer period for axons to grow (8 DIV) before fully cut them out, in this case we performed axonal KD from 8 to 9 DIVs. This is the same period used for the staining and quantifications shown in figure 4. All this is properly clarified in the main text and figures.

In Figure 5 we performed a more challenging experiment that required to transfect cells with an EB3-GFP plasmid, then perform axotomy along with axonal KD as well as pharmacological treatment selectively in axonal compartment. First, we tried to measure microtubule dynamics under the same temporal frame of figure 3. Nevertheless, expression levels of EB3-GFP were not adequate for axonal measurements by live-cell imaging. Therefore, compared to figure 3, we increased the time frame after axotomy 24 hours (from 9 to 10 DIV) by this technical reason, but also to explore whether the changes on tubulin intensity might be revealed more clearly (which was the case, figure 5B). These considerations are now included in the main text

Regarding the significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5. Given that in figure 5D axons are left growing for two days instead of one, the number of intersections and the differences between conditions is modified compared to figure 3, while retaining the overall trends. Note that to improve the reproducibility of our outgrowth measurements, we revised this analysis approach. Based on previous work of a co-autor (McCurdy et al., 2019), instead of reporting the "relative number of intersections," we now present the total counts obtained from the Sholl analysis of binarized axons (see Materials and methods). To this end, we took advantage of the NeuroAnatomy plugin of FIJI, which precisely tracks axon trajectories and makes the measurements more independent of axon width segmentation. Also, this new approach avoids the conflict we had with what we considered the "first line" after the groove ends, which was a bit of arbitrary. Accordingly, the correct term is now "summation of intersections (sum.)" at different distance bins, as reflected in the new Figure 5D.

Could the authors provide a rescue condition for their siRNA (using a siRNA-resistant construct) to show that their siRNA is specific for RTN1. They nicely show the efficiency of the siRNA but not its specificity. This is crucial because if not specific, this will affect a large part of their study. They already have RTN1A and RTN1C constructs available. Such a rescue experiment should ideally also be performed for one or more of their phenotypic experiments, such as the one presented in Figure 3A or 5 to show that the phenotype is really RTN1 dependent. If done by re-expressing either RTN1A or RTN1C, this could provide insightful information on the relevant isoforms.

__R: __We agree with the reviewer that this is a critical point. A major challenge in demonstrating the functional role of axonally synthesized proteins using a KD approach is that the rescue may also need to occur locally. Since axonal Rtn-1 appears to play a distinct role compared to its somato-dendritic counterpart (Figure 3), a siRNA-resistant construct would ideally require an axon-targeting sequence to restore local synthesis. As this is technically demanding, we have not yet been able to perform such an experiment, but we are actively working on identifying the optimal sequence to direct Rtn-1C to axons. Importantly, studies performing axonal KD typically rely on at least two independent siRNA sequences, thereby minimizing the likelihood that a phenotype arises from off-target effects. Thus, we have now validated a third siRNA (siRNA 3), which selectively downregulates Rtn-1C. Then, following the same experimental frame of figure 3, we performed axonal Rtn-1 KD after injury and observed that siRNA 3 also significantly increases the outgrowth of injured axons (Supplementary figure 2). This suggests that, at least this phenotype, is not product of an off-target effect. Complementarily, pharmacological rescue with the Spastin inhibitor SPTZ mitigated both the reduction in distal axonal β3-tubulin and the increase on axon outgrowth, supporting that the observed phenotypes are unlikely to arise from off-target effects. If these effects were due to random interference with unrelated mRNA targets, inhibition of an ostensibly independent target such as Spastin would not be expected to yield such a consistent rescue. Accordingly, SPTZ treatment alone did not increase β3-tubulin, indicating that its action is specifically contingent upon Rtn-1 KD. Taken together, the pharmacological rescue in axons (Figure 5B) and the Rtn-1C/Spastin co-distribution in heterologous cells, which correlates with preserved microtubules (improved Figure 7), provide converging evidence to suggest that Rtn-1C-Spastin interplay may underly the observed phenotypes in axons.

• I find the data presented in Figure 4A/B confusing. Axonal RTN-1 KD does not reduce axonal RTN1 levels, but somatic KD does. I understand that this implies most protein comes from the soma, and the authors indeed present an explanation that increased somatic RTN1 occurs after axonal KD as a compensation mechanism. However, this can also be interpreted that there is no axonal synthesis of RTN1 after injury and axonal KD has indirect or even aspecific effects. Their model depends on this difference. Their data in Figure 6 could provide supporting evidence if it shows RTN1 puro-PLA after injury. Along these same lines, in Figure 6, they nicely include a compartment control for puro-PLA. It therefore seems doable to include a somatic puromycin control for their axonal puro-PLA, to exclude and diffusion/transport of the newly synthesized peptides. This is especially considering two recent papers reporting on this possible phenomenon, although these studies were not performed in neurons.*

__R: __We consider the possibility that after injury there is no axonal Rtn-1 synthesis as a plausible and relevant appreciation. Unfortunately, we could not perform a puro-PLA experiment after injury, which would have provided a more definite answer. However, now we are more confident of regulating Rtn-1 synthesis before injury as supported by a new supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD. Thus, based on the similar phenotypes observed before and after injury, we consider our results are still compatible with Rtn-1 axonal synthesis being downregulated, but not absent after injury. First, axonal Rtn-1 KD decreased β3-tubulin levels before and after injury according to figure 5B and the improved statistical analysis performed on figure 2E. Similarly, axonal Rtn-1KD significantly increases microtubule growth rate before and after injury according to the current statistical comparisons (Figure 5E). Second, if β3-tubulin decrease was a merely unspecific siRNA targeting, it is unlikely that SPTZ treatment should increase and restore β3-tubulin levels only in the context of axonal Rtn-1 KD (Figure 5B). We have now included these considerations in the discussion (lines 537-543). Although on a different track, the mechanistic relationship between Rtn-1C and Spastin suggested in Figure 7 could make more plausible that a similar phenomenon regarding the control of tubulin levels may occur locally in axons.

Following the reviewer's valuable suggestion, we performed additional quantifications in which puromycin was applied exclusively to the somatic compartment. Under these conditions, we still observed amplification in axons (~4 puncta per 1000 µm²), although this value was significantly lower than when puromycin was applied directly to axons (~10 puncta per 1000 µm²). This analysis provided a novel appreciation of the puro-PLA technique in neurons: at least half of the signal originates in the axonal compartment, while a portion may reflect proteins synthesized in soma and transported anterogradely to the axon through yet-unknown mechanisms (potentially involving rapid anterograde transport). Note that we revised the criteria for detecting true amplification spots based in staining without puromycin, which increased true amplification numbers. Still, these seemingly low values are compatible with reflecting a limited amount of time (only 15´ of puromycin pulse) and the stringent conditions of this experiment in which secondary antibodies were avoided by directly labeling primary ones. This approach makes the classical 30-40nm distance for PLA even narrower, thus reducing signal. In any case, assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in somata. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value, which makes sense for the expected difference in ribosome density.

• In Figure 5A the authors find an increased co-localization (RTN1/Spastin) after axotomy. From their images, it seems that the amount of Spastin is hugely increased, which would by default increase the chance of (random) colocalization of RTN1 on Spastin. Could the authors comment on this?*

__R: __Thanks for this relevant and constructive critique. We formerly based our colocalization analysis on deconvolved images. However, after performing several quantifications through different deconvolution parameters, we were not convinced about the robustness of this finding and the performed staining. Thus, we performed a new set of experiments and found that non-deconvolved images from the STED microscope were more informative about the expected tubular morphology of the axonal ER. Thus, we improved figure 5A, and now the main conclusion is just that both proteins are closely distributed in distal axons before and after injury.

• In figure 5E and 5F, the condition of scr + SPTZ is omitted. What is the reason for this? The explanation of results in these figures is confusing. The authors report a 'clear trend' in increase in comet track length and lifetime upon addition of SPTZ to axonal RTN-1 KD. This is however not significant. The comparisons that are made afterwards are confusing (e.g. increase in comet lifetime of SPTZ in non-injured axons with RTN1 KD compared to Scr+DMSO and KD + DMSO in injured axons). Their conclusion is axonal RTN-1 synthesis in injured axons (see my concern in the points above on this) governs microtubules growth rate beyond Spastin activity yet blocking Spastin activity still completely blocks the effect of KD on outgrowth.*

* *__R: __We thank this observation and fully agree that the general description provided in figure 5 E wasn't satisfactory. We have re-organized the descriptions of these results and performed more relevant statistical comparisons (lines 338-359). Based on the reviewer observation, we now conclude: "Together, these results suggest that axonal Rtn-1 synthesis controls microtubule dynamics in both non-injured and injured axons, mostly independently of Spastin-mediated microtubule severing." (lines 357-359).

Other/minor concerns:

- The gene ontology analysis in Figure 1A contains the category 'Endoplasmic reticulum'. In this category are mainly ribosomal proteins. Although in a gene ontology analysis these proteins will be included in this category, it is misleading in this respect since they are just as likely to be coming from cytoplasmic ribosomes. Although it cannot be excluded that these are ER-bound ribosomes, not in the last place because a recent study (Koppers et al., 2024, doi: 10.1016/j.devcel.2024.05.005) found ribosomes attached to the ER in axons, I believe the category should be adapted or at the least clarified in the text.

• *

__R: __Many thanks for the suggestion, which is now included in the text. "Note that several of the identified transcripts in the category 'endoplasmic reticulum' code for cytoplasmic ribosomal components, which indeed can be attached to the axonal ER (Koppers et al., 2024) and be locally synthesized in axons (Shigeoka et al., 2019)." (lines 125-128)

- Is RTN-1C isoform still an ER-shaping protein or rather an ER protein with alternative functions? The final sentence in the abstract makes a statement that a locally synthesized ER-shaping protein lessens microtubule dynamics. Could the authors provide a clearer description and discussion of the evidence in literature for this? RTN1C has been suggested to perform alternative functions in which case the statement that the local synthesis of an ER-shaping protein is important for axonal outgrowth should be adapted.

R: We agree with the reviewer and are aware that some non-canonical roles of Rtn-1C may partially explain the observed phenotypes. Thus, we have rephrased the last statement of the abstract: "These findings uncover a mechanism by which axonal protein synthesis provides fine control over the microtubule cytoskeleton in response to injury.". Also, we have modified the discussion section introducing new references accordingly..." Some studies have pointed to a non-canonical role for Rtn-1C in the nucleus, including DNA binding and histone deacetylase inhibition (Nepravishta et al., 2010, 2012). It is tempting to speculate that these still emerging roles may also contribute to the observed phenotypes. Of note, different axonally synthesized proteins exert transcriptional control in response to injury or local cues (Twiss et al., 2016)." (lines 576-580).

• Is there a difference in RTN1 distribution or levels pre- and post-axotomy?

R: Thanks for the suggestion, with the new analysis we have only found slight reorganization of Rtn-1C and Spastin in distal axons (Figure 5A). We have also included now quantification of their levels and found no significant differences for both proteins (Supplementary figure 4)

- Line 100/101 states 'the interactome of the axonal ER provides...'. To my knowledge there has been no study looking at the interactome of the axonal ER specifically. Surely axonal ER proteins are known but there is a difference.

• *

__R: __We agree with the reviewer that the phrase was misleading, so we rephrased it in the introduction "...Different lines of evidence support that the protein components of the axonal ER may interact with proteins that regulate microtubule dynamics"

* - Typo line 160 'localla'*

• *

__R: __Thanks for taking the time, we have now corrected it.

- In Figure S1 B, please add the DIVs to make it clearer what each graph corresponds to. The legend of S1B states different distances from the cell body but the graph shows distances from the tip.

• *

__R: __We have now corrected the legend accordingly.

- Figure 2C, why does B3 tubulin decrease in soma, aspecific effect of siRNA?

• *

__R: __This was indeed an unexpected finding. However, we do not observe unspecific or global changes in β3-tubulin levels (see Figure 2A and Supplementary Figure 2). Considering our other results linking Rtn-1 to the regulation of the microtubule cytoskeleton, we interpret this decrease as an indirect effect of Rtn-1 depletion rather than an off-target action of the siRNA. Moreover, if the effect were unspecific, both proteins would likely be reduced in the cell body, given that the siRNA was specifically designed to target Rtn-1 as its primary sequence-specific target.

- What is the rationale on the opposite effect found in outgrowth in Figure 3?

• *

__R: __The apparent opposite outcomes observed in Figure 3 - where axonal versus somatic Rtn-1 knockdown leads to divergent effects on axonal outgrowth - can be explained by compartment-specific environments and isoform distribution. The siRNA targets the conserved RHD region, reducing both Rtn-1A and Rtn-1C. Axons are enriched in Rtn-1C. Thus, axonal KD preferentially reduces Rtn-1C. In contrast, somatic KD reduces both isoforms. Rtn-1A, predominant in cell bodies, may probably engage other signaling pathways (Kaya et al., 2013). Interestingly, it was reported by Nozumi et al. (2009b) that global Rtn-1 depletion reduces axonal outgrowth in developing cortical neurons. This aligns with the notion that somatic KD mimics a more global loss of function, whereas axonal KD reveals a compartmentalized, pro-regenerative effect due to local Rtn-1C regulation. (All the references indicated here are in the main manuscript). These considerations are now included in the discussion ( lines 581-593).

* - Missing word 'we' on line 194*

• *

__R: __ We have corrected it.

- Typo line 629 'witmn h', please proofread the entire manuscript carefully.

• *

__R: __ We apologize for the spellings, now we have carefully revised the manuscript.

- Could the authors comment on why, in Figure 7B/C, GFP only is colocalizing with Spastin-RFP? In general, GFP should be diffusive and not display punctate colocalization with Spastin.

• *

We appreciate the reviewer's comment. Under normal conditions, GFP displays a diffuse cytoplasmic distribution. However, in our experimental setup, we observed punctate GFP signals only in the context of co-expression with Spastin-RFP. This is consistent with prior reports showing that soluble GFP can occasionally be sequestered into late endosomal structures (Sahu et al., 2011), which are also known to harbor the M87 Spastin isoform (Allison et al., 2013; Allison et al., 2019). To rigorously exclude the possibility of unspecific fluorescence crosstalk, we independently acquired each fluorophore channel and confirmed that GFP puncta were genuine and not due to bleed-through (Supplementary Figure 5). Further, cells expressing only GFP or only Spastin-RFP did not show overlapping puncta, and co-expression of GFP with Rtn-1A-RFP did not produce any apparent overlap, indicating that the punctate GFP pattern is specifically associated with Spastin co-expression. Thus, the observed GFP colocalization with Spastin reflects a biological phenomenon potentially linked to the endosomal localization of M87 Spastin, and not an artifact of imaging or fluorophore bleed-through.

Reviewer #2 (Significance (Required)):

* Axonal mRNA localization and localized translation support many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.*

*

The audience for this study will be mainly basic research in the fields of both axonal protein synthesis and axon regeneration. My expertise is in the field of mRNA localization and local protein synthesis.*

Batista, A. F. R., Martínez, J. C., & Hengst, U. (2017). Intra-axonal synthesis of SNAP25 is required for the formation of presynaptic terminals. Cell Reports, 20(13), 3085. https://doi.org/10.1016/J.CELREP.2017.08.097

Fan, X. xuan, Hao, Y. ying, Guo, S. wen, Zhao, X. ping, Xiang, Y., Feng, F. xue, Liang, G. ting, & Dong, Y. wei. (2018). Knockdown of RTN1-C attenuates traumatic neuronal injury through regulating intracellular Ca2+ homeostasis. Neurochemistry International, 121, 19-25. https://doi.org/10.1016/J.NEUINT.2018.10.018

Gracias, N. G., Shirkey-Son, N. J., & Hengst, U. (2014). Local translation of TC10 is required for membrane expansion during axon outgrowth. Nature Communications 2014 5:1, 5(1), 1-13. https://doi.org/10.1038/ncomms4506

Lucci, C., Mesquita-Ribeiro, R., Rathbone, A., & Dajas-Bailador, F. (2020). Spatiotemporal regulation of GSK3β levels by miRNA-26a controls axon development in cortical neurons. Development (Cambridge), 147(3). https://doi.org/10.1242/DEV.180232,

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

This manuscript investigates the relationship between the endoplasmic reticulum morphogen reticulon-1 (Rtn-1) and the microtubule severing protein spastin in axons after injury. The main message and conclusion of the paper is that local axonal synthesis of Rtn-1 plays a role in regulating the microtubule severing activity of spastin by interacting with spastin and inhibiting its activity. This mechanism would be important after injury by regulating axonal growth.

* The conclusions of the paper are based on the following claims:*

* 1) Rtn-1 is synthesized locally in axons.*

* 2) Specific downregulation in Rtn-1 in axons using microfluidic chambers affects microtubules abundance (measured by beta-3 tubulin) and promotes axon growth after injury.*

* 3) Inhibition of spastin MT-severing activity with a specific drug rescues the growth effect induced by axonal downregulation of Rtn-1.*

* 4) Rtn-1c interacts with spastin-M87 to limit its MT-severing activity in a cellular system upon overexpression.*

*

*

Major comments:

1) Evidence that Rtn-1 is synthesized in axons comes from two experiments. Initially, the authors show that Rtn-1 siRNA transfection in the axonal compartment of microfluidic chambers reduces Rtn-1 levels in axons, suggesting that there is some local synthesis. Although this method is very attractive, I am concerned about the statistical analysis. The graphs show bars rather than individual data points from the average of many neurons (about 300). The plots also show the SEM instead of the SD, thus covering all the variability that is inherent in this type of experiment. The statistics are probably not performed on the 3 biological replicates, but consider the individual neurons as N. This is obviously not correct, since neurons in an experiment may all be affected by the same technical problem and are not independent replicates. For this reason, I am a bit skeptical about this quantification. Another problem is that the quantification of the fluorescence intensity of the sample does not take the nuclei into account. Are the nuclei removed for analysis? Are the images single planes? Addressing the quantification issues is crucial also for data in Figure 4, where the authors show a different effect of Rtn-1 axonal KD after injury.

* The second experiment is the Puro-PLA in Figure 6D. This experiment shows an average of 1.5 dots of signal per soma, which is a very low level of translation for this compartment where most of the synthesis should be taking place. In the axons, it is not clear how they calculate the axonal area. Again, the number of dots detected is very low and the physiological significance is questionable. A control with a known mRNA translated in axons would be important.*

* Finally, as an important control, the authors should show the presence of Rtn-1 mRNA by FISH in their experimental system.*

__R: __We appreciate the critical points addressed here as they moved us to improve the quality of the findings. We analyzed cells/axons as statistical units to increase statistical power given the subtle nature of these local changes. We agree with the reviewer that this approach may increase the risk of finding false positives. To address this point, i) we plotted the individual data points and colored them according with the different experimental dates (all the dates showed a similar trend) ii) We indicated SD instead of SEM iii) We analyzed our data using linear mixed-effects models, with experimental date included as a random effect. This approach allows to preserve the granularity and statistical power, while avoiding pseudoreplication. To exclude artifactual changes, we now analyzed the intensity fold change of total fluorescence normalized to Scr. Our former quantifications were based on the corrected fluorescence intensity used to construct the plot profiles, which could be adding some distortion to the measurements. These changes were applied throughout figures 2 and 4 (pages 34 and 38, respectively). After these new analyses the formerly presented results remain valid.

We thank the reviewer for raising concerns about the quantification of fluorescence intensity in cell bodies. We now specify in Materials and methods that fluorescence intensity analysis of distal axons (always isolated by the microfluidic chambers) and of cell bodies was performed using the wide-field configuration of the microscope. In all the cases, a single (epifluorescent) plane was analyzed to reflect the total fluorescence of a cell or axon. We did not exclude the nuclear region from the quantifications, as this would also remove cytoplasmic signal located above or below the nucleus.

We also understand the concerns about puro-PLA experiments. We agree with the reviewer that an average of 1.5 puncta per soma initially appeared low. We have identified at least three reasons for this. First, the signal derives from only a 15-minute puromycin pulse, which is a short labeling window. Second, our puro-PLA assay is particularly stringent, as ligation relied directly on puromycin- and Rtn-1C-labeled primary antibodies, without the additional spacing normally introduced by secondary antibodies. In standard PLA, the critical distance for amplification is ~30-40 nm, whereas in our assay this distance is even more restrictive. Third, in our initial analysis we applied an overly cautious threshold to define "true" amplification. We have now refined this threshold using a baseline defined by the absence of puromycin stimulation. With this improved criterion, we now quantify an average of ~5 puncta per soma and ~10 puncta per 1000 µm² of axonal area (Supplementary Figure 3D). As it is now included in methods, we calculated the axonal area by binarizing β3-tubulin staining and only counted the true amplification spots inside this region. Assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in somata. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value which seems more reasonable. This is also compatible with most of Rtn-1C synthesis comes from the cell body.

Unfortunately, we could not be able to perform puro-PLA of other axonally synthesized proteins. Nevertheless, to further validate our puro-PLA signal, we tested the specificity of the Rtn-1C antibody we used for this assay by WB, IF, and Rtn-1 KD (Supplementary figure 3 A-C). In addition, we performed axonal Rtn-1 KD in microfluidic chambers for twenty-four hours, which elicited a significant decrease in puro PLA signal compared to Scr (Supplementary figure 3D). Together, these results strongly indicate that the quantified signal reflects Rtn-1C synthesis. To prove that Rtn-1 mRNA is present in these conditions, we now included a RT-PCR performed on RNA isolated from the somato-dendritic and pure axonal fractions of 8 DIV microfluidic chambers (Supplementary figure 3D). Note that the presence of this mRNA in axons has been supported by several studies, one of them using cortical neurons of similar DIV and cultured in microfluidic chambers (Table I and figure 1).

2) The effects on tubulin following Rtn-1 downregulation in axons is potentially very interesting, but the authors should be careful because it could also mean that the axons are suffering. Can they also stain for other cytoskeletal markers?

R: Regarding this concern, we are aware that in the former Figure 3 we mistakenly selected axonal fields that did not display healthy axons, which was not the dominant trend. This is accredited by the lack of fragmentation and by the functional responsiveness (microtubule dynamics) shown in Figures 4 and 5B, C, E. We have now replaced the previous axonal fields in Figure 3 with more representative axons (healthy), devoid of varicosities and fragmentation (page 37)

3) The results using SPTZ are very interesting and implicate spastin microtubule severing activity in the observed phenotype. In my opinion these experiments however do not prove that "axonal Rtn-1 is indeed promoting the severing of microtubules by spastin", but simply that the blocking spastin activity prevents the appearance of the microtubular phenotype (which appears still with a mysterious mechanism). What happens if they try to stabilize the cytoskeleton by another mean (with taxol for example?). The authors should rephrase this conclusion.

__R: __We completely agree with the reviewer's appreciation. We now explicitly indicate in the main text that this is (so far in the manuscript) a still correlative phenomenon that suggests an interplay with Spastin activity "..Together, these results suggest that locally synthesized Rtn-1 normally acts to suppress the outgrowth of injured axons, a process that could involve the microtubule-severing activity of Spastin." (lines 321-323). Later in the article, with the improved Figure 7, we further propose that these findings may reflect a causal relationship, although this mechanism has not yet been directly demonstrated in axons.

4) The last experiment (Figure 7) that aims to connect Rtn-1 and spastin function is very artificial, since it is based on overexpression. Why should spastin M87 interact with an ER morphogen? Endogenously it is conceivable that spastin M1 which localizes to the ER would interact with Rtn-1. Moreover, this experiment needs further controls and quantifications. First, it is quite obvious from panel 7C that there is crossover of signal in the two fluorescence channels (see GFP and spastin). Controls need to be shown, where only one of the two fluorescent proteins is expressed, and the specificity of the laser is tested. This experiment is based on only 1 cell shown where co-localisation is detected based on a line that is placed in a specific area of the cell. The effects on the microtubular network needs quantification.

__R: __We have now improved Figure 7 and added the requested controls to rule out crosstalk as indicated in Supplementary Figure 5 and in the main text. We agree that under normal conditions GFP should display a diffuse cytoplasmic distribution. However, in our experimental setup, we observed punctate GFP signals only in the context of co-expression with Spastin-RFP. This is consistent with prior reports showing that soluble GFP can occasionally be sequestered into late endosomal structures (Sahu et al., 2011), which are also known to harbor the M87 Spastin isoform (Allison et al., 2013; Allison et al., 2019). To exclude the possibility of unspecific fluorescence crosstalk, we independently acquired each fluorophore channel and confirmed that GFP puncta were genuine and not due to bleed-through (Supplementary Figure 5). Further, cells expressing only GFP or only Spastin-RFP did not show overlapping puncta (arrowheads), and the co-expression of GFP with Rtn-1A-RFP did not produce any apparent overlap, indicating that the punctate pattern of GFP is specifically associated with Spastin co-expression. Thus, we consider that the observed GFP colocalization with Spastin potentially reflects a true phenomenon and not an artifact of imaging or fluorophore bleed-through.

We thank for these observations and apologize for the confusion in the outline of the former figure 7 and the lack of a better description. As the reviewer indicates, one interesting aspect of the M87 isoform is that lacks the ER morphogen domain (so is soluble or cytoplasmic in principle). However, it also harbors endosome and microtubule binding domains which according to previous literature (now included in the main text) may render it a punctate rather than a homogeneous pattern. Also, M87 is the most abundant isoform in the nervous system, particularly at early development. This is the reason why we selected this isoform to test our model. To clarify this point, we based our colocalization analysis in different cells and experimental dates and analyzed all the z-stacks for each cell (see new figure 7B and methods), the intensity plots (now removed) were only for graphical purposes. Similarly, we had already quantified the total tubulin intensity in COS cells based on many cells from different dates and included the sum projections of all the z-stacks from these cells (see new figure 7C). Thus, we removed the intensity profiles as they were clearly misleading (see new figure 7).

We agree that over-expressing constructs may force interactions or co-distribution of proteins. However, in this case, if the observed results were mainly due to over-expression, we should see a similar trend with isoform A as both constructs are under the control of the same strong promoter (CMV) and harbor the same ER morphogen domain (RHD). Nevertheless, the distribution of M87 tightly mirrors Rtn-1C, which is not the case for Rtn-1A. Only as a theoretical prediction, our molecular modeling suggests that Rtn-1C may be associated with Spastin through its microtubule binding domain (Figure 7E). This would suppose that Spastin "decorates" ER-tubules rather than being in the same ER membranous structure. This discrete pattern of Spastin is more coherent with the distribution of both proteins that is now more clearly observed in distal axons by STED super-resolution (new figure 5A). So, despite a bit unexpected, these results suggest a novel interaction mechanism between these two proteins that deserves further validation.

5) What is exactly the model proposed? The title implies that axonal synthesis of Rtn-1 is important during injury, but the data in the paper rather suggest that upon injury the majority of Rtn-1 is not locally synthesized. If the levels of Rtn-1 do not change, why the effect on the microtubules should be specific? Why would a siRNA against Rtn-1 in axons not affect the levels of Rtn-1, but those of tubulin? The authors should be careful, and test other control siRNAs, and Rtn-1 siRNAs, since it is well known even in more simple cellular systems that the toxicity of individual siRNAs can vary greatly.

We consider the possibility that after injury there is no axonal Rtn-1 synthesis as a plausible and relevant appreciation. Unfortunately, we could not perform a puro-PLA experiment after injury, which would have provided a more definite answer. However, now we are more confident of regulating Rtn-1 synthesis before injury as supported by a Supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD. Thus, based on some similar phenotypes before and after injury, we consider our results are still compatible with Rtn-1 axonal synthesis being downregulated, but not fully absent (the mRNA is still detected, as described by Taylor 2009). As such, axonal Rtn-1 KD decreased β3-tubulin levels before and after injury according to figure 5B and the improved statistical analysis performed on figure 2E. Similarly, axonal Rtn-1KD significantly increases microtubule growth rate before and after injury according to the current statistical comparisons (Figure 5E). in complement, if β3-tubulin decrease was merely due to unspecific siRNA targeting, it is unlikely that SPTZ treatment should restore β3-tubulin only in the context of axonal Rtn-1 KD (Figure 5B). Although on a different track, the mechanistic relationship between Rtn-1C and Spastin suggested in Figure 7 could make more plausible that a similar phenomenon regarding the control of tubulin levels could be occurring locally in axons. We have now included these considerations in the discussion (lines 535-543).

To discard off-targets effects, we have now validated a third siRNA sequence (siRNA 3) specifically designed against Rtn-1 and showed that it selectively downregulates Rtn-1C but not β3-tubulin in cultured cortical neurons. Then, following the same experimental frame of figure 3, we performed axonal Rtn-1 KD after injury and observed that siRNA 3 also significantly increases the outgrowth of injured axons (Supplementary figure 2). This suggests that, at least this phenotype, is not product of an off-target effect. Thus, the pharmacological rescue of β3-tubulin levels by SPTZ (Figure 5B) and the Rtn-1C/Spastin co-distribution in heterologous cells, which correlates with preserved microtubules (improved Figure 7), provide converging evidence to suggest that Rtn-1C-Spastin interplay may underly the observed phenotypes in axons.

Minor comments:

In Figure 5A, it would be helpful to indicate the border of the axon. The figure is not really convincing.

Following yours and other reviewer comments, we have analyzed a new set of experiments regarding the STED images of non-injured and injured axons. To eliminate the risk of artifactual descriptions, we have avoided deconvolution and worked directly with raw STED images (Figure 5A). Under these conditions, distribution of Spastin and its intensity in distal axons are not modified by injury, nor those of Rtn-1C and Spastin (Supplementary figure 4). Despite these results, data still supports that both proteins are restricted to similar domains subcellular domains before and after injury.

Reviewer #3 (Significance (Required)):

The manuscript uses complex methods to address an interesting cell biological question of relevance to understand axonal growth regulation upon injury. A limitation of the study is the statistical analysis, which triggers some doubts about the reproducibility of the data. Further experiments and the addition of controls would be important to support the claims of the authors.

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Referee #3

Evidence, reproducibility and clarity

This manuscript investigates the relationship between the endoplasmic reticulum morphogen reticulon-1 (Rtn-1) and the microtubule severing protein spastin in axons after injury. The main message and conclusion of the paper is that local axonal synthesis of Rtn-1 plays a role in regulating the microtubule severing activity of spastin by interacting with spastin and inhibiting its activity. This mechanism would be important after injury by regulating axonal growth.

The conclusions of the paper are based on the following claims:

1. Rtn-1 is synthesized locally in axons.
2. Specific downregulation in Rtn-1 in axons using microfluidic chambers affects microtubules abundance (measured by beta-3 tubulin) and promotes axon growth after injury.
3. Inhibition of spastin MT-severing activity with a specific drug rescues the growth effect induced by axonal downregulation of Rtn-1.
4. Rtn-1c interacts with spastin-M87 to limit its MT-severing activity in a cellular system upon overexpression.

Major comments:

1. Evidence that Rtn-1 is synthesized in axons comes from two experiments. Initially, the authors show that Rtn-1 siRNA transfection in the axonal compartment of microfluidic chambers reduces Rtn-1 levels in axons, suggesting that there is some local synthesis. Although this method is very attractive, I am concerned about the statistical analysis. The graphs show bars rather than individual data points from the average of a large number of neurons (about 300). The plots also show the SEM instead of the SD, thus covering all the variability that is inherent in this type of experiment. The statistics are probably not performed on the 3 biological replicates, but consider the individual neurons as N. This is obviously not correct, since neurons in an experiment may all be affected by the same technical problem and are not independent replicates. For this reason, I am a bit skeptical about this quantification. Another problem is that the quantification of the fluorescence intensity of the sample does not take the nuclei into account. Are the nuclei removed for analysis? Are the images single planes? Addressing the quantification issues is crucial also for data in Figure 4, where the authors show a different effect of Rtn-1 axonal KD after injury. The second experiment is the Puro-PLA in Figure 6D. This experiment shows an average of 1.5 dots of signal per soma, which is a very low level of translation for this compartment where most of the synthesis should be taking place. In the axons, it is not clear how they calculate the axonal area. Again, the number of dots detected is very low and the physiological significance is questionable. A control with a known mRNA translated in axons would be important. Finally, as an important control, the authors should show the presence of Rtn-1 mRNA by FISH in their experimental system.
2. The effects on tubulin following Rtn-1 downregulation in axons is potentially very interesting, but the authors should be careful because it could also mean that the axons are suffering. Can they also stain for other cytoskeletal markers?
3. The results using SPTZ are very interesting and implicate spastin microtubule severing activity in the observed phenotype. In my opinion these experiments however do not prove that "axonal Rtn-1 is indeed promoting the severing of microtubules by spastin", but simply that the blocking spastin activity prevents the appearance of the microtubular phenotype (which appears still with a mysterious mechanism). What happens if they try to stabilize the cytoskeleton by another mean (with taxol for example?). The authors should rephrase this conclusion.
4. The last experiment (Figure 7) that aims to connect Rtn-1 and spastin function is very artificial, since it is based on overexpression. Why should spastin M87 interact with an ER morphogen? Endogenously it is conceivable that spastin M1 which localizes to the ER would interact with Rtn-1. Moreover, this experiment needs further controls and quantifications. First, it is quite obvious from panel 7C that there is crossover of signal in the two fluorescence channels (see GFP and spastin). Controls need to be shown, where only one of the two fluorescent proteins is expressed and the specificity of the laser is tested. This experiment is based on only 1 cell shown where co-localisation is detected based on a line that is placed in a specific area of the cell. The effects on the microtubular network needs quantification.
5. What is exactly the model proposed? The title implies that axonal synthesis of Rtn-1 is important during injury, but the data in the paper rather suggest that upon injury the majority of Rtn-1 is not locally synthesized. If the levels of Rtn-1 do not change, why the effect on the microtubules should be specific? Why would a siRNA against Rtn-1 in axons not affect the levels of Rtn-1, but those of tubulin? The authors should be careful, and test other control siRNAs, and Rtn-1 siRNAs, since it is well known even in more simple cellular systems that the toxicity of individual siRNAs can vary greatly.

Minor comments:

In Figure 5A, it would be helpful to indicate the border of the axon. The figure is not really convincing.

Significance

The manuscript uses complex methods to address an interesting cell biological question of relevance to understand axonal growth regulation upon injury. A limitation of the study is the statistical analysis, which triggers some doubts about the reproducibility of the data. Further experiments and the addition of controls would be important to support the claims of the authors.

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Referee #2

Evidence, reproducibility and clarity

Axonal mRNA localization and localized translation supports many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

Major concerns:

1. In figure 1, the authors provide an analysis of overlapping axonal mRNAs. There are more axonal transcriptome studies and a recent study by von Kugelgen and Chekulaeva (2020; doi: 10.1002/wrna.1590) already performed such an analysis, which included more studies. It would be good to mention this. It can be perceived that studies were now chosen to get the outcome that Rtn-1 is present in all studies. For example, von Kugelgen finds mRNA coding for RTN3, another ER structural protein, as present in 16 out of 20 studies analyzed. That said, the authors present more reasons to look at Rtn-1, so the selection to continue with this protein remains valid but can be written up differently so not to present it as the 'sole' ER-shaping protein consistently present in axonal transcriptomes.
2. The description of methods is currently insufficient and incomplete and does not allow for reproducibility of this study. For example, different Rtn-1 antibodies seem to be used in this study. Is the same antibody used for staining and WB? There is no listing of any of the antibodies used in the study and which one is used for which technique/experiment. This should be clarified and should be easy to do so in the methods section (antibody name, origin/company, dilution used) to enhance reproducibility of this study. This is not limited to primary antibodies and any information on secondary antibodies, including what was used for STED is completely missing.
3. The timeline of KD experiments in Figure 2 and 3 are unclear. For the Western blot KD is performed at DIV7 and collected 48 hours later. However, this is not specified for the stainings done in Figure 2C-E. Is this also at DIV7 and then for 48 hours? In figure 3 the siRNA is added at DIV8 (together with axotomy) and outgrowth is measured 24 hours later. Is 24 hours sufficient to achieve knockdown? Is this also what was done for stainings? Later on in Figure 5B, 48 hours of KD is again used. It is unclear what the rationale of these differing timepoints is. Why was this chosen? Is the timeline also the reason for the difference in segment lengths chosen? In Figure 3, there is a significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5.
4. Could the authors provide a rescue condition for their siRNA (using a siRNA-resistant construct) to show that their siRNA is specific for RTN1. They nicely show the efficiency of the siRNA but not its specificity. This is crucial because if not specific, this will affect a large part of their study. They already have RTN1A and RTN1C constructs available. Such a rescue experiment should ideally also be performed for one or more of their phenotypic experiments, such as the one presented in Figure 3A or 5 to show that the phenotype is really RTN1 dependent. If done by re-expressing either RTN1A or RTN1C, this could provide insightful information on the relevant isoforms.
5. I find the data presented in Figure 4A/B confusing. Axonal RTN-1 KD does not reduce axonal RTN1 levels but somatic KD does. I understand that this implies most protein comes from the soma and the authors indeed present an explanation that increased somatic RTN1 occurs after axonal KD as a compensation mechanism. However, this can also be interpreted that there is no axonal synthesis of RTN1 after injury and axonal KD has indirect or even aspecific effects. Their model depends on this difference. Their data in Figure 6 could provide supporting evidence if it shows RTN1 puro-PLA after injury. Along these same lines, in Figure 6, they nicely include a compartment control for puro-PLA. It therefore seems doable to include a somatic puromycin control for their axonal puro-PLA, to exclude and diffusion/transport of the newly synthesized peptides. This is especially in light of two recent papers reporting on this possible phenomenon, although these studies were not performed in neurons.
6. In Figure 5A the authors find an increased co-localization (RTN1/Spastin) after axotomy. From their images, it seems that the amount of Spastin is hugely increased, which would by default increase the chance of (random) colocalization of RTN1 on Spastin. Could the authors comment on this?
7. In figure 5E and 5F, the condition of scr + SPTZ is omitted. What is the reason for this? The explanation of results in these figures is confusing. The authors report a 'clear trend' in increase in comet track length and lifetime upon addition of SPTZ to axonal RTN-1 KD. This is however not significant. The comparisons that are made afterwards are confusing (e.g. increase in comet lifetime of SPTZ in non-injured axons with RTN1 KD compared to Scr+DMSO and KD + DMSO in injured axons). Their conclusion is axonal RTN-1 synthesis in injured axons (see my concern in the points above on this) governs microtubules growth rate beyond Spastin activity yet blocking Spastin activity still completely blocks the effect of KD on outgrowth.

Other/minor concerns:

• The gene ontology analysis in Figure 1A contains the category 'Endoplasmic reticulum'. In this category are mainly ribosomal proteins. Although in a gene ontology analysis these proteins will be included in this category, it is misleading in this respect since they are just as likely to be coming from cytoplasmic ribosomes. Although it cannot be excluded that these are ER-bound ribosomes, not in the last place because a recent study (Koppers et al., 2024, doi: 10.1016/j.devcel.2024.05.005) found ribosomes attached to the ER in axons, I believe the category should be adapted or at the least clarified in the text.
• Is RTN-1C isoform still an ER-shaping protein or rather an ER protein with alternative functions? The final sentence in the abstract makes a statement that a locally synthesized ER-shaping protein lessens microtubule dynamics. Could the authors provide a clearer description and discussion of the evidence in literature for this? RTN1C has been suggested to perform alternative functions in which case the statement that the local synthesis of an ER-shaping protein is important for axonal outgrowth should be adapted.
• Is there a difference in RTN1 distribution or levels pre- and post-axotomy?
• Line 100/101 states 'the interactome of the axonal ER provides...'. To my knowledge there has been no study looking at the interactome of the axonal ER specifically. Surely axonal ER proteins are known but there is a difference.
• Typo line 160 'localla'
• In Figure S1 B, please add the DIVs to make it more clear what each graph corresponds to. The legend of S1B states different distances from the cell body but the graph shows distances from the tip.
• Figure 2C, why does B3 tubulin decrease in soma, aspecific effect of siRNA?
• What is the rationale on the opposite effect found in outgrowth in Figure 3?
• Missing word 'we' on line 194
• Typo line 629 'witmn h', please proofread the entire manuscript carefully.
• Could the authors comment on why, in Figure 7B/C, GFP only is colocalizing with Spastin-RFP? In general, GFP should be diffusive and not display punctate colocalization with Spastin.

Significance

Axonal mRNA localization and localized translation supports many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

The audience for this study will be mainly basic research in the fields of both axonal protein synthesis and axon regeneration. My expertise is in the field of mRNA localization and local protein synthesis.

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Referee #1

Evidence, reproducibility and clarity

In this paper, the authors focus on the role of Reticulon-1C in concert with Spastin in response to axonal injury. In data mining, they find axonal mRNAs encoding for ER-associated proteins including Rtn-1. They establish a knockdown targeting both Rtn-1 isoforms Rtn-1A and Rtn-1C. They observe decreased beta-3-Tubulin levels in the soma while axonal protein levels are unchanged. In microfluidic devices, they characterise the effect of a compartment-specific Rtn-1 KD on axonal outgrowth in the axonal compartment. The authors quantify axonal outgrowth, seeing increased outgrowth in an axonal compartment-specific Rtn-1 KD, while the effect seems to be reversed when applying the KD construct in the somatic compartment. When focussing on the axonal growth cone, they find the Rtn-1 KD shows differences in several morphological features of the growth cone. They find an increase in Tubulin levels in an axonal compartment-specific, but a decrease in a somatic compartment-specific Rtn-1 KD. Colocalisation of Rtn-1C and Spastin is shown to be monolaterally increased following axotomy. Combining axotomy with the Rtn-1 KD shows increases in dynamic microtubule growth rates and track lengths. In another model system, neuron balls, they show Rtn1-C, but not Rtn1-A to be present in the axon. In a puro-PL assay they also show it can be synthesised in the axonal compartment. To investigate the mechanism enabling the cooperation between Spastin and Rtn-1C, they move to a cell line model in which they see a correlating distribution between Spastin and Rtn-1C but not Rtn-1A. Finally, they use in silico modelling to speculate on binding between Spastin domains and Rtn-1 isoforms.

Major comment:

The rationale behind the work is convincing, however some interpretations are presented as more robust than some data allow. Most notably, while the interaction between Rtn-1 and Spastin has been shown prior to this study, it is only presented here through in silico analysis. In figure 5, an increase in the growth rate of dynamic microtubules is observed in either a Rtn-1C KD or by using a Spastin-inhibitor. Due to a described increase in colocalisation between Rtn-1C and Spastin (5A), the increase in growth rate is displayed as caused by Rtn-1 promoting Spastin's severing ability. This result might however be correlative. Further in the injured samples, Spastin-levels seemingly increase (in the representative images) and it is thus not surprising that the level of Rtn-1C colocalising with Spastin increases as well. This might not be indicative of a cooperation and further experimental evidence are required.

Other comments:

• Generally, graphs would benefit from individual values plotted as well as the summary. Font sizes and types (but rarely) are sometimes inconsistent. Proteins should be consistently written (capitalised or not).
• Table 1 and figure 1 present data collected from a vast amount of resources. It should be highlighted that datasets from which data was obtained includes many different models, different DIVs and neuronal cell types. Figure 1B may benefit from a different colour scheme. "Ex-vivo" should be "Ex vivo". For "ER mRNAs are a relevant category" it is not described what "relevant" would mean in this context. The title might remove this small part or describe it in the text. It should be described how it is decided that mRNAs are "common".
• Figure 2: add description to y-axis to describe what fold change is displayed, applies to multiple figures. Will improve readability of the figures. In 2C, the ROI showing neuronal somata should be increased to show part of the axon and not cut off the soma.
• Figure 3: Three out of four axonal compartments seem to be comprised of dying or damaged axons. Especially the axonal KD scrambled image. It should be ensured that neuronal cultures are healthy. Typo in "intersections". The schematic of 3B is a great addition to explain the graphs above. Perhaps it could be a bit refined as it is currently hard to see whether this is a neuron or a growth cone without context. Maybe show where the axon connects to the depicted growth cones and change the third icon which looks like it was crossed out. Small formatting issues: remove additional space bar before "Figure 3." And add after "Bar"
• Figure 4: If not misunderstanding what is depicted, in 4A and B, different lookup tables are used to depict the same signal. Only one of each images is necessary. Do the axons have more tiny branches in the Rtn-1 KD condition in 4A? Unclear why Rtn-1 levels are increased in the Rtn-1 KD (4C), please clarify.
• Figure 5: It may be easier to understand what "axotomy" samples are if just referred to as "injured" as later in the same figure. The procedure could also very briefly be explained in the results. 5C should depict AUC in µm2 not µm. 5D Spastin is barely visible, brightness and contrast should be adjusted to enhance visibility.
• Figure 6: It should be made clear why it is necessary to switch to another model system just for 6A, please indicate this in the text. PCR bands seem very pixelated, check the quality. It is unclear why soma genes/proteins were only tested with either PCR or WB others with both. Rtn-1C and Rtn1-A should be presented in the same order in the PCR and WB panel. Correct "Rtn1-1A" typo. In 6D, 1.5 dots per soma seems like a low number. When normalised to the area the soma vs the axon occupies, the compartmentalisation does not work? May be it make sense to refine analysis or apply puromycin in the somatic compartment and analyse the axonal compartment as comparison?
• Figure 7: 7A shows two images depicting the same information that may not be needed. Can probably be removed. In 7B there is no negative (or any) correlation between Spastin levels and Tubulin, however later it is mentioned that Rtn-1C transports Spastin thus causing a decrease in Tubulin at certain locations? It is nclear if Spastin levels vary intensely between different samples. Mean intensity of the somatic area may be beneficial to rule this out. 7B Tubulin on the right top panel seems to have a decrease in Tubulin levels which is not visible due to the Y axis of Tubulin being set to a different range than the middle and lower panel. The average of line scans from multiple cells may be helpful to determine whether there is indeed no colocalization between Rtn-1A and Spastin. The provided representative images seem to show similar degrees of colocalization between Spastin and Rtn-1A/C.

Results:

• It would be helpful to reiterate the hypothesis at the start to ease the reading flow.
• There seems to be minor redundancy in lines 132-138.
• There are several spellings, proof-reading is recommended. For example, in line 136 should be "promotes". 160 "localla", 192 should be "the actin cytoskeleton".,194 should be "we first examined", 195 should be "Different", 223 "using", 259 "axons". ...
• 154-155: Unclear, why the lower MW Rtn-1C was seen as more important.
• 167 results of 2E not stated before interpreting them.
• 181 would suggest "outline" instead of "perimeter".
• 183-184 "longest shortest path" is a confusing term.
• figure 4B should be referenced earlier in the sentence.
• 243-244 may be correlation. Rtn-1 and Spastin do not necessarily interact so that this result is achieved.
• 246: In figure 1 the KD seemed to have an effect on both Rtn-1 isoforms, why not here anymore? 259 "axons". 284 "counteract" instead of "suppress"?
• 485: rephrase as the interaction between Rtn-1C with Spastin has not been shown directly in these experiments.

Methods: 535 "in PBS". 543 citation error. 689-699 is it necessary to add a gaussian blur?

References: Mannan, A U et al. appears twice in the citation list (36 and 44).

Significance

Overall, this manuscript describes novel fundings which will be interesting to the neuronal cell biology community and scientists working on the field of neuronal injury and regeneration. It is well structured, and the data are mostly well presented but sometimes conclusions are over-interpreted. However, several points need to be addressed in a more convincing way.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

This manuscript described the translational responses to single and combined BCAA shortages in mouse cell lines. Using Ribo-seq and RNA-seq analysis, the authors found selective ribosome pausing at codons that encode the depleted amino acids, where the pausing at valine codons was prominent at both a single and triple starvations whereas isoleucine codons showed pausing only under a single depletion. They analyzed the mechanisms of the unexpected selective pausing and proposed that the positional codon usage bias could shape the ribosome stalling and tRNA charging patterns across different amino acids. They also examined the stress responses and the changes in the protein expression levels under BCAA starvation.

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

We thank the reviewer for the thoughtful and positive evaluation of our work.

Major comments

1. The abstract may need to be revised since it is hard to immediately catch the authors' main point. If the authors regard this work as a resource paper, the current version is fine. But it could be better to point out the positional codon usages the authors found, which is a strong point of the current manuscript.

Response: We thank the reviewer for highlighting the importance of positional codon usage, which indeed represents a key finding of our study. We revised the abstract, and we now emphasize this aspect more clearly. However, in response to review #2, we have framed the observed positional effects and the idea of an elongation bottleneck as one possible contributing mechanism among others and relate it specifically to the attenuation of isoleucine-specific stalling under triple starvation.

1. Page 18 "Beyond these tRNA dynamics, our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress." This idea is interesting. To what extent the authors think this could be generalized? The authors may discuss whether they think their proposed model is specific to the different ribosome stalling patterns between valine and isoleucine codons or generalized to other codon combinations. For example, the positional codon usage bias will be different among different organisms, and are there any previous reports on ribosome behaviors that align with their model?

Response: We thank the reviewer for raising these important points. While our study primarily focuses on the differential stalling patterns of valine and isoleucine codons, we believe the underlying principle, that the position of codons within the CDS can modulate the extent of ribosome stalling, may under very specific circumstances extend beyond this amino acid pair. We expect this positional effect to be potentially relevant for combinations in which one amino acid has considerable enrichment near the 5′ end of coding sequences, coupled with starvation-sensitive tRNA isoacceptors, while the other does not. In our case, valine meets these criteria (see Fig. S11A and Fig. 6). In contrast, isoleucine and leucine codons, although also relatively frequent, show more variable positional distributions and are both decoded by isoacceptors that appear more resistant to starvation, as illustrated in Fig. 6 and reported for mammals and bacteria in Saikia et al. 2016; Darnell, Subramaniam, and O’Shea 2018; Elf et al. 2003; Dittmar et al. 2005. To explore the generalizability of this model, we have now included a transcriptome-wide analysis of codon position biases in mouse for all codons in the revised manuscript (Supplementary Figures 10 and 11). This analysis may serve as a basis to identify additional candidate codons for future studies. Furthermore, we now mention in the Discussion that amino acids with similar properties to valine regarding their positional distribution and tRNA isoacceptors, such as phenylalanine, and glutamine, whose tRNA isoacceptors are predicted to be fully deacylated under their respective starvation in bacteria (Elf et al. 2003), could be promising candidates for testing this model, in combination with amino acids, whose tRNAs are expected to remain partially charged under starvation or to be depleted at the start of the CDS such as i.e. His (Supplementary Fig.11C).

Even if the authors think this model can be applied to BCAA starvation, would it be possible to explain the different isoleucine codon responses between single and double starvation? The authors may discuss why the ribosome stalling at isoleucine AUU and AUC codons was slightly attenuated under double starvation. And how about the different leucine codon responses among single, double, and triple starvations, although the pausing is not as strong as isoleucine and valine codons?

Response: Regarding the attenuated isoleucine stalling under double starvation, we believe this is primarily due to stronger inhibition of the mTORC1 pathway when leucine is co-depleted (i.e., in the double starvation condition; Fig. 2D–F). This results in a more substantial suppression of global translation, reducing overall tRNA demand and thereby mitigating stalling (Darnell, 2018). A similar effect may explain the only mild leucine codon stalling observed under single leucine starvation, which also triggers strong mTORC1 inhibition and reduced initiation. In contrast, triple starvation does not suppress mTORC1 to the same extent, and thus reduced initiation alone cannot explain the absence of leucine codon stalling. Instead, we propose that additional features, such as the relative sensitivity of tRNA isoacceptors to starvation and their aminoacylation dynamics, must be considered. Valine tRNAs, for example, are known to be highly sensitive and become strongly deacylated under starvation in bacteria (Elf et al. 2003), a pattern that we also find in our own data (Fig. 6). Leucine tRNAs, by contrast, appear more resistant, possibly due to better amino acid recycling or isoacceptor-specific differences in charging kinetics, though further validation would be needed. However, combined with the strong stalling at 5′-enriched valine codons, this could reduce downstream ribosome traffic and limit exposure of leucine codons, thus preventing stalling. However, our new analysis of the positional relationship between valine and leucine codons within individual transcripts (now shown in Supplementary Figure 11B) did not reveal as strong a pattern as we observed for valine and isoleucine codons. We now discuss these points and their implications in the revised Discussion.

Experimental validation using artificial reporters carrying biased sequences may also be considered.

Response: We appreciate the reviewer’s suggestion. In fact, we explored this experimentally using a dual-fluorescent reporter system (GFP–RFP) (Juszkiewicz and Hegde 2017) containing consecutive Val or Ile codons. However, the constructs yielded variable and non-reproducible results under starvation conditions. In addition, testing the role of codon position would require placing the same codons at multiple defined positions within a single transcript and performing ribosome profiling directly on the reporter. This type of targeted experimental validation is technically challenging and falls beyond the scope of the current study. We now mention this explicitly in the revised Discussion as an interesting direction for future work.

1. Page 13 "Moreover, we noticed that DT changes extend beyond the ribosomal A-site, including the P-site, E-site, and even further positions (Supplementary Fig. 2A), consistent with other studies on single amino acid starvation 39 (Supplementary Fig. 2B-C)." Could the widespread DT changes be due to Ribo-DT pipeline they used or difficulties in offset determination? Indeed the authors showed that this feature was found in other datasets, but it seems that the datasets were processed and analyzed in the same way as their data. The original Ribo-DT paper (Gobet and Naef, 2022, Methods) also showed some widespread DT changes even from RNA-seq. Another analysis method like the codon subsequence abundant shift as a part of diricore analysis (Loayza-Puch et al., 2016, Nature) did not show that broad changed regions. The authors are encouraged to re-analyze the data sets using different methods.

Response: We agree with the reviewer that the fact that DT changes beyond the ribosomal A-site is puzzling, but this has already been seen in other papers using other approaches (Darnell, Subramaniam, and O’Shea 2018). To validate that this shift is not due to our A-site assignment, enrichment analysis, or DT method, we applied the Diricore pipeline to our Ribo-Seq data. The output of the pipeline provides either 5’-end ribosome density or “subsequence” analysis using an A-site offset for each read size based on the metagene profile at the start codon. Both analyses show the same enriched codons across the different conditions as in our analyses, and the broad shift is similar, with the maximum signal at E, -1 position (Fig. R1).

1. Page 13 "Intriguingly, only two of the three isoleucine codons (AUU and AUC) showed increased DTs upon Ile starvation (p < 0.01), while just one leucine codon (CUU) exhibited a modest but significant DT increase (p < 0.01) under Leu starvation (Figure 1A-B, Supplementary Figure 2A)." How can the authors explain the different strengths of ribosome pausing at Ile codons under Ile and double starvation? The AUA codon did not show any pausing under either of the starvation conditions. Throughout the manuscript, the authors mainly describe the difference between amino acids but it is desirable to discuss the codon-level difference as well.

Response: Thank you for raising this point. The observed differences in stalling between the isoleucine codons can likely be explained by differences in tRNA isoacceptor charging and positional bias within transcripts. The AUA codon is decoded by a distinct tRNAIle isoacceptor (tRNAIleUAU), which, according to our tRNA charging data (Fig. 6), remains largely charged during Ile starvation. This observation aligns with previous reports suggesting that this isoacceptor is more resistant to starvation-induced deacylation in mammalian cells and bacteria (Saikia et al. 2016; Elf et al. 2003). In contrast, the AUU and AUC codons are primarily decoded by the tRNAIleAAU isoacceptor, which we find to be strongly deacylated under Ile starvation, likely contributing to the observed codon-specific ribosome pausing. Additionally, we found that the AUA codons are relatively rare in general and particularly underrepresented near the 5′ ends of coding sequences. Our new spatial analysis (now included in Supplementary Figure 11B) confirms that AUA codons tend to occur downstream of AUU and AUC codons within transcripts. This potentially further reduces stalling on these codons and further diminishes their apparent DT increase under starvation. In order to better explain these important points, we have now expanded the codon-level discussion of these differences in the revised manuscript.

1. Page 13 "We examined the effects of single amino acid starvations (-Leu, -Ile and -Val), as well as combinations, including a double starvation of leucine and isoleucine (hereafter referred to as "double") and a starvation of leucine, isoleucine, and valine ("triple"), allowing us to identify potential non-additive effects." The different double starvations, isoleucine and valine, and leucine and valine, will further support their hypothesis on the effects of the positional codon usage bias on ribosome pausing and tRNA charging patterns. Although this could be beyond the scope of the current manuscript, the authors are encouraged to provide a rationale for the chosen combination.

Response: Our experimental design evolved stepwise: we initially focused on leucine and isoleucine depletion as we found that despite their structure similarity these had respectively short and long dwell times in our previous work in the mouse liver (Gobet et al. 2020). Valine was included at a later stage to cover all the BCAAs. At the time, we did not anticipate valine to yield particularly striking effects in cells, and therefore we did not include systematic pairwise depletions involving valine. However, the strong and unexpected stalling observed at valine codons, especially under triple starvation, became a central aspect of the study. Thus, we agree that additional combinations, such as Leu/Val or Val/Ile, could be informative and now mention this in the Discussion as a potential direction for future studies.

Minor comments

Page 16 "these results imply that BCAA deprivation lowers protein output through multiple pathways: a combination of reduced initiation, direct elongation blocks (stalling), and possibly an increased proteolysis" This conclusion is totally right but may be too general. Could the authors summarize BCAA-specific features of the events including reduced initiation, stalling, and proteolysis that all contribute to protein outputs? This is not well discussed in the latter sections including Discussion.

Response: We thank the reviewer for this helpful suggestion. We agree that the original statement was too general and have revised the relevant section to more clearly delineate the distinct responses observed under each BCAA starvation condition. Specifically, we now summarize that valine starvation is characterized by strong, positionally biased ribosome stalling; leucine starvation primarily impacts translation initiation, likely via mTORC1 repression; and isoleucine starvation shows a mixed phenotype, with features of both impaired initiation and codon-specific elongation delays. We also clarify that while protein stability or degradation may contribute to the observed changes in protein output, our current data do not allow for quantitative assessment of proteolytic effects (e.g., changes in protein half-life). Therefore, we refrain from making direct quantitative conclusions about the differential modulations of proteolysis and instead focus our discussion on the translational mechanisms supported by our data.

Reviewer #1 (Significance):

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

We thank the reviewer for the encouraging comments and share the view that positional codon-usage bias is an important result; accordingly, we now underscore this point explicitly in the revised Abstract. We also emphasise that our other observations are, to our knowledge, novel: only a handful of multi-omics studies have combined ribosome-pausing profiles with direct tRNA-aminoacylation measurements, and none has systematically examined multiple amino-acid-deprivation conditions as presented here.

Reviewer #2 (Evidence, reproducibility and clarity):

This study examines the consequences of starvation for the BRCAAs, either singly, for Leu & Ile, or for all three simultaneously in HeLa cells on overall translation rates, decoding rates at each codon, and on ribosome density, protein expression, and distribution of ribosome stalling events across the CDS for each expressed gene. The single amino acid starvation regimes specifically reduce the cognate intracellular amino acid pool and lead to deacylation of at least a subset of the cognate tRNAs in a manner dependent on continuing protein synthesis. They also induce the ISR equally and decrease bulk protein synthesis equally in a manner that appears to occur largely at the initiation level for -Leu and -Val, judging by the decreased polysome:monsome ratio, but at both the initiation and elongation levels for -Ile-a distinction that remains unexplained. Only -Leu appears to down-regulate mTORC1 and TOP mRNA translation.There is a significant down-regulation of protein levels for 50-200 genes, which tend to be unstable in nutrient-replete cells, only a fraction of which are associated with reduced ribosome occupancies (RPFs measured by Ribo-Seq) on the corresponding mRNAs in the manner expected for reduced initiation, suggesting that delayed elongation is responsible for reduced protein levels for the remaining fraction of genes. All three single starvations lead to increased decoding times for a subset of the cognate "hungry" codons: CUU for -Leu, AUU and AUC for -Ile, and all of the Val codons, in a manner that is said to correspond largely to the particular tRNA isoacceptors that become deacylated, although this correspondence was not explained explicitly and might not be as simple as claimed. All three single starvations also evoke skewing of RPFs towards the 5' ends of many CDSs in a manner correlated with an enrichment within the early regions of the CDSs for one or more of the cognate codons that showed increased decoding times for -Ile (AUC codon) and -Val (GUU, GUC, and GUG), but not for -Leu-of which the latter was not accounted for. These last findings suggest that, at least for -Val and -Ile, delays in decoding N-terminal cognate codons cause elongating ribosomes to build-up early in the CDS. They go on to employ a peak calling algorithm to identify stalling sites in an unbiased way within the CDS, which are greatest in number for -Val, and find that Val codons are enriched in the A-sites (slightly) and adjacent 5' nucleotides (to a greater extent) for -Val starvation; and similarly for Ile codons in -Ile conditions, but not for -Leu starvation-again for unknown reasons. It's unclear why their called stalling sites have various other non-hungry codons present in the A sites with the cognate hungry codons being enriched further upstream, given that stalling should occur with the "hungry" cognate codon in the A site. The proteins showing down-regulation are enriched for stalling sites only in the case of the -Val starvation in the manner expected if stalling is contributing to reduced translation of the corresponding mRNA. It's unclear why this enrichment apparently does not extend to -Ile starvation which shows comparable skewing of RPFs towards the 5'ends, and this fact diminishes the claim that pausing generally contributes to reduced translation for genes with abundant hungry codons. All of the same analyses were carried out for the Double -Ile/-Leu and Triple starvations and yield unexpected results, particularly for the triple starvation wherein decoding times are increased only at Val codons, skewing of RPFs towards the 5' ends of CDSs is correlated only with an enrichment for Val codons within the early regions of the CDSs, and stall sites are enriched only for Val codons at nearly upstream sites, all consistent with the finding that only Val tRNAs become deacylated in the Triple regime. To explain why only Val tRNA charging is reduced despite the observed effective starvation for all three amino acids, they note first that stalling at Val codons is skewed towards the 5'ends of CDS for both -Val and triple starvations more so than observed for Ile or -Leu starvation, which they attribute to a greater frequency of Val codons vs Ile codons in the 5' ends of CDSs. As such, charged Val tRNAs are said to be consumed in translating the 5'ends of CDSs and the resulting stalling prevents ribosomes from reaching downstream Ile and Leu codons at the same frequencies and thus prevents deacylation of the cognate Ile and Leu tRNAs. It's unclear whether this explanation is adequate to explain the complete lack of Ile or Leu tRNA deacylation observed even when amino acid recycling by the proteasome is inhibited-a treatment shown to exacerbate deacylation of cognate tRNAs in the single amino acid starvations and of Val tRNA in the triple starvation. As such, the statement in the Abstract "Notably, we could show that isoleucine starvation-specific stalling largely diminished under triple starvation, likely due to early elongation bottlenecks at valine codons" might be too strong and the word "possibly" would be preferred over "likely". It's also unclear why the proteins that are down-regulated in the triple starvation are not significantly enriched for stalling sites (Fig. 5B) given that the degree of skewing is comparable or greater than for -Val. This last point seems to undermine their conclusion in the Abstract that "that many proteins downregulated under BCAA deprivation harbor stalling sites, suggesting that compromised elongation contributes to decreased protein output." In the case of the double -Ile/-Leu starvation, a related phenomenon occurs wherein decoding rates are decreased for only the AUU Ile codon and only the AAU Ile tRNA becomes deacylated; although in this case increased RPFs in the 5' ends are not correlated with enrichment for Ile or Leu codons and, although not presented, apparently stall sites are not associated with the Ile codon in the double starvation. In addition, stalling sites are not enriched in the proteins down-regulated by the double starvation. Moreover, because Ile codons are not enriched in the 5'ends of CDS, it doesn't seem possible to explain the selective deacylation of the single Ile tRNA observed in the double starvation by the same "bottleneck" mechanism proposed to explain selective deacylation of only Val tRNAs during the triple starvation. This is another reason for questioning their "bottleneck" mechanism.

We thank the reviewer for their deep assessment, exhaustive reading, and constructive feedback, which have greatly contributed to improving the clarity and contextualization of our manuscript. We would first like to clarify that all experiments in this study were conducted in NIH3T3 mouse fibroblasts, not HeLa cells; we assume this was a misunderstanding and have verified that the correct cell line is consistently indicated throughout the manuscript. We also clarify that our data show that -Leu, double starvation, and to a lesser extent -Ile, downregulate mTORC1 signaling and TOP mRNA translation, whereas valine -Val and triple starvation had minimal effects on these pathways. We agree that some of our conclusions and observed phenomena were not explained in sufficient detail in the original version. To address this, we have significantly reworked the discussion, added complementary figures and clarified key points throughout the text, to better convey the underlying rationale and biological interpretation of our findings. We address each of the reviewer’s points in detail in the point-by-point responses below.

Specific comments (some of which were mentioned above):

-The authors have treated cells with CHX in the Ribo-Seq experiments, which has been shown to cause artifacts in determining the locations of ribosome stalling in vivo owing to continued elongation in the presence of CHX (https://doi.org/10.1371/journal.pgen.1005732 ). The authors should comment on whether this artifact could be influencing some of their findings, particular the results in Fig. 5C where the hungry codons are often present upstream of the A sites of called stalling sites in the manner expected if elongation continued slowly following stalling in the presence of CHX.

Response: We thank the reviewer for raising this important concern. We would like to clarify that our ribosome profiling protocol did not include CHX pretreatment of live cells. CHX was added only during the brief PBS washes immediately before lysis and in the lysis buffer itself. This approach aligns with best practices aimed at minimizing post-lysis ribosome run-off, and is intended to prevent the downstream ribosome displacement artifacts described by Hussmann et al. 2015, which result from pre-incubation of live cells with CHX for several minutes before harvesting. Furthermore, recent studies have demonstrated that CHX-induced biases are species-specific. For instance, Sharma et al. 2021 found that human (and mice) ribosomes are not susceptible to conformational restrictions by CHX, nor does CHX distort gene-level measurements of ribosome occupancy. This suggests that the use of CHX in the lysis buffer, as performed in our protocol, is unlikely to introduce significant artifacts in our ribosome profiling data. To further support this, we reanalyzed data from Darnell, Subramaniam, and O’Shea 2018, where the ribosome profiling samples were prepared without any CHX pretreatment or CHX in the wash buffer, and still observed similar upstream enrichments in their stalling profiles (see Supplementary Figure 2B-C in our manuscript). Additionally, in our previous work (Gobet et al. 2020), we compared ribosome dwell times with and without CHX in the lysis buffer and found no significant differences, reinforcing the notion that CHX use during lysis does not substantially affect the measurement of ribosome stalling. Given these considerations, we believe that CHX-related artifacts, such as downstream ribosome movement, are unlikely to explain the enrichment of hungry codons upstream of identified stalling sites in our data. We have now adjusted the Methods section to clarify this point.

-p. 12: "These starvation-specific DT and ribosome density modulations were also evident at the individual transcript level, as exemplified by Col1a1, Col1a2, Aars, and Mki67 which showed persistent Val-codon-specific ribosome density increases but lost Ile-codon-specific increases under triple starvation (Supplementary Figure 3A-D). " This conclusion is hard to visualize for any but Val codons. It would help to annotate the relevant peaks of interest for -Ile starvation with arrows.

Response: We agree and thank the reviewer for this observation. We have now annotated exemplary peaks in Supplementary Figure 3A–D to highlight ribosome pileups over Ile codons. However, we agree that it is still hard to visualize in the given Figure. Therefore, we added scatter plots for each of the transcripts that show the RPM of each position in the Ctrl vs starvation to allow for a better illustration of the milder effects upon Ile starvation (Supplementary Figure 4).

-To better make the point that codon-specific stalling under BCAA starvation appears to be not driven by codon usage, rather than the analysis in Fig. 1H, wouldn't it be better to examine the correlation between increases in DT under the single amino acid starvation conditions and the codon frequencies across all codons?

Response: We appreciate the suggestion. We have now added an additional analysis correlating the change in DT with codon usage frequency for each starvation condition. This is included in Supplementary Figure 5A-D and supports our interpretation that codon frequency alone does not explain the observed stalling behavior.

-p. 13, entire paragraph beginning with "Our RNA-seq and Ribo-seq revealed a general activation of stress response pathways across all starvations..." It is difficult to glean any important conclusions from this lengthy analysis, and the results do not appear to be connected to the overall topic of the study. If there are important conclusions here that relate to the major findings then these connections should be made or noted later in the Discussion. If not, perhaps the analysis should be largely relegated to the Supplemental material.

Response: We thank the reviewer for this comment. The paragraph in question is intended to provide a global overview of transcriptional and translational responses across the starvation conditions. It serves both as a quality control (e.g., PCA clustering and global shifts in RPF/RNA-seq profiles), and to confirm that expected starvation-induced responses are among the strongest detectable signals separating the starved samples from the control. Indeed, these observations establish that the perturbations are effective and that hallmark nutrient stress responses are globally engaged across conditions. Importantly, very few studies to date have examined transcriptional and translational responses under single or combined branched-chain amino acid (BCAA) starvation conditions. It therefore remains unclear to what extent BCAA depletion broadly remodels gene expression and translation. Our analysis contributes to addressing this gap, revealing that while certain stress pathways are commonly induced, others show condition-specific patterns such as we observed for -Ile starvation. To maintain focus, we have kept the detailed pathway analyses and transcript-level enrichments in the Supplement and rewritten the corresponding text in a more compact manner, reducing it by more than one third.

-p. 15: "Together, these findings highlight that BCAA starvation triggers a combination of effects on initiation and elongation, with varying dynamics by amino acid starvation." I take issue with this statement as it appears that translation is reduced primarily at the initiation step for all conditions except -Ile. As noted above, these data are never menitioned in the DISCUSSION as to why only -Ile would show a marked elongation component to the inhibition whereas -Val gives the greatest amount of ribosome stalling.

Response: We acknowledge the reviewer’s point. While the polysome profiles (Figure 3F-H) directly indicate that most conditions repress initiation, codon- and condition-specific elongation defects can still contribute to reduced protein output, even if they are not always detectable as global polysome shifts. Polysome profiles reflect the combined outcome of reduced initiation (which decreases polysome numbers) and ribosome stalling (which can, but does not always have to, increase ribosome density on individual transcripts, potentially counteracting the effects of reduced initiation). For valine starvation strong stalling occurs very early in the CDS (Figure 5F). This bottleneck restricts overall ribosome movement to downstream regions. Thus, while elongation is profoundly impaired, the total number of ribosomes per transcript (which polysome signals largely reflect) may appear low due to reduced overall ribosome traffic. In contrast, isoleucine codon stalling tends to occur also further downstream on the transcript (Figure 5F), allowing ribosomes to accumulate in larger numbers on the mRNA, leading to a clearer "elongation signature" in polysome profiles (Figure 3F, H). Additionally, we observed slightly higher inter-replicate variance for isoleucine starvation (Supplementary Figure 6B), which may have reduced the number of statistically significant stalling sites extracted compared to valine. We have revised the main text and discussion to clarify these points.

-I cannot decipher Fig. 4D and more detail is required to indicate the identity of each column of data.

Response: We thank the reviewer for pointing this out. Figure 4D (now Figure 4E) presents an UpSet plot, which is a scalable alternative to Venn diagrams commonly used to visualize intersections across multiple sets. Briefly, each bar in the upper plot represents the number of transcripts with increased 5′ ribosome coverage (Δpi < -0.15; p < 0.05) shared across the conditions indicated in the dot matrix below. Each column in the dot matrix highlights the specific combination of conditions contributing to a given intersection (e.g., dots under “Val” and “Triple” show the overlap between these two). To improve clarity, we have expanded the figure legend accordingly and now refer to the UpSetR methodology in the main text.

-In Fig. 4E, one cannot determine what the P values actually are, which should be provided in the legend to confirm statistical significance.

Response: Thank you for pointing that out. The legend in Figure 4E (now Figure 4F) for the p-values was accidentally removed during figure editing. We have added the legend back, so that the statistical significance is clear.

-It's difficult to understand how the -Leu condition and the Double starvation can produce polarized RPFs (Fig. 4A) without evidence of stalling at the cognate hungry codons (Fig. 4E), despite showing later in Fig. 5A that the numbers of stall sites are comparable in those cases to that found for -Ile.

Response: We appreciate this comment, which points to an important property of RPF profiles under nutrient stress. As shown in Figure 4A, all starvation conditions induce a degree of 5′ ribosome footprint polarization, a pattern that can be observed under various stress conditions and perturbations (Allen et al. 2021; Hwang and Buskirk 2017; Li et al. 2023). This general 5′ bias likely reflects a combination of slowed elongation and altered ribosome dynamics and is not necessarily linked to codon-specific stalling. However, Val and Triple starvation show a much stronger and more asymmetric polarization, characterized by pronounced 5′ accumulation and 3′ depletion of ribosome density. To better illustrate this, we have updated the visualization of polarity scores and added a new bar chart summarizing the number of transcripts showing strong 5′ polarization under each condition. This quantification highlights that the effect is markedly more prevalent under Val and Triple conditions than under Leu or Double starvation. In addition, Figure 4F demonstrates that this polarity is codon-specific under Val and Triple starvation. We clarify that this analysis tests for enrichment of specific codons near the start codon among the polarized transcripts and does not directly assess stalling. The observed enrichment of Val codons in the 5′ regions of polarized transcripts supports the interpretation that early elongation delays contribute to the RPF shift. In contrast, no such enrichment is observed for Leu starvation, reinforcing that Leu-induced polarity is not driven by stalling at Leu codons. While Figure 5 shows a similar number of peak-called stalling sites in -Leu, -Ile, and Double starvation, we note that Ribo-seq signal variability under Ile starvation was higher, which may have limited statistical power for detecting stalling sites, even though clear dwell time increases were observed at specific codons. Additionally, we have improved the metagene plots depicting total ribosome footprint density in Figure 4A. The previous version incorrectly showed sharp drops at CDS boundaries due to binning artifacts. The updated version more accurately reflects the density distribution and further highlights the stronger polarization in Val and Triple conditions. Together, these clarifications and improvements within the main text now more clearly distinguish between general polarity effects and codon-specific stalling.

-Fig. 5B: the P values should be given for all five columns, and it should be explained here or in the Discussion why the authors conclude that stalling is an important determinant for reduced translation when a significant correlation seems to exist only for the -Val condition and not even for the Triple condition.

Response: We thank the reviewer for this important observation. In response, we have revised both the text and the figures to provide a clearer and biologically more meaningful representation of the relationship between ribosome stalling and reduced protein output. Specifically, we have replaced the previous Figure 5B with a new analysis that stratifies transcripts based on the number of identified stalling sites. This updated analysis, now shown in Figure 5B, reveals that under Val and Triple starvation conditions, proteins that are downregulated tend to originate from transcripts with multiple stalling sites. Importantly, the corresponding p-values for all five conditions are now explicitly shown in the figure (as red lines). As the reviewer correctly notes, only the Val condition shows a statistically significant enrichment when considering overall overlap. Triple starvation shows a similarly high proportion of overlap (72.3%) but does not reach statistical significance, likely due to the more complex background composition under combined starvation, which increases the expected overlap and reduces statistical power. By stratifying transcripts by the number of stalling sites, we uncover that transcripts with ≥2 stalling sites are enriched among downregulated proteins specifically under Val and Triple conditions, providing a more robust indication of the link between stalling and translation repression under Valine deprivations. We believe this refined approach, prompted by the reviewer’s comment, offers a clearer and biologically more relevant perspective on the role of ribosome stalling. The original analysis previously shown in Figure 5B is now provided as Supplemental Figure 10C for transparency and comparison. We have clarified this in the revised text and now interpret the relationship more cautiously.

-p. 17: "Of note, in cases where valine or isoleucine codons were present just upstream (rather than at) the stalling position, we noted a strong bias for GAG (E), GAA (E), GAU (D), GAC (D), AAG (K), CAG (Q), GUG (V) and GGA (G) (Val starvation) and AAC (N), GAC (D), CUG (L), GAG (E), GCC (A), CAG (Q), GAA (E) and AAG (K) (Ile starvation) at the stalling site (Supplementary Figure 7B)." The authors fail to explain why these codons would be present in the A sites at stalling sites rather than the hungry codons themselves, especially since it is the decoding times of the hungry codons that are increased according to Fig. 1A-E. As suggested above, is this a CHX artifact?

Response: We agree that the observation that the listed codons are enriched at identified stalling positions (now Supplementary Figure 10C), while the depleted amino acid codon is located upstream, is a finding that needs more detailed explanation. Importantly, this phenomenon is not attributable to CHX artifacts, as our Ribo-seq protocol employs CHX solely during brief washes and lysis to prevent post-lysis ribosome run-off, rather than live-cell pre-treatment. Instead, we propose two hypotheses to explain this pattern: Firstly, many of these enriched codons are already inherently slow-decoded with longer DTs even under control conditions (Supplementary Figure 5H, newly added). Together with the upstream hungry codons they might form a challenging consecutive decoding environment, which results in an attenuated ribosome slowdown downstream after the hungry codon. Second, ribosome queuing may further explain this pattern. When a ribosome encounters a critically hungry codon and stalls, subsequent ribosomes can form a queue. The codon within the A-site of the queued ribosome would be (more or less) independent of the identity of the hungry codon itself that caused the initial stall. Since the listed codons have a high frequency within the transcriptome (Supp. Fig 5B), they therefore have an increased likelihood of appearing at this “stalling site”. Importantly, both of these phenomena are not necessarily represented by a general increase of DT on all of the listed codons and would therefore only be captured by the direct extraction of stalling sites but might be averaged out in the global dwell time analysis. We mention this phenomenon now in the Discussion.

-Fig. 5D: P values for the significance, or lack thereof, of the different overlaps should be provided.

Response: Thanks for pointing out this omission. We have now computed hypergeometric p-values for comparisons shown in Figure 5D and Figure 5E, and report them directly in the main text. As described, the overlap in stalling sites between Val and triple starvation is highly significant (2522 positions, p < 2.2×10⁻¹⁶), while overlaps involving Ile-specific stalling positions are smaller but still statistically robust (e.g., 149 positions for Ile – Triple, p = 1.77×10⁻⁵²). Notably, we also calculated p-values at the transcript level and found that a large fraction of transcripts with Ile-specific stalling under single starvation also stall under triple starvation, though often at different positions (1806 transcripts, p = 1.78×10⁻⁵⁸). These values are now included in the revised results section to support the interpretation of these overlaps.

-p. 17: "Nonetheless, when we examined entire transcripts rather than single positions, many transcripts that exhibited isoleucine-related stalling under Ile starvation also stalled under triple starvation, but at different sites along the CDS (Figure 5E). This finding is particularly intriguing, as it suggests that while Ile-starvation-specific stalling sites may shift under triple starvation, the overall tendency of these transcripts to stall remains." The authors never come back to account for this unexpected result.

Response: Thank you for highlighting this point. We've incorporated this finding as part of the proposed "bottleneck" scenario. While the isoleucine-specific stalling sites identified under Ile starvation do shift or disappear under triple starvation, we've observed that the same transcripts still tend to exhibit stalling. However, this now primarily occurs at upstream valine codons. We interpret this as a consequence of early elongation stalling caused by strong pausing at Val codons. This restriction on ribosome progression effectively prevents ribosomes from reaching the original Ile stalling sites. Therefore, the stalling sites identified under triple starvation are largely explained by the Val codons, reflecting a redistribution of stalling rather than its loss. To further clarify this crucial point, we've now explicitly mentioned Figure 5D-E again in the subsequent paragraph, which introduces the bottleneck theory.

-It seems very difficult to reconcile the results in Fig. 5F with those in Fig. 4A, where similar polarities in RPFs are observed for -Ile and -Val in Fig, 4A but dramatically different distributions of stalling sites in Fig. 5F. More discussion of these discrepancies is required.

Response: Thank you for pointing this out. The apparent discrepancy between the RPF profiles shown in Figure 4A and the stalling site distributions in Figure 5F likely reflects the fact that RPF polarization includes both general (unspecific) and codon-specific components. Figure 4A displays total ribosome footprint density, capturing both broad stress-induced effects and codon-specific contributions, whereas Figure 5F focuses specifically on peak-called stalling sites, representing localized and statistically significant pauses. Importantly, we would like to emphasise that Fig 4 shows that -Val and -Ile starvation exhibit different responses and not the same patterns. To make these differences even clearer, we have now updated the visualizations in Figure 4, including improved polarity plots and a new bar chart summarizing the number of transcripts with strong 5′ polarization. These additions highlight that the RPF profiles under -Val starvation are more pronounced and asymmetric, particularly due to 3′ depletion, while the polarity under -Ile is milder and a distinct, much smaller subset of transcripts appears to show polarity score shifts. We believe the updated figures and accompanying explanations now make these distinctions clearer.

• p. 18: " These isoacceptor-specific patterns correlate largely with the particular subsets of leucine and isoleucine codons that stalled (Figure 1A)." This correlation needs to be addressed for each codon-anticodon pair for all of the codons showing stalling in Fig. 1A.

Response: We thank the reviewer for this important comment. In the revised manuscript, we have expanded the relevant sections to address codon–anticodon relationships more thoroughly. We now explicitly match codons that exhibited increased dwell times under starvation to the corresponding tRNA isoacceptors whose charging was affected, and we provide a clearer discussion of the caveats involved. As noted by the reviewer, this correlation is not straightforward, as it is complicated by wobble base pairing, anticodon modifications, and the fact that multiple codons can be decoded by more than one isoacceptor, and vice versa. Moreover, in our qPCR-based tRNA charging assay, certain isoacceptors cannot be distinguished due to highly similar sequences (e.g., LeuAAG and LeuUAG, and LeuCAA and LeuCAG), which limits resolution for exact pairing. In addition, we did not assess absolute tRNA abundance, which may further influence decoding capacity. Nevertheless, where resolution is possible, the patterns align well: All tRNAVal isoacceptors became uncharged under Val and triple starvation, matching the consistent dwell time increases across all Val codons. Only tRNAIleAAU (decoding AUU and AUC) was deacylated, matching to these codons showing increased dwell times, while AUA (decoded by still-charged tRNAIleUAU) did not. Only CUU (decoded by uncharged tRNALeuGAA) showed increased dwell time. A mild deacylation of the other Leu isoacceptors was observed, but isoacceptor-level resolution is limited by assay constraints. However, these rather minimal tRNA and DT changes were consistent with more dominant initiation repression rather than elongation stalls. To support this analysis, we included an illustrative figure (now in Supplementary Figure 12F) summarizing the codon–anticodon matches.

-p. 19: "For instance, in our double starvation condition, unchanged tRNA charging levels (Figure 6E) may result from a pronounced downregulation of global translation initiation, likely driven by the activation of stress responses (Figure 2), subsequently lowering the demand for charged tRNAs as it has been observed previously for Leu starvation 39.” This seems at odds with the comparable down-regulation of protein synthesis for the Double starvation and -Leu and -Ile single starvations shown in Fig. 3C. Also, in the current study, Leu starvation does lower charging of certain Leu tRNAs.

Response: We thank the reviewer for raising this important point. In the revised manuscript, we have clarified this section and now offer a more refined interpretation of the tRNA charging patterns observed under double starvation. While Figure 3C shows a comparable reduction in global protein synthesis across the -Leu, -Ile, and double starvation conditions, it needs to be considered that the OPP assay has limited sensitivity. It operates in a relatively low fluorescence intensity range and is subject to background signal, which may obscure subtle differences between conditions. Moreover, other factors such as changes in protein stability or turnover could also contribute to the observed differences. Therefore, inter-condition differences in translation repression should be interpreted with caution. However, based on our stress response analysis (Figure 2), mTORC1 inactivation appears strongest under double starvation, likely leading to more profound suppression of translation initiation. This would reduce the overall demand for charged tRNAs and could explain why no detectable tRNA deacylation was observed under double starvation, even though mild uncharging of Leu isoacceptors occurred under -Leu, which exhibited a milder stress response. This distinction is consistent with the observed mild dwell time increases for one Leu codon under -Leu, but not in the double condition. Similarly, the absence of Ile codon stalling and tRNA deacylation under double starvation may be attributed to stress-driven reductions in elongation demand, preventing the tRNA depletion and codon-specific delays observed under single Ile starvation. A more direct clarification is now included in the revised manuscript.

Reviewer #2 (Significance):

The results here are significant in showing that starvation for a single amino acid does not lead to deacylation of all isoacceptors for that amino acid and in revealing that starvation for one amino acid can prevent deacylation of tRNAs for other amino acids, as shown most dramatically for the selective deacylation of only Val tRNAs in the triple BRCAA starvation condition. For the various reasons indicated above, however, I'm not convinced that their "bottleneck" mechanism is adequate to explain this phenomenon, especially in the case of the selective deacylation of Ile vs Leu tRNA in the Double starvation regime. It's also significant that deacylation leads to ribosome build-up near the 5'ends of CDS, which seems to be associated with an enrichment for the hungry codons in the case of Val and Ile starvation, but inexplicably, not for Leu or the Double starvations. This last discrepancy makes it hard to understand how the -Leu and Double starvations produce RPF buildups near the 5 ends of CDSs. In addition, the claim in the Discussion that "our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress" overstates the strength of evidence that the stalling events lead to substantial decreases in translational efficiencies for the affected mRNAs, as the stalling frequency and decreased protein output are significantly correlated only for the -Val starvation, and the data in Fig. 3 D-H suggest that the reductions in protein synthesis generally occur at the level of initiation, even for -Val starvation, with a contribution from slow elongation only for -Ile-which is in itself difficult to understand considering that stalling frequencies are highest in -Val. Thus, while many of the results are very intriguing and will be of considerable interest to the translation field, it is my opinion that a number of results have been overinterpreted and that important inconsistencies and complexities have been overlooked in concluding that a significant component of the translational inhibition arises from the increased decoding times at hungry codons during elongation and that the selective deacylation of Val tRNAs in the Triple starvation can be explained by the "bottleneck" mechanism. The complexities and limitations of the data and their intepretations should be discussed much more thoroughly in the Discussion, which currently is devoted mostly to other phenomena often of tangential importance to the current findings. A suitably revised manuscript would clearly state the limitations and caveats of the proposed mechanisms and consider other possible explanations as well.

Again, we thank the reviewer for the valuable insights and constructive critiques. We believe that the concerns regarding potential overinterpretation and inconsistencies have now been addressed through clearer explanations and more cautious interpretation throughout the revised manuscript. We also agree that the original Discussion included aspects that, while interesting, were of secondary importance. In light of the reviewer’s suggestions, we have restructured and rebalanced the Discussion to focus more directly on the key findings and their implications. Importantly, we wish to clarify that we do not propose the elongation bottleneck model as a general mechanism across all conditions. In particular, for double (Leu/Ile) starvation, we attribute the observed effects primarily to stress response–mediated translational repression, and not to codon-specific stalling or tRNA depletion. We believe that this distinction is now more clearly conveyed in the revised manuscript.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary

Worpenberg and colleagues investigated the translational consequences of branched-chain amino acid (BCAA) starvation in mouse cells. Limitation of individual BCAAs has been reported to cause codon-specific and global translational repression. In this paper, the authors use RNA-seq, ribosome profiling (Ribo-seq), proteomics, and tRNA charging assays to characterize the impacts of individual and combined depletion of leucine, isoleucine, and valine on translation. They find that BCAA starvation increases codon-specific ribosome dwell times, activates global translational stress responses and reduces global protein synthesis. They infer that this effect is due to decreased translation initiation and codon-specific translational stalling. They find that the effects of simultaneous depletion are non-additive. In valine and triple (valine, leucine, and isoleucine) depletion, they show that affected transcripts have a high density of valine codons early in their coding sequences, creating an "elongation bottleneck" that obscures the impact of starvation of other amino acids. Finally, they identify isoacceptor-specific differences in tRNA charging that help explain the codon-specific effects that they observe.

We find the major findings convincing and clear. We find that some results are incompletely explained. We suggest an additional experiment and also have some minor comments that we hope will improve clarity and rigor.

We thank the reviewer for the thorough and constructive feedback. We appreciate the recognition of our main findings and the helpful suggestions for improving the manuscript. Below we address each point in detail.

Major comments

Figure 3O: In this figure and the associated text, the authors try to determine whether differences in protein degradation can explain why some proteins have higher ribosome density but lower proteomic expression. However, since this analysis relies on published protein half-lives from non-starvation conditions and on the assumption that protein synthesis has entirely stopped, we are not convinced it is informative for this experimental context. It does not distinguish between a model in which protein synthesis has been reduced by stalling and a model in which both protein synthesis and degradation rate have increased, which are both consistent with their Ribo-seq and proteomic data. To address this issue, the authors should either perform protein half-life measurements under their starvation conditions, or more clearly explain these two models in the text and acknowledge that they cannot distinguish between them.

Response: We agree with the reviewer that our current analysis, which is based on protein half-lives obtained under non-starvation conditions, can not definitively separate the effects of reduced translation from those of increased protein degradation. We have revised the relevant section in the manuscript to more clearly state that this analysis is correlative in nature and serves only to explore one possible explanation for the observed disconnect between ribosome density and protein levels. We now also explicitly acknowledge that our dataset does not allow us to distinguish between a model in which protein output is reduced due to stalling and one in which both translation and degradation rates are altered. However, the observed log2FC in the proteomics data are often milder than expected based on complete-medium condition half-life alone, which would be difficult to reconcile with a dominant contribution from global protein destabilization. That said, we also acknowledge that protein degradation is highly context- and protein-specific, and that proteolytic regulation might still play a role. Performing a direct protein half-life measurement under our starvation conditions would indeed be required to rigorously test this, but such an experiment is outside the scope of this study. We now highlight this as a limitation and a valuable direction for future work, and we have softened any interpretations in the main text to reflect the uncertainty regarding the contribution of protein stability changes.

Minor comments

Figure 1G: Why does intracellular valine seem to be less depleted under starvation conditions than intracellular leucine or isoleucine? Are the limits of detections different for different amino acids? The authors should acknowledge this discrepancy and comment on whether it has any implications for interpretation of their results.

Response: We thank the reviewer for this important point. While valine appears slightly less depleted than leucine or isoleucine in Figure 1G, the fold changes and absolute reductions are strong for all three BCAAs, including valine. To further illustrate this, we have added a supplementary bar chart showing the measured intracellular concentrations in µmol/L, including mean and variance across five biological replicates (Supplementary Figure 5A). We believe that the variation may reflect technical factors, such as differences in detection sensitivity or ionization efficiency between amino acids in the targeted metabolomics assay and, therefore, that the observed difference does not have a meaningful impact on the interpretation of our results. We now directly acknowledge these differences in the main text.

Figure 1H: These data do not appear to meet the assumptions for linear regression. We suggest either reporting a Spearman R correlation (as the data appears linear in rank but not absolute value), or remove it entirely - we think the plot without statistics is sufficient.

Response: We thank the reviewer for the suggestion. In the revised manuscript, we removed the statistical annotation and retained only the trend line to illustrate the general pattern. We agree that this visualization alone is sufficient to support the qualitative point we aimed to convey.

Figure 2B: The in-text description of this figure states that "most" ISR genes show a "robust induction," but only three genes are shown in the figure, two of which are upregulated. The authors should instead specify that 2 out of the 3 genes profiled were robustly induced.

Response: We have rephrased the sentence to say “two of the three genes profiled…” for precision and consistency with the data shown.

Figure 2D: Please include the full, uncropped blots in the supplementary materials.

Response: We have now added the full, uncropped western blots to the supplementary material (Supplementary Figure 8).

Figure 2E: Swap the positions of the RPS6 and 4E-BP1 plots so they line up with their respective blots to make these figures easier to interpret. Authors should consider doing a one-way ANOVA and post-hoc analysis, if we correctly understand that they are making a conclusion about the difference between multiple groups in aggregate.

Response: We thank the reviewer for the suggestion. The alignment of the RPS6 and 4E-BP1 plots with their respective blots has been corrected. As this panel focuses on comparisons to the control condition only, we have retained the original presentation.

Figure 4B: Panel A in this figure is very convincing, and these plots don't add additional information. The authors could consider removing them. If this panel stays in, we suggest removing the "mid index" plot, since it is never referenced in the text and doesn't seem relevant to the message of the figure.

Response: We appreciate the feedback. While we considered removing panel B as suggested, we decided to retain it because it provides a useful summary of panel A. To improve clarity and visual interpretation, we replaced the original boxplot with a bar plot displaying mean values and SEM error bars. We believe the bar plot now nicely illustrates that Val and Triple starvation lead to stronger effects, especially in the reduction of the 3′ index. The “mid index” plot, which was not referenced in the text and did not contribute to the central message, has been removed as suggested.

Figure 4E: Why is there a reduction in frequency of a Leu and a Val codon under Ile starvation?

Response: Thank you for highlighting this observation. The reduction in the frequency of a specific Leu and Val codon under Ile starvation in Figure 4F (former Figure 4E) is indeed intriguing. This figure reflects codon usage in the first 20% of the CDSs among the subset of transcripts that exhibit a footprint polarization under each starvation condition. As such, the observed depletion likely arises from the specific transcript composition of the polarized subset under -Ile, which differs from that under -Val or other conditions. Importantly, this pattern is not consistently observed when analyzing the full transcripts (another Leu codon is affected), indicating that it is not a systematic depletion of these codons. One possibility is that an increased frequency of Ile codons (AUC) within the constrained region may lead to a relative underrepresentation of other codons, such as Leu and Val. Alternatively, this may reflect non-random codon co-occurrence patterns within specific transcripts. While our current data do not allow us to investigate this further, we acknowledge these as speculative explanations and now mention this point in the Discussion as a potential avenue for future study.

Figure 5G: There appears to be one Val codon early in the Hint1 transcript without much stalling under triple or valine starvation conditions. The authors should acknowledge this and comment on why this may be.

Response: We thank the reviewer for pointing this out. While the Hint1 transcript indeed contains a valine codon early in its CDS, no clear stalling peak was observed at that position under valine or triple starvation. Several factors may contribute to this: local sequence context can influence ribosome pausing, and not all cognate codons necessarily lead to detectable stalling even under amino acid starvation. Additionally, coverage at the 5′ end of Hint1 is relatively sparse in our dataset, and potential mappability limitations, such as regions with low complexity or repetitive elements, may further reduce resolution at specific sites. We now briefly mention this in the manuscript to clarify the possible causes.

Figure 5B: In the text referencing this figure, the authors state that "a high number of downregulated proteins with associated ribosome stalling sites did not show an overall decreased mean RPF count...as it would be expected from translation initiation defects, linking these stalling sites directly to proteomic changes." However, RPF is affected both by stalling (increases RPF) and initiation defects (decreases RPF). A gene with both stalling and decreased initiation may appear to have no RPF change. The data does suggest a contribution from stalling, but the authors should also acknowledge that reduced initiation may also be playing a role.

Response: We agree with the reviewer comment. Our cited statement should indeed be more nuanced. The reviewer correctly points out that RPFs are influenced by both increased ribosome density due to stalling and decreased ribosome density due to reduced initiation. Therefore, a gene experiencing both stalling and reduced initiation might appear to have no net change in RPF, or even a slight increase if stalling is dominant. Thus, while the presence of stalling sites strongly suggests a contribution from compromised elongation to reduced protein output, we cannot definitively rule out a concurrent role for reduced initiation, even in cases where RPF counts are not globally decreased. We revised this section in the manuscript to acknowledge this interplay.

Figure 5E: the black text on dark brown in the center of the Venn diagram is difficult to read. The diagram should either have a different color scheme, or the text in the center should be white instead of black for higher contrast.

Response: We have adjusted the text color for better contrast and improved readability.

Supplementary Figure 1C: The ribosome dwell time data in this study is described as "highly correlated" with another published dwell time dataset, but the P and E site data do not seem strongly correlated. The authors should remove the word "highly."

Response: We have removed the word “highly” to have a more cautious interpretation in the text.

Supplementary Figure 3E: Not all of the highlighted codons in this figure are ones with prolonged dwell times. To clarify the point that dwell time change is not related to codon frequency, this figure should only highlight codons that have a significantly prolonged dwell time in at least one starvation condition.

Response: We thank the reviewer for pointing this out. To improve clarity, we have revised the figure and now specifically highlight codons with significantly prolonged dwell times with stars.

Supplementary Figure 5C: The gene Chop is mentioned in the main text when referencing this figure, but is absent from the heatmap.

Response: We thank the reviewer for noting this. The gene Chop is annotated under its alternative name Ddit3 in the current version of the heatmap and is indeed present. To avoid confusion, we have now updated the label in the figure to display Chop (Ddit3) directly.

Supplementary Figure 7A: The authors could clarify this figure by adding additional language to either the figure panel or the figure legend specifying that the RPM metric being used comes from Ribo-seq.

Response: We have updated the legend to explicitly state that the RPM values shown are derived from Ribo-seq data.

Supplementary Figure 7D: The metric used to describe the spatial relationship between the first valine and isoleucine codons in transcripts in this figure seems to be describing something conceptually similar to the stalling sites in Figure 5G, but uses a different metric. These figures would be easier to interpret if these spatial relationships were presented in a consistent way throughout the manuscript.

Response: We thank the reviewer for this helpful observation. Supplementary Figure 7D (now Supplementary Figure 11B) originally used a gene-length-normalized metric to describe codon spacing, whereas Figure 5G depicted absolute nucleotide distances to stalling sites. To ensure consistency across the manuscript, we have now updated Supplementary Figure 11B to also use absolute distances. We believe this adjustment improves clarity and allows for a more direct comparison between spatial codon patterns and stalling events.

Discussion:

Reader understanding would be improved if the relevance of paragraphs were established in the first sentence. For instance, in the paragraphs about adaptive misacylation and posttranscriptional modifications, it is unclear until the end of the paragraph how these topics are relevant. Introducing the relevant aspects of the study (the fact that some starvation conditions have less severe effects and the observation about m6A-related mRNAs) at the beginning of these paragraphs would improve clarity.

Response: We thank the reviewer for this helpful comment. We agree that the flow and clarity of the Discussion can be improved by making the relevance of each paragraph clearer from the outset. In the revised manuscript, we have restructured these sections to better highlight the connection between each topic and our main findings. These changes also align with suggestions from Reviewer 2, and we believe they help to focus the Discussion more tightly around the core insights of our study.

The authors should provide more information and speculation about possible physiological relevance of their findings, particularly about the way that the effects of triple starvation are highly valine-dependent. Are there physiological conditions under which starvation of all three BCAAs is more likely than starvation of one or two of them? If so, are there any reasons why a valine-based bottleneck might be advantageous?

Response: We appreciate the reviewer's insightful question regarding the physiological relevance of our findings, particularly the valine-dependent bottleneck observed under triple BCAA starvation. This prompts a crucial discussion on the broader biological context of our work.

While complete starvation of all three BCAAs might be less frequent than individual deficiencies, such conditions are physiologically relevant in several contexts. In prolonged fasting, starvation, or severe cachectic states associated with chronic diseases (e.g., advanced cancer, critical illness), systemic amino acid pools, including BCAAs, can become significantly depleted due to increased catabolism and insufficient intake (Yu et al. 2021). Moreover, certain specialized diets or therapeutic strategies aim to modulate BCAA levels. For instance, in some Maple Syrup Urine Disease (MSUD) management protocols, BCAA intake is severely restricted to prevent the accumulation of toxic BCAA metabolites (Mann et al. 2021). Similarly, emerging cancer therapies sometimes explore nutrient deprivation strategies to selectively target tumor cells, which could involve broad BCAA reduction (e.g. Sheen et al. 2011; Xiao et al. 2016).

In these contexts, a valine-based bottleneck, as we describe, could indeed represent an adaptive strategy. If valine-tRNAs are particularly susceptible to deacylation and valine codons are strategically enriched at the 5' end of transcripts, stalling at these early positions could serve as a rapid "gatekeeper" for global translation. This early-stage inhibition would conserve cellular energy and available amino acids by quickly reducing the overall demand for charged tRNAs. Such a mechanism could potentially prioritize the translation of a subset of proteins that might have different codon usage biases or are translated via alternative, less valine-dependent mechanisms. This aligns with the concept of a multi-layered translational control where global initiation repression (as reflected in mTORC1 inhibition and polysome profiles) is complemented by specific elongation checkpoints, allowing for a more nuanced and adaptive response to severe nutrient stress.

Reviewer #3 (Significance):

Nature and significance of the advance

The main contribution of this work is to demonstrate that depletion of multiple amino acids simultaneously impacts translation elongation in ways that are not necessarily additive. These impacts can depend on the distribution of codons in a transcript. It adds to a growing body of work showing that essential amino acid starvation can cause codon-specific ribosome stalling. The authors suggest that the position-dependent stalling they observe could be a novel regulatory mechanism to alleviate the effects of multi-amino acid starvation. However, it is not fully clear from the paper what the significance of a valine-based regulatory adaptation to BCAA starvation is, or whether simultaneous starvation of all three BCAAs is of particular physiological relevance. The paper's primary contribution is mainly focused on the similarity between valine and triple BCAA starvation, and it provides limited insight into the effects of combined depletion of two BCAAs.

Context of existing literature

Although ribosome profiling does not distinguish between actively-elongating and stalled ribosomes, sites with higher read coverage, and thereby higher inferred dwell time, can be used to infer ribosome stalling (Ingolia 2011). Various downstream effects of essential amino acid depletion have been documented, such as leucine deficiency being sensed by mTORC1 via leucyl-tRNA synthetase (Dittmar 2005, Han 2012), and shared transcriptional responses among many amino acid depletion conditions (Tang 2015). These authors have previously measured the translational effects of nutrient stress using ribosome profiling (e.g., Gobet 2020), as have others (Darnell 2018, Kochavi et al. 2024). The present work represents the first study (to our knowledge) combining BCAA depletions, representing an incremental and useful contribution to our understanding of translational responses to stress conditions.

Audience

This work is of interest to investigators studying the response of human cells in stress conditions, such as in human disease, as well as investigators studying the basic biology of eukaryotic translational control.

Reviewer expertise: mRNA decay and translation regulation in bacteria.

We hope the authors have found our comments thoughtful and useful. We welcome further discussion or clarification via email: Juliana Stanley (julianst@mit.edu) and Hannah LeBlanc (leblanch@mit.edu).

We sincerely thank the reviewers for their thoughtful and constructive feedback, as well as for their careful and thorough reading of our manuscript. We also gratefully acknowledge the invitation for further discussion and would be happy to engage in future correspondence.

References

Allen, George E., Olesya O. Panasenko, Zoltan Villanyi, Marina Zagatti, Benjamin Weiss, Lucile Pagliazzo, Susanne Huch, et al. 2021. “Not4 and Not5 Modulate Translation Elongation by Rps7A Ubiquitination, Rli1 Moonlighting, and Condensates That Exclude eIF5A.” Cell Reports 36 (9): 109633. https://doi.org/10.1016/j.celrep.2021.109633.

Darnell, Alicia M., Arvind R. Subramaniam, and Erin K. O’Shea. 2018. “Translational Control through Differential Ribosome Pausing during Amino Acid Limitation in Mammalian Cells.” Molecular Cell 71 (2): 229-243.e11. https://doi.org/10.1016/j.molcel.2018.06.041.

Dittmar, Kimberly A., Michael A. Sørensen, Johan Elf, Måns Ehrenberg, and Tao Pan. 2005. “Selective Charging of tRNA Isoacceptors Induced by Amino-Acid Starvation.” EMBO Reports 6 (2): 151–57. https://doi.org/10.1038/sj.embor.7400341.

Elf, Johan, Daniel Nilsson, Tanel Tenson, and Mans Ehrenberg. 2003. “Selective Charging of tRNA Isoacceptors Explains Patterns of Codon Usage.” Science (New York, N.Y.) 300 (5626): 1718–22. https://doi.org/10.1126/science.1083811.

Gobet, Cédric, Benjamin Dieter Weger, Julien Marquis, Eva Martin, Nagammal Neelagandan, Frédéric Gachon, and Felix Naef. 2020. “Robust Landscapes of Ribosome Dwell Times and Aminoacyl-tRNAs in Response to Nutrient Stress in Liver.” Proceedings of the National Academy of Sciences of the United States of America 117 (17): 9630–41. https://doi.org/10.1073/pnas.1918145117.

Hussmann, Jeffrey A., Stephanie Patchett, Arlen Johnson, Sara Sawyer, and William H. Press. 2015. “Understanding Biases in Ribosome Profiling Experiments Reveals Signatures of Translation Dynamics in Yeast.” Edited by Michael Snyder. PLOS Genetics 11 (12): e1005732. https://doi.org/10.1371/journal.pgen.1005732.

Hwang, Jae-Yeon, and Allen R. Buskirk. 2017. “A Ribosome Profiling Study of mRNA Cleavage by the Endonuclease RelE.” Nucleic Acids Research 45 (1): 327–36. https://doi.org/10.1093/nar/gkw944.

Juszkiewicz, Szymon, and Ramanujan S. Hegde. 2017. “Initiation of Quality Control during Poly(A) Translation Requires Site-Specific Ribosome Ubiquitination.” Molecular Cell 65 (4): 743-750.e4. https://doi.org/10.1016/j.molcel.2016.11.039.

Li, Fajin, Jianhuo Fang, Yifan Yu, Sijia Hao, Qin Zou, Qinglin Zeng, and Xuerui Yang. 2023. “Reanalysis of Ribosome Profiling Datasets Reveals a Function of Rocaglamide A in Perturbing the Dynamics of Translation Elongation via eIF4A.” Nature Communications 14 (1): 553. https://doi.org/10.1038/s41467-023-36290-w.

Mann, Gagandeep, Stephen Mora, Glory Madu, and Olasunkanmi A. J. Adegoke. 2021. “Branched-Chain Amino Acids: Catabolism in Skeletal Muscle and Implications for Muscle and Whole-Body Metabolism.” Frontiers in Physiology 12 (July):702826. https://doi.org/10.3389/fphys.2021.702826.

Saikia, Mridusmita, Xiaoyun Wang, Yuanhui Mao, Ji Wan, Tao Pan, and Shu-Bing Qian. 2016. “Codon Optimality Controls Differential mRNA Translation during Amino Acid Starvation.” RNA (New York, N.Y.) 22 (11): 1719–27. https://doi.org/10.1261/rna.058180.116.

Sharma, Puneet, Jie Wu, Benedikt S. Nilges, and Sebastian A. Leidel. 2021. “Humans and Other Commonly Used Model Organisms Are Resistant to Cycloheximide-Mediated Biases in Ribosome Profiling Experiments.” Nature Communications 12 (1): 5094. https://doi.org/10.1038/s41467-021-25411-y.

Sheen, Joon-Ho, Roberto Zoncu, Dohoon Kim, and David M. Sabatini. 2011. “Defective Regulation of Autophagy upon Leucine Deprivation Reveals a Targetable Liability of Human Melanoma Cells In Vitro and In Vivo.” Cancer Cell 19 (5): 613–28. https://doi.org/10.1016/j.ccr.2011.03.012.

Xiao, Fei, Chunxia Wang, Hongkun Yin, Junjie Yu, Shanghai Chen, Jing Fang, and Feifan Guo. 2016. “Leucine Deprivation Inhibits Proliferation and Induces Apoptosis of Human Breast Cancer Cells via Fatty Acid Synthase.” Oncotarget 7 (39): 63679–89. https://doi.org/10.18632/oncotarget.11626.

Yu, Deyang, Nicole E. Richardson, Cara L. Green, Alexandra B. Spicer, Michaela E. Murphy, Victoria Flores, Cholsoon Jang, et al. 2021. “The Adverse Metabolic Effects of Branched-Chain Amino Acids Are Mediated by Isoleucine and Valine.” Cell Metabolism 33 (5): 905-922.e6. https://doi.org/10.1016/j.cmet.2021.03.025.

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Referee #3

Evidence, reproducibility and clarity

Summary

Worpenberg and colleagues investigated the translational consequences of branched-chain amino acid (BCAA) starvation in mouse cells. Limitation of individual BCAAs has been reported to cause codon-specific and global translational repression. In this paper, the authors use RNA-seq, ribosome profiling (Ribo-seq), proteomics, and tRNA charging assays to characterize the impacts of individual and combined depletion of leucine, isoleucine, and valine on translation. They find that BCAA starvation increases codon-specific ribosome dwell times, activates global translational stress responses and reduces global protein synthesis. They infer that this effect is due to decreased translation initiation and codon-specific translational stalling. They find that the effects of simultaneous depletion are non-additive. In valine and triple (valine, leucine, and isoleucine) depletion, they show that affected transcripts have a high density of valine codons early in their coding sequences, creating an "elongation bottleneck" that obscures the impact of starvation of other amino acids. Finally, they identify isoacceptor-specific differences in tRNA charging that help explain the codon-specific effects that they observe.

We find the major findings convincing and clear. We find that some results are incompletely explained. We suggest an additional experiment and also have some minor comments that we hope will improve clarity and rigor.

Major comments

Figure 3O: In this figure and the associated text, the authors try to determine whether differences in protein degradation can explain why some proteins have higher ribosome density but lower proteomic expression. However, since this analysis relies on published protein half-lives from non-starvation conditions and on the assumption that protein synthesis has entirely stopped, we are not convinced it is informative for this experimental context. It does not distinguish between a model in which protein synthesis has been reduced by stalling and a model in which both protein synthesis and degradation rate have increased, which are both consistent with their Ribo-seq and proteomic data. To address this issue, the authors should either perform protein half-life measurements under their starvation conditions, or more clearly explain these two models in the text and acknowledge that they cannot distinguish between them.

Minor comments

Figure 1G: Why does intracellular valine seem to be less depleted under starvation conditions than intracellular leucine or isoleucine? Are the limits of detections different for different amino acids? The authors should acknowledge this discrepancy and comment on whether it has any implications for interpretation of their results.

Figure 1H: These data do not appear to meet the assumptions for linear regression. We suggest either reporting a Spearman R correlation (as the data appears linear in rank but not absolute value), or remove it entirely - we think the plot without statistics is sufficient.

Figure 2B: The in-text description of this figure states that "most" ISR genes show a "robust induction," but only three genes are shown in the figure, two of which are upregulated. The authors should instead specify that 2 out of the 3 genes profiled were robustly induced.

Figure 2D: Please include the full, uncropped blots in the supplementary materials.

Figure 2E: Swap the positions of the RPS6 and 4E-BP1 plots so they line up with their respective blots to make these figures easier to interpret. Authors should consider doing a one-way ANOVA and post-hoc analysis, if we correctly understand that they are making a conclusion about the difference between multiple groups in aggregate.

Figure 4B: Panel A in this figure is very convincing, and these plots don't add additional information. The authors could consider removing them. If this panel stays in, we suggest removing the "mid index" plot, since it is never referenced in the text and doesn't seem relevant to the message of the figure.

Figure 4E: Why is there a reduction in frequency of a Leu and a Val codon under Ile starvation?

Figure 5G: There appears to be one Val codon early in the Hint1 transcript without much stalling under triple or valine starvation conditions. The authors should acknowledge this and comment on why this may be.

Figure 5B: In the text referencing this figure, the authors state that "a high number of downregulated proteins with associated ribosome stalling sites did not show an overall decreased mean RPF count...as it would be expected from translation initiation defects, linking these stalling sites directly to proteomic changes." However, RPF is affected both by stalling (increases RPF) and initiation defects (decreases RPF). A gene with both stalling and decreased initiation may appear to have no RPF change. The data does suggest a contribution from stalling, but the authors should also acknowledge that reduced initiation may also be playing a role.

Figure 5E: the black text on dark brown in the center of the Venn diagram is difficult to read. The diagram should either have a different color scheme, or the text in the center should be white instead of black for higher contrast.

Supplementary Figure 1C: The ribosome dwell time data in this study is described as "highly correlated" with another published dwell time dataset, but the P and E site data do not seem strongly correlated. The authors should remove the word "highly."

Supplementary Figure 3E: Not all of the highlighted codons in this figure are ones with prolonged dwell times. To clarify the point that dwell time change is not related to codon frequency, this figure should only highlight codons that have a significantly prolonged dwell time in at least one starvation condition.

Supplementary Figure 5C: The gene Chop is mentioned in the main text when referencing this figure, but is absent from the heatmap.

Supplementary Figure 7A: The authors could clarify this figure by adding additional language to either the figure panel or the figure legend specifying that the RPM metric being used comes from Ribo-seq.

Supplementary Figure 7D: The metric used to describe the spatial relationship between the first valine and isoleucine codons in transcripts in this figure seems to be describing something conceptually similar to the stalling sites in Figure 5G, but uses a different metric. These figures would be easier to interpret if these spatial relationships were presented in a consistent way throughout the manuscript.

Discussion:

Reader understanding would be improved if the relevance of paragraphs were established in the first sentence. For instance, in the paragraphs about adaptive misacylation and posttranscriptional modifications, it is unclear until the end of the paragraph how these topics are relevant. Introducing the relevant aspects of the study (the fact that some starvation conditions have less severe effects and the observation about m6A-related mRNAs) at the beginning of these paragraphs would improve clarity.<br /> The authors should provide more information and speculation about possible physiological relevance of their findings, particularly about the way that the effects of triple starvation are highly valine-dependent. Are there physiological conditions under which starvation of all three BCAAs is more likely than starvation of one or two of them? If so, are there any reasons why a valine-based bottleneck might be advantageous?

We hope the authors have found our comments thoughtful and useful. We welcome further discussion or clarification via email: Juliana Stanley (julianst@mit.edu) and Hannah LeBlanc (leblanch@mit.edu).

Significance

Nature and significance of the advance

The main contribution of this work is to demonstrate that depletion of multiple amino acids simultaneously impacts translation elongation in ways that are not necessarily additive. These impacts can depend on the distribution of codons in a transcript. It adds to a growing body of work showing that essential amino acid starvation can cause codon-specific ribosome stalling. The authors suggest that the position-dependent stalling they observe could be a novel regulatory mechanism to alleviate the effects of multi-amino acid starvation. However, it is not fully clear from the paper what the significance of a valine-based regulatory adaptation to BCAA starvation is, or whether simultaneous starvation of all three BCAAs is of particular physiological relevance. The paper's primary contribution is mainly focused on the similarity between valine and triple BCAA starvation, and it provides limited insight into the effects of combined depletion of two BCAAs.

Context of existing literature

Although ribosome profiling does not distinguish between actively-elongating and stalled ribosomes, sites with higher read coverage, and thereby higher inferred dwell time, can be used to infer ribosome stalling (Ingolia 2011). Various downstream effects of essential amino acid depletion have been documented, such as leucine deficiency being sensed by mTORC1 via leucyl-tRNA synthetase (Dittmar 2005, Han 2012), and shared transcriptional responses among many amino acid depletion conditions (Tang 2015). These authors have previously measured the translational effects of nutrient stress using ribosome profiling (e.g., Gobet 2020), as have others (Darnell 2018, Kochavi et al. 2024). The present work represents the first study (to our knowledge) combining BCAA depletions, representing an incremental and useful contribution to our understanding of translational responses to stress conditions.

Audience

This work is of interest to investigators studying the response of human cells in stress conditions, such as in human disease, as well as investigators studying the basic biology of eukaryotic translational control.

Reviewer expertise: mRNA decay and translation regulation in bacteria.

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Referee #2

Evidence, reproducibility and clarity

Summary and General Critique:

This study examines the consequences of starvation for the BRCAAs, either singly, for Leu & Ile, or for all three simultaneously in HeLa cells on overall translation rates, decoding rates at each codon, and on ribosome density, protein expression, and distribution of ribosome stalling events across the CDS for each expressed gene. The single amino acid starvation regimes specifically reduce the cognate intracellular amino acid pool and lead to deacylation of at least a subset of the cognate tRNAs in a manner dependent on continuing protein synthesis. They also induce the ISR equally and decrease bulk protein synthesis equally in a manner that appears to occur largely at the initiation level for -Leu and -Val, judging by the decreased polysome:monsome ratio, but at both the initiation and elongation levels for -Ile-a distinction that remains unexplained. Only -Leu appears to down-regulate mTORC1 and TOP mRNA translation. There is a significant down-regulation of protein levels for 50-200 genes, which tend to be unstable in nutrient-replete cells, only a fraction of which are associated with reduced ribosome occupancies (RPFs measured by Ribo-Seq) on the corresponding mRNAs in the manner expected for reduced initiation, suggesting that delayed elongation is responsible for reduced protein levels for the remaining fraction of genes. All three single starvations lead to increased decoding times for a subset of the cognate "hungry" codons: CUU for -Leu, AUU and AUC for -Ile, and all of the Val codons, in a manner that is said to correspond largely to the particular tRNA isoacceptors that become deacylated, although this correspondence was not explained explicitly and might not be as simple as claimed. All three single starvations also evoke skewing of RPFs towards the 5' ends of many CDSs in a manner correlated with an enrichment within the early regions of the CDSs for one or more of the cognate codons that showed increased decoding times for -Ile (AUC codon) and -Val (GUU, GUC, and GUG), but not for -Leu-of which the latter was not accounted for. These last findings suggest that, at least for -Val and -Ile, delays in decoding N-terminal cognate codons cause elongating ribosomes to build-up early in the CDS. They go on to employ a peak calling algorithm to identify stalling sites in an unbiased way within the CDS, which are greatest in number for -Val, and find that Val codons are enriched in the A-sites (slightly) and adjacent 5' nucleotides (to a greater extent) for -Val starvation; and similarly for Ile codons in -Ile conditions, but not for -Leu starvation-again for unknown reasons. It's unclear why their called stalling sites have various other non-hungry codons present in the A sites with the cognate hungry codons being enriched further upstream, given that stalling should occur with the "hungry" cognate codon in the A site. The proteins showing down-regulation are enriched for stalling sites only in the case of the -Val starvation in the manner expected if stalling is contributing to reduced translation of the corresponding mRNA. It's unclear why this enrichment apparently does not extend to -Ile starvation which shows comparable skewing of RPFs towards the 5'ends, and this fact diminishes the claim that pausing generally contributes to reduced translation for genes with abundant hungry codons.<br /> All of the same analyses were carried out for the Double -Ile/-Leu and Triple starvations and yield unexpected results, particularly for the triple starvation wherein decoding times are increased only at Val codons, skewing of RPFs towards the 5' ends of CDSs is correlated only with an enrichment for Val codons within the early regions of the CDSs, and stall sites are enriched only for Val codons at nearly upstream sites, all consistent with the finding that only Val tRNAs become deacylated in the Triple regime. To explain why only Val tRNA charging is reduced despite the observed effective starvation for all three amino acids, they note first that stalling at Val codons is skewed towards the 5'ends of CDS for both -Val and triple starvations more so than observed for Ile or -Leu starvation, which they attribute to a greater frequency of Val codons vs Ile codons in the 5' ends of CDSs. As such, charged Val tRNAs are said to be consumed in translating the 5'ends of CDSs and the resulting stalling prevents ribosomes from reaching downstream Ile and Leu codons at the same frequencies and thus prevents deacylation of the cognate Ile and Leu tRNAs. It's unclear whether this explanation is adequate to explain the complete lack of Ile or Leu tRNA deacylation observed even when amino acid recycling by the proteasome is inhibited-a treatment shown to exacerbate deacylation of cognate tRNAs in the single amino acid starvations and of Val tRNA in the triple starvation. As such, the statement in the Abstract "Notably, we could show that isoleucine starvation-specific stalling largely diminished under triple starvation, likely due to early elongation bottlenecks at valine codons" might be too strong and the word "possibly" would be preferred over "likely". It's also unclear why the proteins that are down-regulated in the triple starvation are not significantly enriched for stalling sites (Fig. 5B) given that the degree of skewing is comparable or greater than for -Val. This last point seems to undermine their conclusion in the Abstract that "that many proteins downregulated under BCAA deprivation harbor stalling sites, suggesting that compromised elongation contributes to decreased protein output."<br /> In the case of the double -Ile/-Leu starvation, a related phenomenon occurs wherein decoding rates are decreased for only the AUU Ile codon and only the AAU Ile tRNA becomes deacylated; although in this case increased RPFs in the 5' ends are not correlated with enrichment for Ile or Leu codons and, although not presented, apparently stall sites are not associated with the Ile codon in the double starvation. In addition, stalling sites are not enriched in the proteins down-regulated by the double starvation. Moreover, because Ile codons are not enriched in the 5'ends of CDS, it doesn't seem possible to explain the selective deacylation of the single Ile tRNA observed in the double starvation by the same "bottleneck" mechanism proposed to explain selective deacylation of only Val tRNAs during the triple starvation. This is another reason for questioning their "bottleneck" mechanism.

Specific comments (some of which were mentioned above):

• The authors have treated cells with CHX in the Ribo-Seq experiments, which has been shown to cause artifacts in determining the locations of ribosome stalling in vivo owing to continued elongation in the presence of CHX (https://doi.org/10.1371/journal.pgen.1005732 ). The authors should comment on whether this artifact could be influencing some of their findings, particular the results in Fig. 5C where the hungry codons are often present upstream of the A sites of called stalling sites in the manner expected if elongation continued slowly following stalling in the presence of CHX.
• p. 12: "These starvation-specific DT and ribosome density modulations were also evident at the individual transcript level, as exemplified by Col1a1, Col1a2, Aars, and Mki67 which showed persistent Val-codon-specific ribosome density increases but lost Ile-codon-specific increases under triple starvation (Supplementary Figure 3A-D). " This conclusion is hard to visualize for any but Val codons. It would help to annotate the relevant peaks of interest for -Ile starvation with arrows.
• To better make the point that codon-specific stalling under BCAA starvation appears to be not driven by codon usage, rather than the analysis in Fig. 1H, wouldn't it be better to examine the correlation between increases in DT under the single amino acid starvation conditions and the codon frequencies across all codons?
• p. 13, entire paragraph beginning with "Our RNA-seq and Ribo-seq revealed a general activation of stress response pathways across all starvations..." It is difficult to glean any important conclusions from this lengthy analysis, and the results do not appear to be connected to the overall topic of the study. If there are important conclusions here that relate to the major findings then these connections should be made or noted later in the Discussion. If not, perhaps the analysis should be largely relegated to the Supplemental material.
• p. 15: "Together, these findings highlight that BCAA starvation triggers a combination of effects on initiation and elongation, with varying dynamics by amino acid starvation." I take issue with this statement as it appears that translation is reduced primarily at the initiation step for all conditions except -Ile. As noted above, these data are never menitioned in the DISCUSSION as to why only -Ile would show a marked elongation component to the inhibition whereas -Val gives the greatest amount of ribosome stalling.
• I cannot decipher Fig. 4D and more detail is required to indicate the identify of each column of data.
• In Fig. 4E, one cannot determine what the P values actually are, which should be provided in the legend to confirm statistical significance.
• It's difficult to understand how the -Leu condition and the Double starvation can produce polarized RPFs (Fig. 4A) without evidence of stalling at the cognate hungry codons (Fig. 4E), despite showing later in Fig. 5A that the numbers of stall sites are comparable in those cases to that found for -Ile.
• Fig. 5B: the P values should be given for all five columns, and it should be explained here or in the Discussion why the authors conclude that stalling is an important determinant for reduced translation when a significant correlation seems to exist only for the -Val condition and not even for the Triple condition.
• p. 17: "Of note, in cases where valine or isoleucine codons were present just upstream (rather than at) the stalling position, we noted a strong bias for GAG (E), GAA (E), GAU (D), GAC (D), AAG (K), CAG (Q), GUG (V) and GGA (G) (Val starvation) and AAC (N), GAC (D), CUG (L), GAG (E), GCC (A), CAG (Q), GAA (E) and AAG (K) (Ile starvation) at the stalling site (Supplementary Figure 7B)." The authors fail to explain why these codons would be present in the A sites at stalling sites rather than the hungry codons themselves, especially since it is the decoding times of the hungry codons that are increased according to Fig. 1A-E. As suggested above, is this a CHX artifact?
• Fig. 5D: P values for the significance, or lack thereof, of the different overlaps should be provided.
• p. 17: "Nonetheless, when we examined entire transcripts rather than single positions, many transcripts that exhibited isoleucine-related stalling under Ile starvation also stalled under triple starvation, but at different sites along the CDS (Figure 5E). This finding is particularly intriguing, as it suggests that while Ile-starvation-specific stalling sites may shift under triple starvation, the overall tendency of these transcripts to stall remains." The authors never come back to account for this unexpected result.
• It seems very difficult to reconcile the results in Fig. 5F with those in Fig. 4A, where similar polarities in RPFs are observed for -Ile and -Val in Fig, 4A but dramatically different distributions of stalling sites in Fig. 5F. More discussion of these discrepancies is required.
• p. 18: " These isoacceptor-specific patterns correlate largely with the particular subsets of leucine and isoleucine codons that stalled (Figure 1A)." This correlation needs to be addressed for each codon-anticodon pair for all of the codons showing stalling in Fig. 1A.
• p. 19: "For instance, in our double starvation condition, unchanged tRNA charging levels (Figure 6E) may result from a pronounced downregulation of global translation initiation, likely driven by the activation of stress responses (Figure 2), subsequently lowering the demand for charged tRNAs as it has been observed previously for Leu starvation 39. This seems at odds with the comparable down-regulation of protein synthesis for the Double starvation and -Leu and -Ile single starvations shown in Fig. 3C. Also, in the current study, Leu starvation does lower charging of certain Leu tRNAs.

Significance

The results here are significant in showing that starvation for a single amino acid does not lead to deacylation of all isoacceptors for that amino acid and in revealing that starvation for one amino acid can prevent deacylation of tRNAs for other amino acids, as shown most dramatically for the selective deacylation of only Val tRNAs in the triple BRCAA starvation condition. For the various reasons indicated above, however, I'm not convinced that their "bottleneck" mechanism is adequate to explain this phenomenon, especially in the case of the selective deacylation of Ile vs Leu tRNA in the Double starvation regime. It's also significant that deacylation leads to ribosome build-up near the 5'ends of CDS, which seems to be associated with an enrichment for the hungry codons in the case of Val and Ile starvation, but inexplicably, not for Leu or the Double starvations. This last discrepancy makes it hard to understand how the -Leu and Double starvations produce RPF buildups near the 5 ends of CDSs. In addition, the claim in the Discussion that "our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress" overstates the strength of evidence that the stalling events lead to substantial decreases in translational efficiencies for the affected mRNAs, as the stalling frequency and decreased protein output are significantly correlated only for the -Val starvation, and the data in Fig. 3 D-H suggest that the reductions in protein synthesis generally occur at the level of initiation, even for -Val starvation, with a contribution from slow elongation only for -Ile-which is in itself difficult to understand considering that stalling frequencies are highest in -Val. Thus, while many of the results are very intriguing and will be of considerable interest to the translation field, it is my opinion that a number of results have been overinterpreted and that important inconsistencies and complexities have been overlooked in concluding that a significant component of the translational inhibition arises from the increased decoding times at hungry codons during elongation and that the selective deacylation of Val tRNAs in the Triple starvation can be explained by the "bottleneck" mechanism. The complexities and limitations of the data and their intepretations should be discussed much more thoroughly in the Discussion, which currently is devoted mostly to other phenomena often of tangential importance to the current findings. A suitably revised manuscript would clearly state the limitations and caveats of the proposed mechanisms and consider other possible explanations as well.

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Referee #1

Evidence, reproducibility and clarity

This manuscript described the translational responses to single and combined BCAA shortages in mouse cell lines. Using Ribo-seq and RNA-seq analysis, the authors found selective ribosome pausing at codons that encode the depleted amino acids, where the pausing at valine codons was prominent at both a single and triple starvations whereas isoleucine codons showed pausing only under a single depletion. They analyzed the mechanisms of the unexpected selective pausing and proposed that the positional codon usage bias could shape the ribosome stalling and tRNA charging patterns across different amino acids. They also examined the stress responses and the changes in the protein expression levels under BCAA starvation.

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

Major comments

1. The abstract may need to be revised since it is hard to immediately catch the authors' main point. If the authors regard this work as a resource paper, the current version is fine. But it could be better to point out the positional codon usages the authors found, which is a strong point of the current manuscript.
2. Page 18 "Beyond these tRNA dynamics, our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress."<br /> This idea is interesting. To what extent the authors think this could be generalized? The authors may discuss whether they think their proposed model is specific to the different ribosome stalling patterns between valine and isoleucine codons or generalized to other codon combinations. For example, the positional codon usage bias will be different among different organisms, and are there any previous reports on ribosome behaviors that align with their model? Even if the authors think this model can be applied to BCAA starvation, would it be possible to explain the different isoleucine codon responses between single and double starvation? The authors may discuss why the ribosome stalling at isoleucine AUU and AUC codons was slightly attenuated under double starvation. And how about the different leucine codon responses among single, double, and triple starvations, although the pausing is not as strong as isoleucine and valine codons? Experimental validation using artificial reporters carrying biased sequences may also be considered.
3. Page 13 "Moreover, we noticed that DT changes extend beyond the ribosomal A-site, including the P-site, E-site, and even further positions (Supplementary Fig. 2A), consistent with other studies on single amino acid starvation 39 (Supplementary Fig. 2B-C)." Could the widespread DT changes be due to Ribo-DT pipeline they used or difficulties in offset determination? Indeed the authors showed that this feature was found in other datasets, but it seems that the datasets were processed and analyzed in the same way as their data. The original Ribo-DT paper (Gobet and Naef, 2022, Methods) also showed some widespread DT changes even from RNA-seq. Another analysis method like the codon subsequence abundant shift as a part of diricore analysis (Loayza-Puch et al., 2016, Nature) did not show that broad changed regions. The authors are encouraged to re-analyze the data sets using different methods.
4. Page 13 "Intriguingly, only two of the three isoleucine codons (AUU and AUC) showed increased DTs upon Ile starvation (p < 0.01), while just one leucine codon (CUU) exhibited a modest but significant DT increase (p < 0.01) under Leu starvation (Figure 1A-B, Supplementary Figure 2A)." How can the authors explain the different strengths of ribosome pausing at Ile codons under Ile and double starvation? The AUA codon did not show any pausing under either of the starvation conditions. Throughout the manuscript, the authors mainly describe the difference between amino acids but it is desirable to discuss the codon-level difference as well.
5. Page 13 "We examined the effects of single amino acid starvations (-Leu, -Ile and -Val), as well as combinations, including a double starvation of leucine and isoleucine (hereafter referred to as "double") and a starvation of leucine, isoleucine, and valine ("triple"), allowing us to identify potential non-additive effects." The different double starvations, isoleucine and valine, and leucine and valiene, will further support their hypothesis on the effects of the positional codon usage bias on ribosome pausing and tRNA charging patterns. Although this could be beyond the scope of the current manuscript, the authors are encouraged to provide a rationale for the chosen combination.

Minor comments

Page 16 "these results imply that BCAA deprivation lowers protein output through multiple pathways: a combination of reduced initiation, direct elongation blocks (stalling), and possibly an increased proteolysis" This conclusion is totally right but may be too general. Could the authors summarize BCAA-specific features of the events including reduced initiation, stalling, and proteolysis that all contribute to protein outputs? This is not well discussed in the latter sections including Discussion.

Significance

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

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Reply to the reviewers

Prior to the point-by-point response to the reviewer, we would like to sincerely thank all the peer reviewers for their overwhelmingly positive comments and helpful suggestions. The recommendations have undoubtedly improved our initial submission, and we have done our best to incorporate as many of the suggestions as possible.

Reviewer #1* (Evidence, reproducibility and clarity (Required)): *

*Jones et al. have submitted a manuscript detailing the role of Coenzyme A in the regulation of macrophage polarization. Overall, the manuscript is well designed, and the conclusions are well supported by the data. I find no major or minor deficiencies that need to be corrected. *

* Reviewer #1 (Significance (Required)): *

For decades the immunology community has boldly stated that mitochondrial metabolism not only provides the bioenergetics for cell expansion but also dictates cell fate. This has been especially true for fatty acid beta oxidation. Macrophage, T-cell and B-cell polarization have all been shown to require FAO for their polarization, but all based on one inhibitor. NONE of these observations hold up with more rigorous experimentation. The Divakaruni group has previously suggested that intracellular CoA homeostasis was the driver of macrophage differentiation as they could reverse the inhibitory effects by providing heroic levels of CoA extracellularly. Here, they have clarified the role of CoA. Intracellular CoA does not affect macrophage polarization/differentiation. This was done with cleaver manipulation of the CoA pools. Rather, extracellular CoA can act as a weak TLR4 ligand. This work nicely clarifies their previous work and further demonstrates a role for this metabolite as an endogenous activator of type 1 macrophages.

We are thrilled by the positive comments about our work, and we are grateful the reviewer found our submission to be clarifying for the field and significant in the larger context of immunometabolism research.

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

*This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough. There are two major issues that need to be addressed: *

We thank the reviewer for their positive comments regarding the quality and clarity of our work.

1. *Previous work has shown the following pathway: LPS>IL10>STAT3>IL4Ra>>>increased responsiveness to IL4/IL13 and increased expression of M2 associated markers (please note, this pathway does not apply to Arg1, often erroneously associated with M2 macrophages - LPS induces Arg1 far more than IL4 and this is independent of the STAT6 pathway - Dichtl et al., Science Advances and El Kasmi et al. Nature Immunology, and others). This pathway was first described in Lang et al. 2002 J. Immunol. Subsequently, other groups showed IL6 (Jens Brüning) and OSM (Carl Richards) do the same thing, which is not surprising given that they are STAT3 activators. Thus, Il4ra is a STAT3 target gene; this also makes sense in the kinetic evolution of macrophages from inflammatory to tissue reparative (if they survive). In my view, the authors have most likely found the same pathway. In Jones, expression of the IL4Ra was not quantified. Thus, the pathway described above needs to be accounted for. It may not apply here but seems the easiest explanation of the data. *

This is an excellent and important experiment suggested by the reviewer, and we address this in our revised Supplemental Figure 5. To determine whether the effect of CoA can be explained simply by a STAT3-mediated effect on the IL-4 receptor, we treated cells with the well-characterized STAT3 inhibitor Napabucasin and measured whether CoA could enhance the macrophage IL-4 response. Two results are clear from the data:

• Treatment with Napabucasin reduced the expression of IL-4-linked cell surface markers and the IL-4 target gene Ccl8. This serves as an important control consistent with the Il4ra gene being a STAT3 target that increases IL-4 responsiveness.
• Despite STAT3 inhibition and a reduced IL-4 response, CoA provision still augmented the IL-4-induced expression of Ccl8 and the percentage of CD206+/CD301+ cells, indicating a STAT3-independent mechanism. The result aligns with our ATAC-Seq data in Figure 6 that shows broad changes in chromatin accessibility that cannot be completely explained by expression-level changes in the IL-4 receptor.

*Can the authors come up with a meaningful in vivo experiment to corroborate their data. Pantothenate-deficient mice have many phenotypes (not fully explored at all - PMID 31918006, for example) and pantothenate metabolism can be manipulated in different ways. Obviously, a complex in vivo experiment is not feasible here. But this should be discussed. What happens in human macrophages, where "polarization" is a completely different beast? *

We thank the reviewer for these thoughtful comments, and address the questions regarding in vivo proof-of-concept and polarization of human macrophages separately:

• Regarding the question of whether CoA can enhance the phenotype of IL-4-activated human macrophages, this is an excellent suggestion and we have added the data as Figure 1h. Indeed, Coenzyme A dramatically amplifies expression of the human IL-4 responsive genes CCL17, TGM2, and PDCD1LG2 (similarly to mouse macrophages). The result substantially expands the significance of our work by showing the phenotype is reproducible in both mouse and human macrophages – unlike many immunometabolic phenotypes – and we thank the reviewer again for suggesting this experiment.
• With respect to an in vivo experiment to corroborate our data, we entirely agree with the reviewer regarding both the importance, but also the difficulty in interpretation, of an experiment genetically manipulating CoA synthesis in vivo. As they have suggested, we raise these issues in the discussion on Lines 370-377 of the revised manuscript. Here, we note the following points:
• Wherever possible/appropriate (e.g. Figures 1g, 3f&g, 5g&h), we have sought to corroborate our in vitro findings with in vivo/ex vivo proofs-of-concept.
• Studying immune phenotypes in pantothenate-deficient mice would be an exciting experiment in principle, but difficult to interpret if conducted. As noted by the reviewer in the work from Drs. Rock and Jackowski, knockout of one of four isoforms of pantothenate kinase (PANK) shows mild phenotypes consistent with compensation across isoforms for CoA provision. Global double knockout of PANK1 and PANK2, however, is postnatally lethal. Regardless, a tissue-specific double knockout in myeloid cells is unlikely to show a phenotype given our results showing that manipulating intracellular CoA levels in BMDMs does not alter the IL-4 response (Figs. 2h-j).
• Given the established role of CoA in postnatal development, it would be difficult to attribute any immunologic phenotypes in genetically modified mice to direct effects of CoA as a metabolic DAMP as opposed to indirect effects from a chronically altered immune system.

Reviewer #2 (Significance (Required)): *This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough.

*

We reiterate our gratitude for the comments on the quality and clarity of our work.

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

Summary: In this manuscript on enhancement of mIL-4 polarization by exogenous CoA, the authors follow up on their previous studies that had shown a correlation between Etomoxir-driven block in mIL-4 and a reduction of intracellular CoA levels. The results obtained (lack of enhancement of IL-4-induced changes in oxidative phosphorylation and glycolysis; lack of impact of pharmacological decrease/increase of intracellular CoA levels) led them to discard their initial hypothesis. Instead, the presence of a proinflammatory gene signature in macrophages treated with IL-4+CoA triggered experiments testing the involvement of TLR-Myd88 signaling and the identification of CoA as a weak agonist for TLR4 (which is consistent with a preprint manuscript posted in 2022 by others and showing induction of proinflammatory gene express in a TLR2/4-dependent manner).

• Significance: Overall, these results are novel and interesting, although the use of yeast-derived CoA preparations raises a question about the contribution of contaminants that is only partially controlled by data obtained with a synthetic CoA. Regarding a biological role for CoA in macrophage biology in vivo, the authors propose that CoA may act as a DAMP upon release from dying/dead cells and thereby modify transcriptional polarization of m(IL-4). I have several comments related to specific experimental conditions and interpretation that should be addressed. Most importantly, the key findings of the manuscript should be demonstrated using synthetic CoA as described in comment #5. *

We are heartened that the reviewer found our initial submission to be novel and interesting, and are grateful for their suggestions to reinforce our existing data with more studies comparing yeast-derived and synthetically-derived Coenzyme A. We have done our best to address each of the individual questions below:

Major comments:

1. *Increasing/decreasing intracellular CoA levels does not alter IL-4-induced CD206 expression (Fig. 2i/j. However, the impact of CoA addition to mIL-4 is stronger for Ccl8 and Mgl2 mRNA (Fig. 1a) than for the CD206+ cell fraction (Fig. 1d). Therefore, it would be better (higher sensitivity) to include expression of these genes as readout after CPCA/PZ-2891 treatment. *

This is a helpful suggestion, and we have now conducted gene expression studies to complement our flow cytometry and mass spectrometry studies while manipulating the intracellular CoA pool. In line with our previous work, neither CPCA (which decreases intracellular free CoA) or PZ-2891 (which increases intracellular free CoA) meaningfully alter expression of IL-4-linked genes including Ccl8 or Mgl2. In fact, the only (statistically insignificant) trend refutes the hypothesis, as gene expression with CPCA leads to marginally increased gene expression. These results are now included in Supplemental Figure S2f. We thank the reviewer for this helpful suggestion, as it has strengthened our conclusion that intracellular CoA levels do not adjust the macrophage IL-4 response.

• The CoA-induced proinflammatory gene expression in Fig. 3c is relatively weak (e.g. compared to LPS). The authors use CoA throughout the manuscript at a concentration of 1 mM, and we do not know how much of it is required to cause an effect at all. Therefore, dose-response curves for the stimulation of macrophages with titrated amounts of CoA should be provided. In addition, *

We thank the reviewer for bringing up this point so we could clarify and add to our existing data. We should note that Supplemental Figures 1b&c of our previous submission (and resubmitted manuscript) detail a concentration-response curve showing that at little as 62.5 mM CoA – the lowest concentration tested – was sufficient to enhance IL-4 cell surface marker expression.

However, it is an excellent suggestion as the reviewer notes, to conduct a similar concentration-response to determine if this lines up with CoA inducing a pro-inflammatory response. The full data set is presented in the answer to reviewer question 4 (comparing CoA purchased from Sigma vs. Avanti Polar Lipids), though we now show in Supplemental Figure S3 that 62.5 mM CoA is sufficient to elicit a pro-inflammatory response. Though it is indeed a weak effect as noted by the reviewer, our data suggest that the relatively mild stimulus is crucial for the effect. Given the results with the TLR3 agonist Poly I:C (Figure 5), which engages a Type 1 interferon response, strong TLR4 agonists that engage the TRIF/Type I interferon arm of the TLR4 response are likely to blunt or block the IL-4 response.

• Related question: we are informed that the concentration of CoA in the mitochondrial matrix is 5mM, whereas cytosol contains 100µM. For CoA to act as DAMP, I would like to know the concentration of it in supernatants of cell cultures (live vs. dying/dead cells) and from tissues. *

This is an important point brought up by the reviewer, and we agree that the implicit issue raised (i.e. “do the concentrations of CoA required to see an effect reconcile with a physiological role as a DAMP?”) should be more thoroughly addressed in the manuscript. Tissue concentrations of free CoA (in ng/mg tissue) are well established for mice and range from >100 nmol/g tissue (liver, heart, brown adipose tissue) to Nonetheless, the reviewer’s larger point is very well reasoned, and we address it in the following ways in the discussion on __Lines 378-391. __

• In light of the reviewer’s comment, we now mention specific instances in the discussion where CoA acting as a DAMP may reasonably play a physiological role (e.g. acetaminophen-induced acute liver injury or other forms of sterile liver injury given that DAMPs are known to be important factors and liver tissue contains relatively high concentrations of CoA).
• Although cytoplasmic concentrations of CoA may only be 50-100 mM, our work establishes a framework for how ubiquitous metabolic co-factors can activate pattern recognition receptors. Put another way, although CoA itself may not be a physiologically relevant DAMP, discovering this pathway could inform how other nucleotide or nucleoside analogs (e.g. adenine- or adenosine-containing molecules present at millimolar concentrations) exert their effects on innate immunity.
• Our newly obtained data with HMDMs (Figure 1h) shows that the CoA response in human macrophages – boosting IL-4-linked gene expression by 10-100X – may be much stronger than the 1.5-5X effect observed in mouse BMDMs. As such, it is exciting to speculate that CoA may have a more potent effect on the IL-4 response in humans relative to mice. We trust the reviewer understands the limitations of obtaining human macrophages that preclude conducting a thorough concentration-response analysis given the restrictions of a manuscript revision.

• It is very good that the authors validate the findings obtained using the yeast-derived CoA with the synthetic molecule. It is very conceivable that the 15% contaminating substances in the yeast CoA could be causing the observed changes in m(IL-4). The fact that synthetic CoA has higher activity in proinflammatory gene expression by BMM (Suppl. Fig. S3) is reassuring, however, it raises the question why this is the case. One possibility is that the concentrations of the different CoA preps cannot directly be compared. Therefore, dose response curves should also be provided for synthetic CoA. *

This is an astute observation by the reviewer and we thank them for reading our manuscript with such detailed attention to pick this up. We are reassured that the reviewer shares our interpretation that the effect of CoA is not due to a contaminating TLR4 agonist in the yeast-derived preparation (from Sigma-Aldrich; ~85% pure) given a negative Limulus Test (Supplemental Figure S4b). Moreover, the synthetically-derived preparation (from Avanti Polar Lipids; ~99% pure) yields a stronger TLR4 response.

An exploration of the follow-on question regarding why the effect is greater than 15% is presented below. These experiments have been added to Supplemental Figure S4c&d. The summary of our data suggests the individual concentrations indeed cannot be compared – matched concentrations of synthetic Avanti CoA have greater than a 15% effect than yeast-derived Sigma CoA. There are likely multiple factors that could explain this, some of which are listed below.

• The physiological effect of a TLR agonist need not be linear with its concentration, as demonstrated by the sigmoidal calibration curves for the TLR-expressing HEK-blue cells (Figures 4b, S4a). This likely does not explain the dramatic difference between the two CoA preparations but is worth noting.
• While we have determined that the 15% contaminating substances in the yeast-derived CoA are not causing the observed changes in the IL-4 response, it is formally possible that there are contaminating substances blunting the pro-inflammatory response and therefore limiting the effect of CoA purchased from Sigma-Aldrich relative to that from Avanti Polar Lipids. Importantly, however, our data in response to Reviewer Question #5 show there is no difference in amplifying the IL-4 response between the yeast- and synthetically-derived CoA.

• The difference in activity of yeast and synth. CoA could also be caused by the additional biologically active molecules in the yeast CoA. Therefore, it is important to show that the key findings in the paper (enhancement of m(IL-4) associated gene expression and CD206+ upregulation in vitro and in vivo) are also induced by synth. CoA. This is even more important in the context of the Myd88-independence of CD206+ upregulation in BMM treated with CoA (Suppl. Fig. S4). The experiment should be repeated with synth. CoA. If the enhancement of CD206+ cells induced by CoA is indeed unchanged in Myd88 KO BMM, then the title of the manuscript "CoA enhances alternative macrophage activation via Myd88" would not be supported by the data and needed to be changed. Activation of the TLR4 reporter cell line should also be tested using the synth. CoA molecule.*

We are grateful for this suggestion by the reviewer to further cement the idea that our observation of CoA enhancing the macrophage IL-4 response was not due to a contaminant in the Sigma-Aldrich CoA preparation. The reviewer makes a few points in this question which we address individually here.

• The suggestion to confirm that the CoA-induced enhancement of M(IL-4) is not due to a contaminating substance in the Sigma-Aldrich CoA is excellent and necessary. Here we show that synthetically derived CoA (99% pure, purchased from Avanti Polar Lipids) quantitatively reproduces the effect from yeast-derived CoA from Sigma-Aldrich in Supplemental Figure S4e. The response is noteworthy because synthetic CoA has profoundly stronger pro-inflammatory response than yeast-derived CoA, yet both have a similar effect on augmenting M(IL-4). This suggests that any appropriate pro-inflammatory response – irrespective of the relative strength or weakness – is sufficient to maximize the effect. This can also be observed with the range of MyD88-linked TLR agonists used in Figures 5 and S6a.
• Similarly, we also conducted experiments to show that the effect of synthetic CoA on M(IL-4) is independent of MyD88 similarly to yeast-derived CoA. These data are present in Supplemental Figure S6b&c. Here again, we should note that the effect of synthetic CoA is quantitatively similar to the effect of yeast CoA and Imiquimod (Supplemental Figure S6a).
• Activation of the TLR4 reporter cell line is available in Supplemental Figure S4c.
• Regarding the title of the manuscript, we acknowledge that we struggled a bit with how to frame our findings. Importantly, our findings support a model where (i) CoA provision enhances the IL-4 response not via metabolic changes but rather by acting as a mild pro-inflammatory stimulus, and (ii) MyD88 signaling augments the IL-4 response. We should also note that our findings simply show that CoA does not exclusively enhance the IL-4 response via MyD88 signaling, and there may be other redundant pathways (similarly to MyD88 agonist imiquimod but unlike the MyD88 agonists Pam3-CSK4 and low concentrations of LPS). We are open to working journal editors to strike the right balance of scientific accuracy and representation of the work when deciding on a final title.

• The results from the tumor model in Fig. 5 are presented to show a stronger tumor-promoting effect of m(IL-4) stimulated with Pam3. However, the variability of the data is high and 2 out of 6 mice in the +Pam3 group appear to actually have a lower tumor weight than the control mice. Therefore, these data are quite superficial and preliminary, and would benefit from a replicate experiment. Furthermore, for the evaluation of CoA as a biologically relevant DAMP, it would be important to know whether CoA-treated m(IL-4) show the same tumor-promoting effect in vivo as Pam3. *

We thank the reviewer for their comment, and agree that our in vivo work is indeed preliminary. Our goal with this report was to focus on the initial discovery of this molecular pathway and its first, broad characterization using a range of techniques (e.g. in vivo outcomes, ATAC-Seq, etc.), many of which can spur more detailed follow-up studies for future papers. As detailed in the manuscript discussion (Lines 415-419), future work beyond our initial discovery is warranted to thoroughly explore the physiological outcomes of CoA as a metabolic DAMP in relevant model systems such as acute liver injury. As an initial proof-of-concept to show that MyD88 signaling can enhance alternative activation, however, we believe our two discrete experiments (sterile inflammation and tumor formation) are sufficient to indicate the phenotype is likely relevant in animal models. In vivo syngeneic tumor models display natural variability in tumor size due to differences in implantation efficiency, host immune responses, and tumor-intrinsic growth kinetics. Nonetheless, our statistical analysis demonstrates that, with high confidence, that the observed differences are reproducible and not attributable to random variation.

Minor comments:

1. • Fig. 1b: where the gates for CD206/CD301 set based on isotype control stainings? *

We thank the reviewer for pointing out this oversight in our methods. The gates were indeed set on isotype control stains, and this is now mentioned in Lines 519-521 of the revised manuscript.

The formatting not cohesive m(IL-4) vs. M(IL-4)

Again, this is an embarrassing oversight on our part and we have done our very best to copy edit the piece and remove any inconsistencies and errors.

*Methods: primer sequences are not shown. They should be provided. *

We thank the reviewer for pointing this out, and now include all primer sequences used in Supplemental Table 1 of the revised manuscript.

Description of flowcytometry (L/D staining after surface? No washing steps after addition of L/D staining)

We thank the reviewer for pointing out another oversight in our methods, and have provided a more detailed description of the flow cytometric analysis in Lines 509-521 of the revised manuscript.

Statistics: the methods section states that variability is indicated by SD, but the Figure legends always mention SEM. Please correct.

We are grateful for the reviewer’s helpful attention to detail, and have corrected the methods to line up with the figure legends.

*A multitude of typos and editorial inconsistencies (e.g. spelling of m(IL-4), punctation and capitalization) should be corrected/streamlined. *

We are grateful for the reviewer’s helpful attention to detail, and have done our best to copy edit the manuscript prior to resubmission.

Reviewer #3 (Significance (Required)):

strengths: I like that the authors follow up their previous work on Etomoxir and CoA, now finding again an unexpected twist in how the effect on m(IL-4) is brought about. This makes the story more complicated, but is important to get to a more precise and realistic understanding of metabolic and transcriptomic regulation and how they are interconnected (or not). In addition, the use of a relatively broad set of methods including ATACseq and mass spectrometry is a strength.

weakness: the use of the not very pure yeast derived CoA prep, which is controlled for induction of proinflammatory cytokines by one experiment with synth. CoA. This validation needs to be expanded (see comments above) to substantiate the main message of the manuscript.

The scope of the manuscript is quite focussed on the mechanism of CoA enhanced m(IL-4). The finding that CoA appears not to act by changing intracellular macrophage metabolism but instead after its release by activation TLR4 widens the scope and suggests a new function for CoA as DAMP. This aspect would need to be further substantiated to be convincing.

Audience: scientists working at the intersection between metabolism and innate immunity will be interested in the results.

We thank the reviewer for their kind comments regarding the precision, credibility, and breadth of our manuscript. We hope they find our revised manuscript an improvement over our previous submission regarding both the new experiments and modified text. The comments have undoubtedly improved our manuscript and we are grateful to the reviewer for the considerable effort they put into reading our submission.

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript on enhancement of mIL-4 polarization by exogenous CoA, the authors follow up on their previous studies that had shown a correlation between Etomoxir-driven block in mIL-4 and a reduction of intracellular CoA levels. The results obtained (lack of enhancement of IL-4-induced changes in oxidative phosphorylation and glycolysis; lack of impact of pharmacological decrease/increase of intracellular CoA levels) led them to discard their initial hypothesis. Instead, the presence of a proinflammatory gene signature in macrophages treated with IL-4+CoA triggered experiments testing the involvement of TLR-Myd88 signaling and the identification of CoA as a weak agonist for TLR4 (which is consistent with a preprint manuscript posted in 2022 by others and showing induction of proinflammatory gene express in a TLR2/4-dependent manner).

Significance:

Overall, these results are novel and interesting, although the use of yeast-derived CoA preparations raises a question about the contribution of contaminants that is only partially controlled by data obtained with a synthetic CoA. Regarding a biological role for CoA in macrophage biology in vivo, the authors propose that CoA may act as a DAMP upon release from dying/dead cells and thereby modify transcriptional polarization of m(IL-4). I have several comments related to specific experimental conditions and interpretation that should be addressed. Most importantly, the key findings of the manuscript should be demonstrated using synthetic CoA as described in comment #5.

Major comments:

1. Increasing/decreasing intracellular CoA levels does not alter IL-4-induced CD206 expression (Fig. 2i/j. However, the impact of CoA addition to mIL-4 is stronger for Ccl8 and Mgl2 mRNA (Fig. 1a) than for the CD206+ cell fraction (Fig. 1d). Therefore, it would be better (higher sensitivity) to include expression of these genes as readout after CPCA/PZ-2891 treatment.
2. The CoA-induced proinflammatory gene expression in Fig. 3c is relatively weak (e.g. compared to LPS). The authors use CoA throughout the manuscript at a concentration of 1 mM, and we do not know how much of it is required to cause an effect at all. Therefore, dose-response curves for the stimulation of macrophages with titrated amounts of CoA should be provided. In addition,
3. Related question: we are informed that the concentration of CoA in the mitochondrial matrix is 5mM, whereas cytosol contains 100µM. For CoA to act as DAMP, I would like to know the concentration of it in supernatants of cell cultures (live vs. dying/dead cells) and from tissues.
4. It is very good that the authors validate the findings obtained using the yeast-derived CoA with the synthetic molecule. It is very conceivable that the 15% contaminating substances in the yeast CoA could be causing the observed changes in m(IL-4). The fact that synthetic CoA has higher activity in proinflammatory gene expression by BMM (Suppl. Fig. S3) is reassuring, however, it raises the question why this is the case. One possibility is that the concentrations of the different CoA preps cannot directly be compared. Therefore, dose response curves should also be provided for synthetic CoA.
5. The difference in activity of yeast and synth. CoA could also be caused by the additional biologically active molecules in the yeast CoA. Therefore, it is important to show that the key findings in the paper (enhancement of m(IL-4) associated gene expression and CD206+ upregulation in vitro and in vivo) are also induced by synth. CoA. This is even more important in the context of the Myd88-independence of CD206+ upregulation in BMM treated with CoA (Suppl. Fig. S4). The experiment should be repeated with synth. CoA. If the enhancement of CD206+ cells induced by CoA is indeed unchanged in Myd88 KO BMM, then the title of the manuscript "CoA enhances alternative macrophage activation via Myd88" would not be supported by the data and needed to be changed. Activation of the TLR4 reporter cell line should also be tested using the synth. CoA molecule.
6. The results from the tumor model in Fig. 5 are presented to show a stronger tumor-promoting effect of m(IL-4) stimulated with Pam3. However, the variability of the data is high and 2 out of 6 mice in the +Pam3 group appear to actually have a lower tumor weight than the control mice. Therefore, these data are quite superficial and preliminary, and would benefit from a replicate experiment. Furthermore, for the evaluation of CoA as a biologically relevant DAMP, it would be important to know whether CoA-treated m(IL-4) show the same tumor-promoting effect in vivo as Pam3.

Minor comments:

1. Fig. 1b: where the gates for CD206/CD301 set based on isotype control stainings?
2. The formatting not cohesive m(IL-4) vs. M(IL-4)
3. Methods: primer sequences are not shown. They should be provided.
4. Description of flowcytometry (L/D staining after surface? No washing steps after addition of L/D staining)
5. Statistics: the methods section states that variability is indicated by SD, but the Figure legends always mention SEM. Please correct.
6. A multitude of typos and editorial inconsistencies (e.g. spelling of m(IL-4), punctation and capitalization) should be corrected/streamlined.

Significance

Strengths: I like that the authors follow up their previous work on Etomoxir and CoA, now finding again an unexpected twist in how the effect on m(IL-4) is brought about. This makes the story more complicated, but is important to get to a more precise and realistic understanding of metabolic and transcriptomic regulation and how they are interconnected (or not). In addition, the use of a relatively broad set of methods including ATACseq and mass spectrometry is a strength.

Weakness: the use of the not very pure yeast derived CoA prep, which is controlled for induction of proinflammatory cytokines by one experiment with synth. CoA. This validation needs to be expanded (see comments above) to substantiate the main message of the manuscript.

The scope of the manuscript is quite focussed on the mechanism of CoA enhanced m(IL-4). The finding that CoA appears not to act by changing intracellular macrophage metabolism but instead after its release by activation TLR4 widens the scope and suggests a new function for CoA as DAMP. This aspect would need to be further substantiated to be convincing.

Audience: scientists working at the intersection between metabolism and innate immunity will be interested in the results.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough. There are two major issues that need to be addressed:

1. Previous work has shown the following pathway: LPS>IL10>STAT3>IL4Ra>>>increased responsiveness to IL4/IL13 and increased expression of M2 associated markers (please note, this pathway does not apply to Arg1, often erroneously associated with M2 macrophages - LPS induces Arg1 far more than IL4 and this is independent of the STAT6 pathway - Dichtl et al., Science Advances and El Kasmi et al. Nature Immunology, and others). This pathway was first described in Lang et al. 2002 J. Immunol. Subsequently, other groups showed IL6 (Jens Brüning) and OSM (Carl Richards) do the same thing, which is not surprising given that they are STAT3 activators. Thus, Il4ra is a STAT3 target gene; this also makes sense in the kinetic evolution of macrophages from inflammatory to tissue reparative (if they survive). In my view, the authors have most likely found the same pathway. In Jones, expression of the IL4Ra was not quantified. Thus, the pathway described above needs to be accounted for. It may not apply here but seems the easiest explanation of the data.
2. Can the authors come up with a meaningful in vivo experiment to corroborate their data. Pantothenate-deficient mice have many phenotypes (not fully explored at all - PMID 31918006, for example) and pantothenate metabolism can be manipulated in different ways. Obviously, a complex in vivo experiment is not feasible here. But this should be discussed. What happens in human macrophages, where "polarization" is a completely different beast?

Significance

This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough.

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

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

Jones et al. have submitted a manuscript detailing the role of Coenzyme A in the regulation of macrophage polarization. Overall, the manuscript is well designed, and the conclusions are well supported by the data. I find no major or minor deficiencies that need to be corrected.

Significance

For decades the immunology community has boldly stated that mitochondrial metabolism not only provides the bioenergetics for cell expansion but also dictates cell fate. This has been especially true for fatty acid beta oxidation. Macrophage, T-cell and B-cell polarization have all been shown to require FAO for their polarization, but all based on one inhibitor. NONE of these observations hold up with more rigorous experimentation. The Divakaruni group has previously suggested that intracellular CoA homeostasis was the driver of macrophage differentiation as they could reverse the inhibitory effects by providing heroic levels of CoA extracellularly. Here, they have clarified the role of CoA. Intracellular CoA does not affect macrophage polarization/differentiation. This was done with cleaver manipulation of the CoA pools. Rather, extracellular CoA can act as a weak TLR4 ligand. This work nicely clarifies their previous work and further demonstrates a role for this metabolite as an endogenous activator of type 1 macrophages.

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

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Reply to the reviewers

Manuscript number: RC-2025-02922

Corresponding author(s): Christian Specht

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1. General Statements [optional]

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We thank the reviewers for their thorough and constructive evaluation of our work. We have revised the manuscript carefully and addressed all the criticisms raised, in particular the issues mentioned by several of the reviewers (see point-by-point response below). We have also added a number of explanations in the text for the sake of clarity, while trying to keep the manuscript as concise as possible.

• *

In our view, the novelty of our research is two-fold. From a neurobiological point of view, we provide conclusive evidence for the existence of glycine receptors (GlyRs) at inhibitory synapses in various brain regions including the hippocampus, dentate gyrus and sub-regions of the striatum. This solves several open questions and has fundamental implications for our understanding of the organisation and function of inhibitory synapses in the telencephalon. Secondly, our study makes use of the unique sensitivity of single molecule localisation microscopy (SMLM) to identify low protein copy numbers. This is a new way to think about SMLM as it goes beyond a mere structural characterisation and towards a quantitative assessment of synaptic protein assemblies.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

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

In this manuscript, the authors investigate the nanoscopic distribution of glycine receptor subunits in the hippocampus, dorsal striatum, and ventral striatum of the mouse brain using single-molecule localization microscopy (SMLM). They demonstrate that only a small number of glycine receptors are localized at hippocampal inhibitory synapses. Using dual-color SMLM, they further show that clusters of glycine receptors are predominantly localized within gephyrin-positive synapses. A comparison between the dorsal and ventral striatum reveals that the ventral striatum contains approximately eight times more glycine receptors and this finding is consistent with electrophysiological data on postsynaptic inhibitory currents. Finally, using cultured hippocampal neurons, they examine the differential synaptic localization of glycine receptor subunits (α1, α2, and β). This study is significant as it provides insights into the nanoscopic localization patterns of glycine receptors in brain regions where this protein is expressed at low levels. Additionally, the study demonstrates the different localization patterns of GlyR in distinct striatal regions and its physiological relevance using SMLM and electrophysiological experiments. However, several concerns should be addressed.

The following are specific comments:

1. Colocalization analysis in Figure 1A. The colocalization between Sylite and mEos-GlyRβ appears to be quite low. It is essential to assess whether the observed colocalization is not due to random overlap. The authors should consider quantifying colocalization using statistical methods, such as a pixel shift analysis, to determine whether colocalization frequencies remain similar after artificially displacing one of the channels. *Following the suggestion of reviewer 1, we re-analysed CA3 images of Glrbeos/eos hippocampal slices by applying a pixel-shift type of control, in which the Sylite channel (in far red) was horizontally flipped relative to the mEos4b-GlyRβ channel (in green, see Methods). As expected, the number of mEos4b-GlyRβ detections per gephyrin cluster was markedly reduced compared to the original analysis (revised__ Fig. 1B__), confirming that the synaptic mEos4b detections exceed chance levels (see page 5). *

Inconsistency between Figure 3A and 3B. While Figure 3B indicates an ~8-fold difference in the number of mEos4b-GlyRβ detections per synapse between the dorsal and ventral striatum, Figure 3A does not appear to show a pronounced difference in the localization of mEos4b-GlyRβ on Sylite puncta between these two regions. If the images presented in Figure 3A are not representative, the authors should consider replacing them with more representative examples or providing an expanded images with multiple representative examples. Alternatively, if this inconsistency can be explained by differences in spot density within clusters, the authors should explain that.

*The pointillist images in Fig. 3A are essentially binary (red-black). Therefore, the density of detections at synapses cannot be easily judged by eye. For clarity, the original images in Fig. 3A have been replaced with two other examples that better reflect the different detection numbers in the dorsal and ventral striatum. *

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Quantification in Figure 5. It is recommended that the authors provide quantitative data on cluster formation and colocalization with Sylite puncta in Figure 5 to support their qualitative observations.

*This is an important point that was also raised by the other reviewers. We have performed additional experiments to increase the data volume for analysis. For quantification, we used two approaches. First, we counted the percentage of infected cells in which synaptic localisation of the recombinant receptor subunit was observed (Fig. 5C). We found that mEos4b-GlyRa1 consistently localises at synapses, indicating that all cells express endogenous GlyRb. When neurons were infected with mEos4b-GlyRb, fewer cells had synaptic clusters, meaning that indeed, GlyR alpha subunits are the limiting factor for synaptic targeting. In cultures infected with mEos4b-GlyRa2, only very few neurons displayed synaptic localisation (as judged by epifluorescence imaging). We think this shows that GlyRa2 is less capable of forming heteromeric complexes than GlyRa1, in line with our previous interpretation (see pp. 9-10, 13). *

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Secondly, we quantified the total intensity of each subunit at gephyrin-positive domains, both in infected neurons as well as non-infected control cultures (Fig. 5D). We observed that mEos4b-GlyRa1 intensity at gephyrin puncta was higher than that of the other subunits, again pointing to efficient synaptic targeting of GlyRa1. Gephyrin cluster intensities (Sylite labelling) were not significantly different in GlyRb and GlyRa2 expressing neurons compared to the uninfected control, indicating that the lentiviral expression of recombinant subunits does not fundamentally alter the size of mixed inhibitory synapses in hippocampal neurons. Interestingly, gephyrin levels were slightly higher in hippocampal neurons expressing mEos4b-GlyRa1. In our view, this comes from an enhanced expression and synaptic targeting of mEos4b-GlyRa1 heteromers with endogenous GlyRb, pointing to a structural role of GlyRa1/b in hippocampal synapses (pp. 10, 13).

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The new data and analyses have been described and illustrated in the relevant sections of the manuscript.

Potential for pseudo replication. It's not clear whether they're performing stats tests across biological replica, images, or even synapses. They often quote mean +/- SEM with n = 1000s, and so does that mean they're doing tests on those 1000s? Need to clarify.

All experiments were repeated at least twice to ensure reproducibility (N independent experiments). Statistical tests were performed on pooled data across the biological replicates; n denotes the number of data points used for testing (e.g., number of synaptic clusters, detections, cells, as specified in each case). We have systematically given these numbers in the revised manuscript (n, N, and other experimental parameters such as the number of animals used, coverslips, images or cells). Data are generally given as mean +/- SEM or as mean +/- SD as indicated.

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Does mEoS effect expression levels or function of the protein? Can't see any experiments done to confirm this. Could suggest WB on homogenate, or mass spec?

The Glrbeos/eos knock-in mouse line has been characterised previously and does not to display any ultrastructural or functional deficits at inhibitory synapses (Maynard et al. 2021 eLife). GlyRβ expression and glycine-evoked responses were not significantly different to those of the wild-type. The synaptic localisation of mEos4b-GlyRb in KI animals demonstrates correct assembly of heteromeric GlyRs and synaptic targeting. Accordingly, the animals do not display any obvious phenotype. We have clarified this in the manuscript (p. 4). In the case of cultured neurons, long-term expression of fluorescent receptor subunits with lentivirus has proven ideal to achieve efficient synaptic targeting. The low and continuous supply of recombinant receptors ensures assembly with endogenous subunits to form heteropentameric receptor complexes (e.g. [Patrizio et al. 2017 Sci Rep]). In the present study, lentivirus infection did not induce any obvious differences in the number or size of inhibitory synapses compared to control neurons, as judged by Sylite labelling of synaptic gephyrin puncta (new__ Fig. 5D__).

Quantification of protein numbers is challenging with SMLM. Issues include i) some of FP not correctly folded/mature, and ii) dependence of localisation rate on instrument, excitation/illumination intensities, and also the thresholds used in analysis. Can the authors compare with another protein that has known expression levels- e.g. PSD95? This is quite an ask, but if they could show copy number of something known to compare with, it would be useful.

We agree that absolute quantification with SMLM is challenging, since the number of detections depends on fluorophore maturation, photophysics, imaging conditions, and analysis thresholds (discussed in Patrizio & Specht 2016, Neurophotonics). For this reason, only very few datasets provide reliable copy numbers, even for well-studied proteins such as PSD-95. One notable exception is the study by Maynard et al. (eLife 2021) that quantified endogenous GlyRb-containing receptors in spinal cord synapses using SMLM combined with correlative electron microscopy. The strength of this work was the use of a KI mouse strain, which ensures that mEos4b-GlyRb expression follows intrinsic regional and temporal profiles. The authors reported a stereotypic density of ~2,000 GlyRs/µm² at synapses, corresponding to ~120 receptors per synapse in the dorsal horn and ~240 in the ventral horn, taking into account various parameters including receptor stoichiometry and the functionality of the fluorophore. These values are very close to our own calculations of GlyR numbers at spinal cord synapses that were obtained slightly differently in terms of sample preparation, microscope setup, imaging conditions, and data analysis, lending support to our experimental approach. Nevertheless, the obtained GlyR copy numbers at hippocampal synapses clearly have to be taken as estimates rather than precise figures, because the number of detections from a single mEos4b fluorophore can vary substantially, meaning that the fluorophores are not represented equally in pointillist images. This can affect the copy number calculation for a specific synapse, in particular when the numbers are low (e.g. in hippocampus), however, it should not alter the average number of detections (Fig. 1B) or the (median) molecule numbers of the entire population of synapses (Fig. 1C). We have discussed the limitations of our approach (p. 11).

Rationale for doing nanobody dSTORM not clear at all. They don't explain the reason for doing the dSTORM experiments. Why not just rely on PALM for coincidence measurements, rather than tagging mEoS with a nanobody, and then doing dSTORM with that? Can they explain? Is it to get extra localisations- i.e. multiple per nanobody? If so, localising same FP multiple times wouldn't improve resolution. Also, no controls for nanobody dSTORM experiments- what about non-spec nb, or use on WT sections?

*As discussed above (point 6), the detection of fluorophores with SMLM is influenced by many parameters, not least the noise produced by emitting molecules other than the fluorophore used for labelling. Our study is exceptional in that it attempts to identify extremely low molecule numbers (down to 1). To verify that the detections obtained with PALM correspond to mEos4b, we conducted robust control experiments (including pixel-shift as suggested by the reviewer, see point 1, revised__ Fig. 1B__). The rationale for the nanobody-based dSTORM experiments was twofold: (1) to have an independent readout of the presence of low-copy GlyRs at inhibitory synapses and (2) to analyse the nanoscale organisation of GlyRs relative to the synaptic gephyrin scaffold using dual-colour dSTORM with spectral demixing (see p. 6). The organic fluorophores used in dSTORM (AF647, CF680) ensure high photon counts, essential for reliable co-localisation and distance analysis. PALM and dSTORM cannot be combined in dual-colour mode, as they require different buffers and imaging conditions. *

The specificity of the anti-Eos nanobody was demonstrated by immunohistochemistry in spinal cord cultures expressing mEos4b-GlyRb and wildtype control tissue (Fig. S3). In response to the reviewer's remarks, we also performed a negative control experiment in Glrbeos/eos slices (dSTORM), in which the nanobody was omitted (new__ Fig. S4F,G__). Under these conditions, spectral demixing produced a single peak corresponding to CF680 (gephyrin) without any AF647 contribution (Fig. S4F). The background detection of "false" AF647 detections at synapses was significantly lower than in the slices labelled with the nanobody. We conclude that the fluorescence signal observed in our dual-colour dSTORM experiments arises from the specific detection of mEos4b-GlyRb by the nanobody, rather than from background, cross-reactivity or wrong attribution of colour during spectral demixing. We have added these data and explanations in the results (p. 7) and in the figure legend of Fig. S4F,G.

What resolutions/precisions were obtained in SMLM experiments? Should perform Fourier Ring Correlation (FRC) on SR images to state resolutions obtained (particularly useful for when they're presenting distance histograms, as this will be dependent on resolution). Likewise for precision, what was mean precision? Can they show histograms of localisation precision.

This is an interesting question in the context of our experiments with low-copy GlyRs, since the spatial resolution of SMLM is limited also by the density of molecules, i.e. the sampling of the structure in question (Nyquist-Shannon criterion). Accordingly, the priority of the PALM experiments was to improve the sensibility of SMLM for the identification of mEos4b-GlyRb subunits, rather than to maximize the spatial resolution. The mean localisation precision in PALM was 33 +/- 12 nm, as calculated from the fitting parameters of each detection (Zeiss, ZEN software), which ultimately result from their signal-to-noise ratio. This is a relatively low precision for SMLM, which can be explained by the low brightness of mEos4b compared to organic fluorophores together with the elevated fluorescence background in tissue slices.

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In the case of dSTORM, the aim was to study the relative distribution of GlyRs within the synaptic scaffold, for which a higher localisation precision was required (p. 6). Therefore, detections with a precision ≥ 25 nm were filtered during analysis with NEO software (Abbelight). The retained detections had a mean localisation precision of 12 +/- 5 for CF680 (Sylite) and 11 +/- 4 for AF647 (nanobody). These values are given in the revised manuscript (pp. 18, 22).

Why were DBSCAN parameters selected? How can they rule out multiple localisations per fluor? If low copy numbers (

Multiple detections of the same fluorophore are intrinsic to dSTORM imaging and have not been eliminated from the analysis. Small clusters of detections likely represent individual molecules (e.g. single receptors in the extrasynaptic regions, Fig. 2A). DBSCAN is a robust clustering method that is quite insensitive to minor changes in the choice of parameters. For dSTORM of synaptic gephyrin clusters (CF680), a relatively low length (80 nm radius) together with a high number of detections (≥ 50 neighbours) were chosen to reconstruct the postsynaptic domain with high spatial resolution (see point 8). In the case of the GlyR (nanobody-AF647), the clustering was done mostly for practical reasons, as it provided the coordinates of the centre of mass of the detections. The low stringency of this clustering (200 nm radius, ≥ 5 neighbours) effectively filters single detections that can result from background noise or incorrect demixing. An additional reference explaining the use of DBSCAN including the choice of parameters is given on p. 22 (see also R2 point 4).

For microscopy experiment methods, state power densities, not % or "nominal power".

*Done. We now report the irradiance (laser power density) instead of nominal power (pp. 18, 21). *

In general, not much data presented. Any SI file with extra images etc.?

*The original submission included four supplementary figures with additional data and representative images that should have been available to the reviewer (Figs. S1-S4). The SI file has been updated during revision (new Fig. S4E-G). *

Clarification of the discussion on GlyR expression and synaptic localization: The discussion on GlyR expression, complex formation, and synaptic localization is sometimes unclear, and needs terminological distinctions between "expression level", "complex formation" and "synaptic localization". For example, the authors state:"What then is the reason for the low protein expression of GlyRβ? One possibility is that the assembly of mature heteropentameric GlyR complexes depends critically on the expression of endogenous GlyR α subunits." Does this mean that GlyRβ proteins that fail to form complexes with GlyRα subunits are unstable and subject to rapid degradation? If so, the authors should clarify this point. The statement "This raises the interesting possibility that synaptic GlyRs may depend specifically on the concomitant expression of both α1 and β transcripts." suggests a dependency on α1 and β transcripts. However, is the authors' focus on synaptic localization or overall protein expression levels? If this means synaptic localization, it would be beneficial to state this explicitly to avoid confusion. To improve clarity, the authors should carefully distinguish between these different aspects of GlyR biology throughout the discussion. Additionally, a schematic diagram illustrating these processes would be highly beneficial for readers.

We thank the reviewer to point this out. We are dealing with several processes; protein expression that determines subunit availability and the assembly of pentameric GlyRs complexes, surface expression, membrane diffusion and accumulation of GlyRb-containing receptor complexes at inhibitory synapses. We have edited the manuscript, particularly the discussion and tried to be as clear as possible in our wording.

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We chose not to add a schematic illustration for the time being, because any graphical representation is necessarily a simplification. Instead, we preferred to summarise the main numbers in tabular form (Table 1). We are of course open to any other suggestions.

Interpretation of GlyR localization in the context of nanodomains. The distribution of GlyR molecules on inhibitory synapses appears to be non-homogeneous, instead forming nanoclusters or nanodomains, similar to many other synaptic proteins. It is important to interpret GlyR localization in the context of nanodomain organization.

The dSTORM images in Fig. 2 are pointillist representations that show individual detections rather than molecules. Small clusters of detections are likely to originate from a single AF647 fluorophore (in the case of nanobody labelling) and therefore represent single GlyRb subunits. Since GlyR copy numbers are so low at hippocampal synapses (≤ 5), the notion of nanodomain is not directly applicable. Our analysis therefore focused on the integration of GlyRs within the postsynaptic scaffold, rather than attempting to define nanodomain structures (see also response to point 8 of R1). A clarification has been added in the revised manuscript (p. 6).

__Reviewer #1 (Significance (Required)): __

The paper presents biological and technical advances. The biological insights revolve mostly on the documentation of Glycine receptors in particular synapses in forebrain, where they are typically expressed at very low levels. The authors provide compelling data indicating that the expression is of physiological significance. The authors have done a nice job of combining genetically-tagged mice with advanced microscopy methods to tackle the question of distributions of synaptic proteins. Overall these advances are more incremental than groundbreaking.

We thank the reviewer for acknowledging both the technical and biological advances of our study. While we recognize that our work builds upon established models, we consider that it also addresses important unresolved questions, namely that GlyRs are present and specifically anchored at inhibitory synapses in telencephalic regions, such as the hippocampus and striatum. From a methodological point of view, our study demonstrates that SMLM can be applied not only for structural analysis of highly abundant proteins, but also to reliably detect proteins present at very low copy numbers. This ability to identify and quantify sparse molecule populations adds a new dimension to SMLM applications, which we believe increases the overall impact of our study beyond the field of synaptic neuroscience.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses.

However I have some minor points that the authors may address for clarification:

1) In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section.

*This is correct; the apparent size of the Sylite spots does not reflect the real size of the synaptic gephyrin domain due to the limited resolution of widefield imaging including the detection of out-of-focus light. We have clarified in the legend of Fig. 1A that Sylite labelling was with classic epifluorescence microscopy. The scale bar in Fig. 1A corresponds to 5 µm. Since the data were not normally distributed, nonparametric tests (Kruskal- Wallis one-way ANOVA with Dunn’s multiple comparison test or Mann-Whitney U-test for pairwise comparisons) were used (p. 23). *

Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided.

The Glrbeos/eos mouse model has been described previously and does not exhibit any structural or physiological phenotypes (Maynard et al. 2021 eLife). The issue was also raised by reviewer R1 (point 5) and has been clarified in the revised manuscript (p. 4).

2) In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text.

Yes, the dSTORM experiments enable dual-colour structural analysis at high spatial resolution (see response to R1 point 7). An explanation has been added (p. 6).

3) Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime.

Acquisition parameters (laser power, exposure time) for dSTORM were chosen to obtain a good localisation precision (~12 nm; see R1 point 8). The number of frames is adequate to obtain well sampled gephyrin scaffolds in the CF680 channel. In the case of the GlyR (nanobody-AF647), the concept of spatial resolution does not really apply due to the low number of targets (see R1, point 13). Power density (irradiance) values have now been given (pp. 18, 21).

4) For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided?

DBSCAN parameters were optimised manually, by testing different values. Identification of dense and well-delimited gephyrin clusters (CF680) was achieved with a small radius and a high number of detections (80 nm, ≥ 50 neighbours), whereas filtering of low-density background in the AF647 channel (GlyRs) required less stringent parameters (200 nm, ≥ 5) due to the low number of target molecules. Similar parameters were used in a previous publication (Khayenko et al. 2022, Angewandte Chemie). The reference has been provided on p. 22 (see also R1 point 9).

5) A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion.

*This part of the manuscript has been completely overhauled. It includes new experimental data, quantification of the data (new Fig.5), as well as the discussion and interpretation of our findings (see also R1, point 3). In agreement with our earlier interpretation, the data confirm that low availability of GlyRa1 subunits limits the expression and synaptic targeting of GlyRa1/b heteropentamers. The observation that GlyRa1 overexpression with lentivirus increases the size of the postsynaptic gephyrin domain further points to a structural role, whereby GlyRs can enhance the stability (and size) of inhibitory synapses in hippocampal neurons, even at low copy numbers (pp. 13-14). *

6) in line 552 "suspension" is misleading, better use "solution"

Done.

__Reviewer #2 (Significance (Required)): __

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript.

Field of expertise: Super-Resolution Imaging and corresponding analysis

__Reviewer #4 (Evidence, reproducibility and clarity (Required)): __

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers.

I have a few points that I hope help to improve the strength of this study.

• In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this.

*It is not clear what the reviewer means by “it remains questionable that these reflect proper GlyRs”. The PALM experiments include a series of stringent controls (see R1, point 1) demonstrating the existence of low-copy GlyRs at inhibitory synapses in the hippocampus (Fig. 1) and in the striatum (Fig. 3), and are backed up by dSTORM experiments (Fig. 2). We have no reason to doubt that these receptors are fully functional (as demonstrated for the ventral striatum (Fig. 4). However, due to their low number, a role in inhibitory synaptic transmission is clearly limited, at least in the hippocampus and dorsal striatum. *

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We therefore propose a structural role, where the GlyRs could be required to stabilise the postsynaptic gephyrin domain in hippocampal neurons. This is based on the idea that the GlyR-gephyrin affinity is much higher than that of the GABAAR-gephyrin interaction (reviewed in Kasaragod & Schindelin 2018 Front Mol Neurosci). Accordingly, there is a close relationship between GlyRs and gephyrin numbers, sub-synaptic distribution, and dynamics in spinal cord synapses that are mostly glycinergic (Specht et al. 2013 Neuron; Maynard et al. 2021 eLife; Chapdelaine et al. 2021 Biophys J). It is reasonable to assume that low-copy GlyRs could play a similar structural role at hippocampal synapses. A knockdown experiment targeting these few receptors is technically very challenging and beyond the scope of this study. However, in response to the reviewer's question we have conducted new experiments in cultured hippocampal neurons (new__ Fig. 5__). They demonstrate that overexpression of GlyRa1/b heteropentamers increases the size of the postsynaptic domain in these neurons, supporting our interpretation of a structural role of low-copy GlyRs (p. 14).

• The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules?

Gephyrin is known to form a two-dimensional scaffold below the synaptic membrane to which inhibitory GlyRs and GABAARs attach (reviewed in Alvarez 2017 Brain Res). The majority of the synaptic receptors are therefore thought to be located in the synaptic membrane, which is supported by the close relationship between the sub-synaptic distribution of GlyRs and gephyrin in spinal cord neurons (e.g. Maynard et al. 2021 eLife). To demonstrate the surface expression of GlyRs at hippocampal synapses we labelled cultured hippocampal neurons expressing mEos4b-GlyRa1 with anti-Eos nanobody in non-permeabilised neurons (see Figure below for the reviewer only). The close correspondence between the nanobody (AF647) and the mEos4b signal confirms that the majority of the GlyRs are indeed located in the synaptic membrane.

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Figure (for the reviewer only).* Left: Lentivirus expression of mEos4b-GlyRa1 in fixed and non-permeabilised hippocampal neurons (mEos4b signal). Right: Surface labelling of the recombinant subunit with anti-Eos nanoboby (AF647). *

• 'We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes'. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations.

We fully agree that background subtraction can be useful with low detection numbers. In the revised manuscript, copy numbers are now reported as background-corrected values. Specifically, the mean number of detections measured in wildtype slices was used to calculate an equivalent receptor number, which was then subtracted from the copy number estimates across hippocampus, spinal cord and striatum. This procedure is described in the methods (p. 20) and results (p. 5, 8), and mentioned in the figure legends of Fig. 1C, 3C. The background corrected values are given in the text and Table 1.

Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript.

*The reviewer is right to point this out. There is still some debate about the stoichiometry of heteropentameric GlyRs. Configurations with 2a:3b, 3a:2b and 4a:1b subunits have been advanced (e.g. Grudzinska et al. 2005 Neuron; Durisic et al. 2012 J Neurosci; Patrizio et al. 2017 Sci Rep; Zhu & Gouaux 2021 Nature). We have therefore chosen a quantification that is independent of the underlying stoichiometry. Since our quantification is based on very sparse clusters of mEos4b detections that likely originate from a single receptor complex (irrespective of its stoichiometry), the reported values actually reflect the number of GlyRs (and not GlyRb subunits). We have clarified this in the results (p. 5) and throughout the manuscript (Table 1). *

• The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function.

This is an interesting suggestion. However, the primary aim of our study was to identify the existence of GlyRs in hippocampal regions. At low copy numbers, the concept of sub-synaptic domains (SSDs, e.g. Yang et al. 2021 EMBO Rep) becomes irrelevant (see R1 point 13). It should be pointed out that the dSTORM pointillist images (Fig. 2A) represent individual GlyR detections rather than clusters of molecules. In the striatum, our specific purpose was to solve an open question about the presence of GlyRs in different subregions (putamen, nucleus accumbens).

• It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test.

Both R1 and R2 have also commented on the data in Fig. 5 and their interpretation. We have substantially revised this section as described before (see R1 point 3) including additional experiments and quantification of the data (new Fig. 5). The findings lend support to our earlier hypothesis that GlyR alpha subunits (in particular GlyRa1) are the limiting factor for the expression of heteropentameric GlyRa/b in hippocampal neurons (pp. 13-14). Since the GlyRa1 subunit itself does not bind to gephyrin (Patrizio et al. 2017 Sci Rep), the synaptic localisation of the recombinant mEos4b-GlyRa1 subunits is proof that they have formed heteropentamers with endogenous GlyRb subunits and driven their membrane trafficking, which the GlyRb subunits are incapable of doing on their own.

__Reviewer #4 (Significance (Required)): __

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution.

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights.

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy.

my expertise is in super-resolution microscopy, synaptic transmission and plasticity

As we have stated before, the novelty of our study lies in the use of SMLM for the identification of very small numbers of molecules, which requires careful control experiments. This is something that has not been done before and that can be of interest to a wider readership, as it opens up SMLM for ultrasensitive detection of rare molecular events. Using this approach, we solve two open scientific questions: (1) the demonstration that low-copy GlyRs are present at inhibitory synapses in the hippocampus, (2) the sub-region specific expression and functional role of GlyRs in the ventral versus dorsal striatum.

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The following review was provided later under the name “Reviewer #4”. To avoid confusion with the last reviewer from above we will refer to this review as R4-2.

__Reviewer #4-2 (Evidence, reproducibility and clarity (Required)): __

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood.

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB.

The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments:

• Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

• They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions.
• The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies.
• Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum.

• The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics A thorough analysis and quantification of the data in Fig.5 has been carried out as requested by all the other reviewers (e.g. R1, point 3). The new data and results have been described in the revised manuscript (pp. 9-10, 13-14).

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit’s localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

*This question has also been raised before (R1, point 5). According to an earlier study the mEos4b-GlyRb knock-in does not cause any obvious phenotypes, with the possible exception of minor loss of glycine potency (Maynard et al. 2021 eLife). The fact that the synaptic levels in the spinal cord in heterozygous animals are precisely half of those of homozygous animals argues against differences in receptor expression, heteropentameric assembly, forward trafficking to the plasma membrane and integration into the synaptic membrane as confirmed using quantitative super-resolution CLEM (Maynard et al. 2021 eLife). Accordingly, we did not observe any behavioural deficits in these animals, making it a powerful experimental model. We have added this information in the revised manuscript (p. 4). *

In addition, without any quantification or statistical analysis, the author’s claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

As mentioned before, we have substantially revised this part (R1, point 3). The quantification and analysis in the new Fig. 5 support our earlier interpretation.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these non-synaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic.

The existence of extrasynaptic GlyRs is well attested in spinal cord neurons (e.g. Specht et al. 2013 Neuron; this study see Fig. S2). The fact that these appear as small clusters of detections in SMLM recordings results from the fact that a single fluorophore can be detected several times in consecutive image frames and because of blinking. Therefore, small clusters of detections likely represent single GlyRs (that can be counted), and not assemblies of several receptor complexes. Due to their diffusion in the neuronal membrane, they are seen as diffuse signals throughout the somatodendritic compartment in epifluorescence images (e.g. Fig. 5A). SMLM recordings of the same cells resolves this diffuse signal into discrete nanoclusters representing individual receptors (Fig. 5B). It is not clear what information co-localisation experiments with specific markers could provide, especially in hippocampal neurons, in which the copy numbers (and density) of GlyRs is next to zero.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Quantification of the data have been carried out (new Fig.5C,D). The results have been described before (R1, point 3) and support our earlier interpretation of the data (pp. 13-14).

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute’s ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good.

We have added the requested information from the ISH database of the Allen Institute in the discussion as suggested by the reviewer (p. 12). However, in combination with the transcriptomic data (Fig. S1) our finding strongly suggest that the expression of synaptic GlyRs depends on the availability of alpha subunits rather than on the presence of the GlyRb transcript. This is obvious when one compares the mRNA levels in the hippocampus with those in the basal ganglia (striatum) and medulla. While the transcript concentrations of GlyRb are elevated in all three regions and essentially the same, our data show that the GlyRb copy numbers *at synapses differ over more than 2 orders of magnitude (Fig. 1B, Table 1). *

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

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

Yes, for the most part.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

N/A

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

A quantification has been added (see R1, point 3).

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results.

We agree in principle with this suggestion. However, the revised Fig. S4 is more complex and we think that it would distract from the data shown in Fig. 2. Given that Fig. S4 is mostly methodological and not essential to understand the text, we have kept it in the supplement for the time being. We leave the final decision on this point to the editor.

__Reviewer #4-2 (Significance (Required)): __

[This review was supplied later]

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions.

• Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function.

• State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims.

*We thank the reviewer for the positive assessment of the technical and biological implications of our work, as well as the interest of our findings to a wide readership of neuroscientists and cell biologists. *

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

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

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Referee #4

Evidence, reproducibility and clarity

Summary: Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood.

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB. The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments: - Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

1) They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions. 2) The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies. 3) Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum. 4) The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit's localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

In addition, without any quantification or statistical analysis, the author's claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these non-synaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute's ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

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

Yes, for the most part.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments: - Specific experimental issues that are easily addressable.

N/A

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions.

• Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function.

• State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers.

I have a few points that I hope help to improve the strength of this study.

• In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this.
• The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules?
• 'We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes'. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations. Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript.
• The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function.
• It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test.

Significance

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution.

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights.

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy.

my expertise is in super-resolution microscopy, synaptic transmission and plasticity

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Referee #2

Evidence, reproducibility and clarity

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses.

However I have some minor points that the authors may address for clarification:

1. In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section. Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided.
2. In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text.
3. Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime.
4. For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided?
5. A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion.
6. in line 552 "suspension" is misleading, better use "solution"

Significance

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript.