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Reply to the reviewers

We thank the three reviewers for their thoughtful and constructive comments which help us to improve the manuscript. Please find our responses below. * *

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

Summary This study investigates how altered expression of cleavage and polyadenylation (CPA) factors affects alternative polyadenylation (APA), transcription termination and cellular phenotypes in colorectal cancer (CRC) cell lines. The authors combine genetic perturbations of CPA factors with chemical inhibition of CPSF73 and assess effects on clonogenic potential, transcription-replication conflicts, APA profiles, and transcription termination-associated RNAPII phosphorylation patterns. The main comparisons are performed between healthy (1CT), primary tumour (SW480, HCT116) and metastatic (SW620) cell lines, which are reported to contain altered expression levels of CPA factors. The data suggest differential dependence on CPA factors between primary tumour-derived and metastatic CRC cell lines, as well as changes in transcription termination patterns. The data are overall well-presented with clear figures. However, in several cases the strength of the conclusions appears to exceed the support provided by the data, and alternative interpretations should be considered.

Major comments 1. Clonogenic sensitivity to CPA factor perturbation and comparability of clonogenic assays between cell lines: -The data indicate that clonogenic potential in SW480 is strongly dependent on CPSF73 and PCF11, whereas SW620 appear less sensitive. However, the interpretation is complicated by differences in depletion efficiencies. In SW620 cells, PCF11 depletion appears inefficient, and protein levels remain higher than in siLUC-treated SW480 cells (Fig. 1D and S1C; also in comparison to 1CT by inference of Fig. 1C). Thus, the apparent resistance of SW620 cells could reflect insufficient depletion rather than true biological tolerance. The effectiveness of siCPSF73 treatments is difficult to assess from the presented data. Quantification of protein knockdown levels should be provided and incorporated into the interpretation.

-In Fig. 1D, 1E, and S1D, colony formation of DMSO- or siLUC-treated SW620 and SW480 cells differs markedly in absolute terms. However, the graphs are normalized separately for each cell line, which obscures this difference. This raises two concerns: First, the baseline clonogenic capacity differs between the lines and should be discussed. Second, it is unclear whether direct comparisons between cell lines are valid when normalization is performed independently. For example, in absolute terms, 1 µM JTE-607 appears to have a similar effect in SW620 cells as 5 µM in SW480 cells, which would contradict the conclusion that metastatic cells are more tolerant to CPA perturbations. This issue should be explicitly addressed.

We thank the reviewer for those thoughtful comments.

a) Assessing the biological meaning of differences in PCF11 depletion efficiency between SW480 and SW620 cell lines is inherently tricky, because the two cell lines differ 3-fold in their baseline PCF11 level (Fig. 1C). Even with equal efficiencies of knock-down, the number of PCF11 molecules per cell left after the treatment will differ. We haven't mentioned this in our original manuscript but will highlight this issue in the revised version - as we agree it is an important consideration for the interpretation of the results.

b) As requested, we will add quantification of western blots from 3 biological replicates to the revised manuscript, to demonstrate the depletion efficiencies. We agree that the single western blot presented by itself was not sufficient; the efficiency of SW620 knock-down is not lower compared to SW480.

c) The baseline clonogenic capacity of SW480 and SW620 has been previously calculated and compared in two publications (PMID: 31961892 and 29796953). In both cases, the SW620 cells showed higher clonogenic potential than SW480, which was calculated based on the number of clones containing more than 50 cells.

d) The reason behind normalization of our data to a control sample is the difference in cell size between the cell lines, which prohibits their direct comparison.

For the colony formation assays, we seeded the same number of cells and cultured them for the same amount of time. However, the difference in cell size, leads to a huge difference in colony sizes (Figure 1D), therefore it was not possible to set the same parameters for counting colonies of SW480 and SW620 cells. Therefore, we decided to use an approach frequently used in high profile cancer studies (e.g. Li at al., 2023, PMID: 37620362, Waterhouse et al., 2025, PMID: 40328966, Yang et al., 2026, PMID: 41484364) and normalize each biological replicate to the control sample to analyze the response to the treatment only.

e) During revision, we might additionally perform CellTiter 96® Non-Radioactive Cell Proliferation Assay (MTT) to test how another cancerous characteristic of SW480 and SW620 cells are affected by JTE-607.

f) We will also perform colony formation and/or MTT assays for 3 additional cell lines: HCT116 (primary tumor-derived) and T87 and COLO-205 (metastasis-derived, which we are currently in the process of obtaining) to assess their sensitivity to JTE-607.

g) The result of higher sensitivity of SW620 cells compared to SW480 cells has been obtained not only for PCF11 knock-down, where inter-cell line differences of baseline protein level make interpretations more difficult, but also for CPSF73 knock-down (Fig. 1D), which baseline level was similar and knock-down was equally efficient in both cell lines, and for CPSF73 inhibition (Fig. 1E); with the use of normalization procedures used frequently in literature (see point d).

Therefore, we argue that our conclusion that SW480 cells are more sensitive than SW620 to the abrogation of 3' pre-mRNA cleavage and transcription termination is valid. However, we are willing to weaken our conclusion if the reviewer does not agree with our point of view.

For the additional cancer-specific experiments proposed above, we suggest the usage of JTE-607 as drug treatment is more robust, reproducible, and medically relevant compared to knock-down experiments.

1. Interpretation of transcription termination markers: -The study uses RNAPII T4ph as a marker of transcription termination, which is well justified based on the ref. [30], but still the mechanistic basis of this modification is not fully understood. Changes in T4ph localization are interpreted as consequences of CPA activity, but possible differences in kinase or phosphatase activities between cell lines are not considered that could affect the T4ph levels or localization. Therefore, conclusions based solely on T4ph redistribution should be presented with greater caution, and alternative explanations should be acknowledged.

While in our experience RNAPII T4ph is the most sensitive and useful termination marker, we agree with the referee that its metabolism and function is insufficiently understood - this is an important and interesting direction for future investigation.

In order to increase the robustness of our study, during revision we will additionally perform nascent transcriptomics on SW480 and SW620 using a different method, POINT-seq. POINT-seq in contrast to T4ph mNET-seq relies neither on RNAPII modification status nor is affected by pausing. We will also probe global T4ph-RNAPII levels in our cellular model by western blot. We will then adjust our manuscript accordingly.

-Line 240 states that premature termination is increased in primary tumour cells. However, the data show increased T4ph signal (Fig. 4B) but no change in total RNAPII occupancy in gene bodies (Fig. 4A). This does not directly demonstrate increased termination. Additional evidence or a more cautious interpretation would be appropriate.

The reviewer is right in pointing out the difference between the Total-RNAPII and T4ph-RNAPII signals across the gene body. We will provide a clearer description and explanation in the revised manuscript.

T4ph-RNAPII is present at low levels in human cells. S2ph and S5ph are the dominant modifications, accounting for ~75% of phospho-counts, whereas T4ph has a relative abundance of ~15% (PMID: 26799765). In addition, T4ph is concentrated at gene ends and typically very low in the gene body (PMID: 28017589, 30819644, doi: 10.1101/2025.07.14.664659). Consequently, it is very easy to spot its gene-body increase in metagene analysis (Figure 4B), even when it happens only on a subset of genes in cancer samples (e.g. Fig. 4D).

Total-RNAPII signal in the gene body largely reflects S2ph-modified RNAPII levels so its metagene analysis is not sufficiently sensitive to detect differences in gene-body T4ph-RNAPII.

Consequently, RNAPII-T4ph and RNAPII-total mNET-seq show distinct metagene patterns and different responses to termination changes. RNAPII-T4ph mNET-seq is a sensitive method to detect changes in termination patterns, while total-RNAPII is much less specific and sensitive with respect to transcription termination.

1. Cleavage-termination distance as a predictor of transcript levels: -Figure 5A presents median distances across all genes. It would be informative to perform a gene-wise comparison between cell lines (difference in cleavage-T4ph distance for the same gene, e.g. in 1CT vs. HCT116, individual differences plotted across all genes). This analysis could help clarify how frequently individual genes experience the effect (shortening of the cleavage-T4ph distance between 1CT and tumour cells) that is observed globally.

Thank you for this valuable suggestion. We have performed the gene-wise comparison which is indeed very informative. Firstly, we observed the same trend as for all active protein-coding genes - shorter distance in all CRC cell lines compared to 1CT cells with the lowest values of the cleavage-termination distance in the primary tumor cells. Secondly, and even more importantly, this analysis additionally shows that the shortening effect is global - only a small percentage of genes do not undergo shortening of the cleavage-T4ph distance between 1CT and tumor cells.

We will incorporate the results of this analysis into the figures of the revised manuscript.

-The manuscript claims that proximity between pre-mRNA 3′-end cleavage and transcription termination predicts increased nuclear transcript levels. However, the correlation coefficients are small (Spearman r ~ -0.2 at most), indicating weak predictive power. Therefore, the use of the term "predicts," especially in the manuscript title, appears to overstate the strength of the relationship. The authors should either moderate this claim or provide additional analysis to support stronger predictive value.

We agree with the reviewer that the term "predicts" is not ideal in this context and are happy to substitute "is associated with". The title would then read: "Proximity of pre-mRNA 3′ end processing and transcription termination is associated with enhanced gene expression".

Minor comments -Figures 1B and S1A: The discontinuous y-axis makes it difficult to assess relative protein level differences between normal and cancer samples. Statistical testing should be included to evaluate significance.

We had decided against statistical testing due to the problems with biological interpretation of such analyses and its limitations for proteins present in the cell at low levels and/or highly variable between samples. PCF11 is such protein. It is an order of magnitude less abundant compared to other RNA 3' processing factors, and its levels are variable as shown in our Fig. 1B (re-analyzed proteomics data from Wiśniewski et al., 2015). Therefore, the increase in PCF11 levels in this dataset is not statistically significant in Mann-Whitney test, while it is significant for CPSF73.

The variability of PCF11 levels can be also observed in the Clinical Proteomic Tumor Analysis Consortium (CPTAC) data in the Human Protein Atlas (while no absolute quantification was performed there).

In two independently obtained proteomics patient datasets (Wiśniewski et al., 2015; CPTAC), as well as in Western blot assays from our cell culture model, an increase in PCF11 protein abundance is observed in cancer cells. This consistency across different datasets and our model holds greater biological relevance than the statistical analysis of highly varied samples. Nevertheless, if the reviewer requires statistics, we will include them in the revised manuscript.

The discontinuous y-axis was applied due to broad range of protein molecules. Presentation of data with linear continuous scale did not allow to present the difference between normal and cancer samples for all the proteins on the same graph.

Alternatively, if the reviewer and editor prefer, we are happy to present the data with log10 transformed scale. The disadvantage of log-scale is that the differences between normal and cancer samples are less obvious to the eye, the advantage is a continuous y-axis.

-Lines 217-218: The text should emphasize that nuclear RNA abundance may not reflect cytoplasmic mRNA levels, particularly when APA alters 3′UTRs and may affect mRNA stability.

We agree and will incorporate the reviewer's suggestion in our revised manuscript.

-Lines 261-264: The cleavage-termination distance metric should be more clearly defined as the distance between the polyadenylation site and the T4ph signal peak.

We plan to incorporate a drawing into the figure, to better explain our cleavage-termination definition.

We also performed the cleavage site to T4ph signal peak (highest signal in the termination window) distance calculations, and they show the same trend as our original method (Figure 5A), with no changes to the conclusions we made. We will incorporate this additional analysis into a supplementary figure.

**Referees cross-commenting**

Reviewer #3:

On the contrary to implied in the reviewer report, this manuscript does not report the effects of CPSF73 inhibitor JTE-607 on APA. On this note, as the authors discuss uncoupling of cleavage and transcription termination, they could consider (this is not a request) testing how the cleavage inhibitor JTE-607 impacts the distribution of transcription termination marker T4ph, and whether the effects would be different in different cell lines where the coupling appears to be different. This could give mechanistic insights into the sources of the differences between cell lines.

In order to get a mechanistic idea why shorter cleavage-termination distance is associated with higher gene expression, we plan to test the cleavage efficiency on genes, which show differences in cleavage-termination distance and expression levels, between SW480 and SW620 cell lines. To this end, we will perform POINT-seq, checking differences between those cell lines in control conditions and with JTE-607. We believe that this new experimental approach will provide a deeper mechanistic insight, compared to performing further correlation analyses repeating the same experiment types.

Reviewer #1 (Significance (Required)):

This study addresses an important question in RNA biology and cancer research: how altered expression or pharmacological targeting of CPA factors affects alternative polyadenylation, transcription termination, and cellular phenotypes in CRC models. This topic is timely, as CPSF73 has been proposed as a therapeutic target, making it important to understand the molecular and cellular consequences of modulating CPA factor activities. A key strength and robust finding of the study is the identification of unexpected relationships between pre-mRNA 3′-end processing and transcription termination during CRC progression. Notably, the authors report that changes in alternative polyadenylation and transcription termination appear to be uncoupled and may even occur in opposite directions. This challenges simplified models in which these processes are tightly coordinated and suggests that their (mis)regulation in cancer cells may be more complex than previously appreciated. Secondly, the study provides an interesting observation that gene-specific changes in cleavage-T4ph distance correlate negatively with changes in nuclear levels of processed transcripts. This suggests a potential relationship between the spatial coupling of 3′-end processing and transcription termination and transcript abundance. If validated mechanistically, this could represent a conceptual advance in understanding how transcription termination dynamics influence gene expression outputs. However, the observed correlations are relatively weak, and the mechanistic basis of this relationship remains unclear. As such, this advance is primarily descriptive at this stage.

As indicated in response to the cross-commenting point above, one possible mechanistic explanation why shorter cleavage-termination distance could be associated with higher gene expression, is increased cleavage efficiency when the cleavage-termination distance is short. To test this hypothesis, we will perform POINT-seq on SW480 and SW620 cell lines, in control and CPSF73 inhibition conditions. We have previously demonstrated that POINT-seq technique allows calculation of cleavage efficiencies, and its alterations (doi: 10.1101/2025.07.14.664659).

So far, our data (Fig. 5F, G) indicates that PCF11 is involved in this process since PCF11 downregulation resulted in lengthening the distance between 3′-end cleavage and RNAPII terminal pausing. This lengthening was in parallel correlated with the decrease of the nuclear RNA levels. However, PCF11 participates in multiple steps of gene expression - pre-mRNA cleavage, alternative polyadenylation, RNAPII pausing, and mRNA export - making the underlying mechanism difficult to pinpoint without additional experiments.

Importantly, our work provides the first clear evidence that changes in cleavage site usage and termination region usage can become uncoupled. We hope that continued tool development, together with studies like ours, will ultimately enable a full mechanistic understanding.

Several interpretations of experimental data would benefit from more cautious framing or additional analysis. In particular, the relationship between changes in CPA factor expression levels and sensitivity to the CPSF73 inhibitor JTE-607 across CRC cell lines remains unclear from the presented data.

During the revision we will explain more clearly the rationale for our interpretation of the data. In cases where more cautious framing would still be needed, we will include alternative interpretations.

This work will be of interest primarily to basic researchers in RNA processing and transcription regulation, gene expression control, cancer cell biology and pharmacological targeting of RNA-processing machineries.

Reviewer field of expertise: My expertise is in RNA processing and gene regulation. I do not have specific expertise clinical oncology or cancer biology.

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

Factors involved in pre-mRNA cleavage and polyadenylation (CPA) are upregulated in many cancers and have been found to be associated with poor prognosis. In their manuscript "Proximity of pre-mRNA 3′ end processing and transcription termination predicts enhanced gene expression", Stepien et al. use colorectal cancer (CRC)-derived cell lines as a model of CPA overexpression to study its biological consequences. To this end, the authors initially confirm increased expression of CPA factors in these cell lines and demonstrate that their knock-down strongly decreases the colony-forming ability of primary tumour-derived CRC cells. They further assess various phenotypes that are expected to depend on CPA activity based on the current knowledge in the field, including poly-A site selection, occurrence of transcription-replication conflicts, and the site of transcription termination. Contrary to expectations, they find a proximal shift in transcription termination to be the most prominent change in CRC ell lines with high CPA levels, despite no clear preference for proximal poly-A site usage in these cells, suggesting an uncoupling of both processes. The authors combine their 3'-end mapping data and T4P-mNET-seq data mapping terminating RNAPII to score cleavage-termination distance at individual genes and find shorter distances to correlate with increased gene expression in the different cell lines. Overall, this is a carefully conducted study, and the claims and conclusions are well supported by the data.

I have some minor comments: 1. PLA assay to quantify transcription-replication conflicts (Figure 2). The quantified data looks very convincing and is also in good agreement with the proximal shift in transcription termination that is demonstrated later in the paper. However, the PLA channel signal in the microscopy image examples shown in panel A looks very blurry, and it is hard to imagine that one would be able to count # foci based on this. This may just be an issue with the resolution of the image provided. Apparently, there are much less foci in the treated samples shown in panel B - maybe microscopy images for these could be provided as well? Also, since none of the treatments impact the # of TRCs, it would have been nice to include a positive control known to induce TRCs to demonstrate that the assay works (if such a control is known) - this is optional, and I would not ask to repeat the entire experiment just for this additional control (but maybe the authors have done it and the data is already available?).

We apologize for the low resolution of the picture presented in Figure 2. We were unable to upload high resolution picture file during the first submission, for technical reasons. We will improve it in the revised manuscript.

The difference in baseline PLA foci between Fig. 2A and 2B reflects a known sensitivity of the PLA assay to cell confluency. As these two experiments were performed at different confluences, direct cross-panel comparison is not appropriate. For this reason, all quantitative comparisons in the manuscript are made strictly within the same plate, the same PLA reaction, and between wells with comparable confluency, which avoids introducing bias from these technical variables. For clarity, we plan to incorporate the above information into the Methods section. To validate assay specificity within each experiment, we confirmed that EdU-positive cells consistently showed higher PLA foci counts than EdU-negative cells from the same wells, demonstrating that quantification reflects genuine PCNA-associated signal above background. With this internal validation in place, each panel's comparisons remain valid and interpretable on their own terms.

No classical positive control exists for a PolII-pThr4/PCNA PLA interaction, as this is a relatively unexplored proximity event with no established positive control condition. We used single-antibody negative controls to establish assay specificity, although we didn't quantify and show it. We also used EdU-negative cells within the same wells as an internal background baseline, ensuring that measured foci reflect genuine signal above background. As a proxy for positive controls, we relied on the detection of changes in PLA foci number between the tested conditions, such as the effect of 4h XRN2 degradation. Also, the consistency of biological replicates and the differences between cell lines made us quite secure we were detecting reproducible and biologically relevant differences.

1. Figure 2A-C: please include information on number of cells quantified

We will incorporate this information into the revised manuscript.

1. Figure 2C: In the label, please include degron, e.g. HCT116 CPSF73-AID rather than just HCT116

We will modify the label according to the reviewer's suggestion.

1. Figure 5C: When quantifying nascent txn based on mNET-seq, to which extent would one expect terminally paused RNAPII along the gene body (premature termination events) to contribute to the increased signal? That is, could an increase in stalling be mistaken for an increase in transcription? Based on the metagene plot in Fig 2A it doesn't look like it, but the authors may be able to estimate the effect (if any) from their data.

We thank the reviewer for pointing this out.

As reviewer #1 observed, and we comment above (Rev.1 point 2b), the increase of premature termination events in cancer cells, which can be readily detected by RNAPII T4ph mNET-seq increase in the gene body, does not globally perturb total RNAPII mNET-seq profiles (see metagenes in figure 4A and 4B).

Nevertheless, mNET-seq method does indeed detect both nascent transcription levels and RNAPII pausing, which is particularly relevant when wanting to make conclusions on a single gene level. In order to increase the robustness of our study and make stronger conclusions about nascent transcription rates, independent of stalling, during revision we will perform POINT-seq experiments in SW480 and SW620 cells. That method, in contrast to mNET-seq, is not pausing sensitive.

Reviewer #2 (Significance (Required)):

The observed uncoupling of poly-A site selection and size of termination window is unexpected and raises important questions on how these coupled processes can be regulated independently.

Strengths of the study: i) Parallel assessment of different CRC-based cell lines provides evidence of phenotype stability across patients. ii) Brings together strong technical expertise combining different state-of-the-art methodologies to map and correlate poly-A site usage, site of transcription termination, and levels of nascent transcription within the same cell lines under the same conditions, providing a comprehensive dataset.

Limitations: i) For the time being, observation limited to CRC cell lines.

While this is the first time that we are able to show the pre-mRNA 3' cleavage and transcription termination uncoupling so clearly, we have previously reported findings in other cell types which pointed to this direction. We found in HeLa cells (PMID: 30819644) that genes preferentially using distal polyadenylation sites exhibit more proximal RNAPII terminal pausing compared to genes that predominantly use proximal polyadenylation sites. Recently, we also found in U2OS cells after SETD2 KO and renal cell carcinoma cell lines with SETD2 mutation, that readthrough transcription occurs independently of APA (doi: 10.1101/2025.07.14.664659). This phenomenon could be frequent, but it has not been investigated until now, as cleavage and termination were usually studied separately.

In terms of the correlation between cleavage-termination distance and expression levels, in our study so far, we found it in CRC (HCT116, SW480, SW620) and cervical cancer (HeLa) cell lines. During revision we plan to test it additionally in pancreatic cell lines, with high sensitivity to JTE-607 treatment (BxPC3), medium (Panc1), and low sensitivity (MiaPaCa2).

ii) Mechanism behind proximal shift of termination to be determined.

We agree with the reviewer that the mechanism underlying the proximal transcription termination is missing. Our unpublished data show correlation between RNAPII pausing and transcription termination factors occupancy on chromatin. However, since more factors are involved, such as elongation speed and chromatin architecture, resolving the mechanism requires further extensive studies.

I expect this work to be of interest to an audience interested in transcription and regulation of gene expression more broadly, with potential translational relevance for cancer therapy.

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

The manuscript by Stępień et al. aims to investigate the roles of pre-mRNA 3′ end processing and transcription termination using colorectal cancer (CRC) cell lines (normal colon epithelial cells: 1CT; primary tumours: HCT116 and SW480; metastatic tumour: SW620). By using publicly available proteomic datasets and their cellular models, the authors first demonstrate elevated expression of several cleavage and polyadenylation (CPA) and termination factors, including CPSF73 and PCF11, in CRC cells. They further assess the functional relevance of CPSF73 and PCF11, showing that siRNA-mediated knockdown of these factors reduces colony formation, particularly in primary cancer cell lines. However, they do not observe a clear association between CPA/termination factors and transcription-replication collisions (TRCs), suggesting that TRCs may not underlie the altered colony formation phenotype.

The authors also examine alternative polyadenylation (APA) using the CPSF73 inhibitor JTE-607 and report complex APA patterns: primary tumour cell lines display a bias toward distal APA site usage, whereas the metastatic SW620 line preferentially uses proximal sites. They further evaluate transcription termination and observe a proximal shift (early termination) in primary CRC cells, and to a lesser extent in SW620 cells. Noting the apparent discrepancy between APA site shifting and proximal termination, the authors introduce a new metric termed cleavage-termination distance, defined as the distance between the coordinates of the major PAS and RNAPII termination site. They report an association between shortening of cleavage-termination distance and increased gene expression, which may contribute to the upregulation of cancer-related genes.

Overall, this is a well-written manuscript that highlights potential roles of pre-mRNA processing and transcription termination in gene expression control, with implications for cancer biology. Nevertheless, several issues should be addressed to strengthen the study:

Overall, this is a well-written manuscript that reveals potential roles of pre-mRNA processing and transcription termination in gene expression control, with implications for cancer biology. Nevertheless, I have a few comments that may help strengthen the study.

Major comments: 1. The study includes two primary tumour cell lines but only one metastatic cell line (SW620), which is derived from the same patient as SW480. It remains unclear whether the observed effects represent general characteristics of metastatic tumour cells or are specific to this particular cell line.

Our primary workhorse in this study are the cell lines SW480 and SW620, which are derived from the same patient, to avoid the confounding variable of genetic diversity between cell lines. Unfortunately, these are the only paired CRC cell lines currently available in cell banks.

We would not want to perform further (expensive and time-consuming) genomic assays on additional CRC metastatic cell lines since the cell lines available were isolated from other types of metastasis (liver or lung, while SW620 comes from lymph node) and other patients - which would make interpreting any results obtained with them difficult. However, we plan to check the sensitivity of one more primary (HCT116) and two more metastatic (T87 and COLO-205) cancer cell lines to JTE-607 treatment in colony formation or MTT assay to find out whether the differences in CRC cell sensitivity are more cancer-stage or patient specific.

Further on, we plan to check whether our finding of alterations in cleavage-termination distance might have clinically relevant prognostic value, even outside of the context of CRC. To this end, we will test the hypothesis that a short cleavage-termination distance could be a prognostic marker for sensitivity of cells to JTE-607 treatment. It has been previously demonstrated that pancreatic cancer (PC) cell lines differ in sensitivity to JTE-607 (PMID: 38191171). We will perform T4ph-mNET-seq and nuclear 3'mRNA-seq experiments on PC cell lines to check the cleavage-termination distance in JTE-607-sensitive (BxPC3), medium sensitive (Panc1) and least JTE-607 sensitive (MiaPaCa2) cells, and for presence or absence of correlation of this distance with the cell sensitivity to JTE-607.

The rationale for focusing on colorectal cancer in this study requires further clarification. Although the Introduction provides a comprehensive review of CPSF73 and PCF11 in other cancer types, evidence specific to colorectal cancer is limited. Are these factors known to be mutated or dysregulated in CRC? Is their expression associated with patient survival? The authors could strengthen their rationale by performing a basic analysis using publicly available datasets (e.g., TCGA), such as evaluating expression levels in tumour versus normal tissue and generating Kaplan-Meier survival curves.

We will respond to these questions in the revision.

1. In Figure 5 and Supplementary Figure 5, the authors analyse cleavage-termination distance across oncogenes and tumour suppressor genes and observe a negative correlation between cleavage-termination distance and gene expression level. This is an interesting finding and suggests a possible mechanism for enhancing expression of cancer-related genes. It would be valuable to extend this analysis more systematically-for example, by stratifying genes based on cleavage-termination distance and performing gene ontology enrichment analysis / GSEA to identify functional categories enriched among genes with shorter or longer distances. The authors could further relate these gene sets to, for example, distinct phenotypes between primary vs metastatic tumours.

This is an excellent suggestion. We will perform the above analyses carefully during the revision. Our initial analysis done upon receiving the reviews suggests that the genes, whose cleavage-termination distance decreases during tumorigenesis, while gene expression increases, are enriched for RNA processing, DNA damage response, chromatin organization and ribosome biogenesis factors. On the other hand, increased cleavage-termination distance and decreased gene expression are mostly associated with organelle assembly and protein localization. We will deepen this analysis and discuss the implication to cancer biology in our revised manuscript.

Minor comments: 4. In Figure 2A, the number of RNAPII-PCNA PLA foci appear comparable between SW480 and SW620, whereas in Figure 2B this seems to be much lower in SW620 compared to SW480. Could the authors clarify this discrepancy?

The difference in baseline PLA foci between Fig. 2A and 2B reflects a known sensitivity of the PLA assay to cell confluency. As these two experiments were performed at different confluencies, direct cross-panel comparison is not appropriate. For this reason, all quantitative comparisons in the manuscript are made strictly within the same plate, the same PLA reaction, and between wells with comparable confluency, which avoids introducing bias from these technical variables. For clarity, we plan to incorporate the above information into the Methods section. To validate assay specificity within each experiment, we confirmed that EdU-positive cells consistently showed higher PLA foci counts than EdU-negative cells from the same wells, demonstrating that quantification reflects genuine PCNA-associated signal above background. With this internal validation in place, each panel's comparisons remain valid and interpretable on their own terms.

1. Is the cleavage-termination distance metric influenced by gene length? If so, should this parameter be normalised to gene length to avoid potential bias?

No, gene length is not a bias in the cleavage-termination distance.

• We performed correlation analysis and there is no significant correlation between the cleavage-termination distance and gene length, in any of cell line pairs in our model: HCT116 vs 1CT (spearman r=0.001, p=0.945); SW480 vs 1CT (spearman r=0.036, p=0.0654); SW620 vs 1CT (spearman r=-0.018, p=0.325).
• Additionally, we quantified the decrease in cleavage-termination distance on the very same gene, just in different cell lines. We will incorporate this result into the manuscript.

  1. The data and analysis scripts generated in this study have not yet been made publicly available and therefore cannot be fully evaluated.

We apologize for this omission. The revised manuscript will contain the link to our publicly available scripts in GitHub and the GEO access.

**Referees cross-commenting**

I agree with the reports from both Reviewer #1 and Reviewer #2.

I would like to thank Reviewer #1 for pointing out my mistaken. The authors did not use JTE-607 to study APA; rather, they studied the differences in APA between cell lines. I apologise for the confusion.

Reviewer #3 (Significance (Required)):

General assessment: This study investigates the contribution of pre-mRNA 3′ end processing and transcription termination to colorectal cancer (CRC) biology using a combination of cell line comparisons (primary versus metastatic tumours), chemical, and RNAi perturbations, and bioinformatic analyses.

The major strengths of the work include: • The use of CRC cell lines representing normal, primary, and metastatic states, including matched primary and metastatic lines derived from the same patient. • A systematic analysis of alternative polyadenylation (APA) and transcription termination, revealing a potential uncoupling between these two closely related processes. • The introduction of a novel quantitative metric-cleavage-termination distance-to examine the relationship between PAS usage and RNAPII termination. • The identification of a negative association between cleavage-termination distance and gene expression, suggesting an additional regulatory layer influencing gene expression.

However, certain limitations should be considered: • The generalisability of conclusions regarding metastatic CRC is limited by reliance on a single metastatic cell line.

We believe that the experiments we outlined above in response to Reviewer #3 point 1 will allow us to extend the generalizability of conclusion.

• The translational relevance of the findings could be further strengthened through patient-level or clinical data analysis.

We agree with the reviewer. Due to technical limitations, it is not possible to perform nascent transcriptomic experiments on patient material at this time. However, we will attempt to strengthen the translational relevance by additional experiments and analysis as indicated in response to Reviewer #3 points 1-3.

Advance: The study proposes potentially novel roles for 3′ end cleavage and transcription termination in regulating gene expression in colorectal cancer. In particular, the conceptual distinction between APA site shifting and transcription termination, together with the introduction of the cleavage-termination distance metric, represents a conceptual advance.

Audience: The work is primarily positioned within basic research. With additional translational context, it may also attract interest from a broader audience.

Field of expertise: transcriptional regulation and bioinformatics

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

The manuscript by Stępień et al. aims to investigate the roles of pre-mRNA 3′ end processing and transcription termination using colorectal cancer (CRC) cell lines (normal colon epithelial cells: 1CT; primary tumours: HCT116 and SW480; metastatic tumour: SW620). By using publicly available proteomic datasets and their cellular models, the authors first demonstrate elevated expression of several cleavage and polyadenylation (CPA) and termination factors, including CPSF73 and PCF11, in CRC cells. They further assess the functional relevance of CPSF73 and PCF11, showing that siRNA-mediated knockdown of these factors reduces colony formation, particularly in primary cancer cell lines. However, they do not observe a clear association between CPA/termination factors and transcription-replication collisions (TRCs), suggesting that TRCs may not underlie the altered colony formation phenotype.

The authors also examine alternative polyadenylation (APA) using the CPSF73 inhibitor JTE-607 and report complex APA patterns: primary tumour cell lines display a bias toward distal APA site usage, whereas the metastatic SW620 line preferentially uses proximal sites. They further evaluate transcription termination and observe a proximal shift (early termination) in primary CRC cells, and to a lesser extent in SW620 cells. Noting the apparent discrepancy between APA site shifting and proximal termination, the authors introduce a new metric termed cleavage-termination distance, defined as the distance between the coordinates of the major PAS and RNAPII termination site. They report an association between shortening of cleavage-termination distance and increased gene expression, which may contribute to the upregulation of cancer-related genes. Overall, this is a well-written manuscript that highlights potential roles of pre-mRNA processing and transcription termination in gene expression control, with implications for cancer biology. Nevertheless, several issues should be addressed to strengthen the study:

Overall, this is a well-written manuscript that reveals potential roles of pre-mRNA processing and transcription termination in gene expression control, with implications for cancer biology. Nevertheless, I have a few comments that may help strengthen the study.

Major comments: 1. The study includes two primary tumour cell lines but only one metastatic cell line (SW620), which is derived from the same patient as SW480. It remains unclear whether the observed effects represent general characteristics of metastatic tumour cells or are specific to this particular cell line. 2. The rationale for focusing on colorectal cancer in this study requires further clarification. Although the Introduction provides a comprehensive review of CPSF73 and PCF11 in other cancer types, evidence specific to colorectal cancer is limited. Are these factors known to be mutated or dysregulated in CRC? Is their expression associated with patient survival? The authors could strengthen their rationale by performing a basic analysis using publicly available datasets (e.g., TCGA), such as evaluating expression levels in tumour versus normal tissue and generating Kaplan-Meier survival curves. 3. In Figure 5 and Supplementary Figure 5, the authors analyse cleavage-termination distance across oncogenes and tumour suppressor genes and observe a negative correlation between cleavage-termination distance and gene expression level. This is an interesting finding and suggests a possible mechanism for enhancing expression of cancer-related genes. It would be valuable to extend this analysis more systematically-for example, by stratifying genes based on cleavage-termination distance and performing gene ontology enrichment analysis / GSEA to identify functional categories enriched among genes with shorter or longer distances. The authors could further relate these gene sets to, for example, distinct phenotypes between primary vs metastatic tumours.

Minor comments: 4. In Figure 2A, the number of RNAPII-PCNA PLA foci appear comparable between SW480 and SW620, whereas in Figure 2B this seems to be much lower in SW620 compared to SW480. Could the authors clarify this discrepancy? 5. Is the cleavage-termination distance metric influenced by gene length? If so, should this parameter be normalised to gene length to avoid potential bias? 6. The data and analysis scripts generated in this study have not yet been made publicly available and therefore cannot be fully evaluated.

Referees cross-commenting

I agree with the reports from both Reviewer #1 and Reviewer #2. I would like to thank Reviewer #1 for pointing out my mistaken. The authors did not use JTE-607 to study APA; rather, they studied the differences in APA between cell lines. I apologise for the confusion.

Significance

General assessment:

This study investigates the contribution of pre-mRNA 3′ end processing and transcription termination to colorectal cancer (CRC) biology using a combination of cell line comparisons (primary versus metastatic tumours), chemical, and RNAi perturbations, and bioinformatic analyses.

The major strengths of the work include:

• The use of CRC cell lines representing normal, primary, and metastatic states, including matched primary and metastatic lines derived from the same patient.
• A systematic analysis of alternative polyadenylation (APA) and transcription termination, revealing a potential uncoupling between these two closely related processes.
• The introduction of a novel quantitative metric-cleavage-termination distance-to examine the relationship between PAS usage and RNAPII termination.
• The identification of a negative association between cleavage-termination distance and gene expression, suggesting an additional regulatory layer influencing gene expression. However, certain limitations should be considered:
• The generalisability of conclusions regarding metastatic CRC is limited by reliance on a single metastatic cell line.
• The translational relevance of the findings could be further strengthened through patient-level or clinical data analysis.

Advance:

The study proposes potentially novel roles for 3′ end cleavage and transcription termination in regulating gene expression in colorectal cancer. In particular, the conceptual distinction between APA site shifting and transcription termination, together with the introduction of the cleavage-termination distance metric, represents a conceptual advance.

Audience: The work is primarily positioned within basic research. With additional translational context, it may also attract interest from a broader audience.

Field of expertise: transcriptional regulation and bioinformatics

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Referee #2

Evidence, reproducibility and clarity

Factors involved in pre-mRNA cleavage and polyadenylation (CPA) are upregulated in many cancers and have been found to be associated with poor prognosis. In their manuscript "Proximity of pre-mRNA 3′ end processing and transcription termination predicts enhanced gene expression", Stepien et al. use colorectal cancer (CRC)-derived cell lines as a model of CPA overexpression to study its biological consequences. To this end, the authors initially confirm increased expression of CPA factors in these cell lines and demonstrate that their knock-down strongly decreases the colony-forming ability of primary tumour-derived CRC cells. They further assess various phenotypes that are expected to depend on CPA activity based on the current knowledge in the field, including poly-A site selection, occurrence of transcription-replication conflicts, and the site of transcription termination. Contrary to expectations, they find a proximal shift in transcription termination to be the most prominent change in CRC ell lines with high CPA levels, despite no clear preference for proximal poly-A site usage in these cells, suggesting an uncoupling of both processes. The authors combine their 3'-end mapping data and T4P-mNET-seq data mapping terminating RNAPII to score cleavage-termination distance at individual genes and find shorter distances to correlate with increased gene expression in the different cell lines. Overall, this is a carefully conducted study, and the claims and conclusions are well supported by the data.

I have some minor comments:

1. PLA assay to quantify transcription-replication conflicts (Figure 2). The quantified data looks very convincing and is also in good agreement with the proximal shift in transcription termination that is demonstrated later in the paper. However, the PLA channel signal in the microscopy image examples shown in panel A looks very blurry, and it is hard to imagine that one would be able to count # foci based on this. This may just be an issue with the resolution of the image provided. Apparently, there are much less foci in the treated samples shown in panel B - maybe microscopy images for these could be provided as well? Also, since none of the treatments impact the # of TRCs, it would have been nice to include a positive control known to induce TRCs to demonstrate that the assay works (if such a control is known) - this is optional, and I would not ask to repeat the entire experiment just for this additional control (but maybe the authors have done it and the data is already available?).
2. Figure 2A-C: please include information on number of cells quantified
3. Figure 2C: In the label, please include degron, e.g. HCT116 CPSF73-AID rather than just HCT116
4. Figure 5C: When quantifying nascent txn based on mNET-seq, to which extent would one expect terminally paused RNAPII along the gene body (premature termination events) to contribute to the increased signal? That is, could an increase in stalling be mistaken for an increase in transcription? Based on the metagene plot in Fig 2A it doesn't look like it, but the authors may be able to estimate the effect (if any) from their data.

Significance

The observed uncoupling of poly-A site selection and size of termination window is unexpected and raises important questions on how these coupled processes can be regulated independently.

Strengths of the study:

i) Parallel assessment of different CRC-based cell lines provides evidence of phenotype stability across patients.

ii) Brings together strong technical expertise combining different state-of-the-art methodologies to map and correlate poly-A site usage, site of transcription termination, and levels of nascent transcription within the same cell lines under the same conditions, providing a comprehensive dataset.

Limitations:

i) For the time being, observation limited to CRC cell lines.<br /> ii) Mechanism behind proximal shift of termination to be determined.

I expect this work to be of interest to an audience interested in transcription and regulation of gene expression more broadly, with potential translational relevance for cancer therapy.

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Referee #1

Evidence, reproducibility and clarity

Summary

This study investigates how altered expression of cleavage and polyadenylation (CPA) factors affects alternative polyadenylation (APA), transcription termination and cellular phenotypes in colorectal cancer (CRC) cell lines. The authors combine genetic perturbations of CPA factors with chemical inhibition of CPSF73 and assess effects on clonogenic potential, transcription-replication conflicts, APA profiles, and transcription termination-associated RNAPII phosphorylation patterns. The main comparisons are performed between healthy (1CT), primary tumour (SW480, HCT116) and metastatic (SW620) cell lines, which are reported to contain altered expression levels of CPA factors.

The data suggest differential dependence on CPA factors between primary tumour-derived and metastatic CRC cell lines, as well as changes in transcription termination patterns. The data are overall well-presented with clear figures. However, in several cases the strength of the conclusions appears to exceed the support provided by the data, and alternative interpretations should be considered.

Major comments

1. Clonogenic sensitivity to CPA factor perturbation and comparability of clonogenic assays between cell lines:
   • The data indicate that clonogenic potential in SW480 is strongly dependent on CPSF73 and PCF11, whereas SW620 appear less sensitive. However, the interpretation is complicated by differences in depletion efficiencies. In SW620 cells, PCF11 depletion appears inefficient, and protein levels remain higher than in siLUC-treated SW480 cells (Fig. 1D and S1C; also in comparison to 1CT by inference of Fig. 1C). Thus, the apparent resistance of SW620 cells could reflect insufficient depletion rather than true biological tolerance. The effectiveness of siCPSF73 treatments is difficult to assess from the presented data. Quantification of protein knockdown levels should be provided and incorporated into the interpretation.
   • In Fig. 1D, 1E, and S1D, colony formation of DMSO- or siLUC-treated SW620 and SW480 cells differs markedly in absolute terms. However, the graphs are normalized separately for each cell line, which obscures this difference. This raises two concerns: First, the baseline clonogenic capacity differs between the lines and should be discussed. Second, it is unclear whether direct comparisons between cell lines are valid when normalization is performed independently. For example, in absolute terms, 1 µM JTE-607 appears to have a similar effect in SW620 cells as 5 µM in SW480 cells, which would contradict the conclusion that metastatic cells are more tolerant to CPA perturbations. This issue should be explicitly addressed.
2. Interpretation of transcription termination markers:
   • The study uses RNAPII T4ph as a marker of transcription termination, which is well justified based on the ref. [30], but still the mechanistic basis of this modification is not fully understood. Changes in T4ph localization are interpreted as consequences of CPA activity, but possible differences in kinase or phosphatase activities between cell lines are not considered that could affect the T4ph levels or localization. Therefore, conclusions based solely on T4ph redistribution should be presented with greater caution, and alternative explanations should be acknowledged.
   • Line 240 states that premature termination is increased in primary tumour cells. However, the data show increased T4ph signal (Fig. 4B) but no change in total RNAPII occupancy in gene bodies (Fig. 4A). This does not directly demonstrate increased termination. Additional evidence or a more cautious interpretation would be appropriate.
3. Cleavage-termination distance as a predictor of transcript levels:
   • Figure 5A presents median distances across all genes. It would be informative to perform a gene-wise comparison between cell lines (difference in cleavage-T4ph distance for the same gene, e.g. in 1CT vs. HCT116, individual differences plotted across all genes). This analysis could help clarify how frequently individual genes experience the effect (shortening of the cleavage-T4ph distance between 1CT and tumour cells) that is observed globally.
   • The manuscript claims that proximity between pre-mRNA 3′-end cleavage and transcription termination predicts increased nuclear transcript levels. However, the correlation coefficients are small (Spearman r ~ -0.2 at most), indicating weak predictive power. Therefore, the use of the term "predicts," especially in the manuscript title, appears to overstate the strength of the relationship. The authors should either moderate this claim or provide additional analysis to support stronger predictive value.

Minor comments

• Figures 1B and S1A: The discontinuous y-axis makes it difficult to assess relative protein level differences between normal and cancer samples. Statistical testing should be included to evaluate significance.
• Lines 217-218: The text should emphasize that nuclear RNA abundance may not reflect cytoplasmic mRNA levels, particularly when APA alters 3′UTRs and may affect mRNA stability.
• Lines 261-264: The cleavage-termination distance metric should be more clearly defined as the distance between the polyadenylation site and the T4ph signal peak.

Referees cross-commenting

Reviewer #3: On the contrary to implied in the reviewer report, this manuscript does not report the effects of CPSF73 inhibitor JTE-607 on APA. On this note, as the authors discuss uncoupling of cleavage and transcription termination, they could consider (this is not a request) testing how the cleavage inhibitor JTE-607 impacts the distribution of transcription termination marker T4ph, and whether the effects would be different in different cell lines where the coupling appears to be different. This could give mechanistic insights into the sources of the differences between cell lines.

Significance

This study addresses an important question in RNA biology and cancer research: how altered expression or pharmacological targeting of CPA factors affects alternative polyadenylation, transcription termination, and cellular phenotypes in CRC models. This topic is timely, as CPSF73 has been proposed as a therapeutic target, making it important to understand the molecular and cellular consequences of modulating CPA factor activities. A key strength and robust finding of the study is the identification of unexpected relationships between pre-mRNA 3′-end processing and transcription termination during CRC progression. Notably, the authors report that changes in alternative polyadenylation and transcription termination appear to be uncoupled and may even occur in opposite directions. This challenges simplified models in which these processes are tightly coordinated and suggests that their (mis)regulation in cancer cells may be more complex than previously appreciated. Secondly, the study provides an interesting observation that gene-specific changes in cleavage-T4ph distance correlate negatively with changes in nuclear levels of processed transcripts. This suggests a potential relationship between the spatial coupling of 3′-end processing and transcription termination and transcript abundance. If validated mechanistically, this could represent a conceptual advance in understanding how transcription termination dynamics influence gene expression outputs. However, the observed correlations are relatively weak, and the mechanistic basis of this relationship remains unclear. As such, this advance is primarily descriptive at this stage. Several interpretations of experimental data would benefit from more cautious framing or additional analysis. In particular, the relationship between changes in CPA factor expression levels and sensitivity to the CPSF73 inhibitor JTE-607 across CRC cell lines remains unclear from the presented data. This work will be of interest primarily to basic researchers in RNA processing and transcription regulation, gene expression control, cancer cell biology and pharmacological targeting of RNA-processing machineries. Reviewer field of expertise: My expertise is in RNA processing and gene regulation. I do not have specific expertise clinical oncology or cancer biology.

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Referee #2

Evidence, reproducibility and clarity

The authors develop a method that extracts functional properties clusters cells from single-cell RNA sequencing using machine learning techniques.

As it stands, there are several major shortcomings in the presentation of the work:

• The motivation for the method is not well explained. Certainly analyses of single cell transcriptomics data do not capture the full state or trajectory, however there isn't any concrete example of the problem that this method intends to solve, nor how/why existing methods fail to capture this.
• No motivation is given for any of the approaches that feature in the method, and therefore there is no consistent logical thread that a reader can follow to be convinced that the results are plausible.
• Methods are not sufficiently explained.

For example: There is no indication of how the original graph is obtained, nor what is diffusing in the 'graph diffusion' method. Statements like "The term 'sparse' indicates the process of sparsifying the matrix." does not explain anything about the actual process of making the matrix sparse. This could perhaps be understood in terms of a 'sparse' function in a particular linear algebra package, which would implicitly make this procedure concrete, but this is not mentioned.

Section 2.2.2 mentions a reinforcement learning scheme, however none of the following explanation describes anything related to the commonly accepted reinforcement learning literature, and several quantities (such as the loss) remain undefined. Similarly, section 2.2.3 mentions the BERT pre-trained transformer without indicating how specifically it was modified or trained for this particular purpose, except perhaps in Figure 4 which itself is intensely confusing. Again in this section the authors mention a 'genetic algorithm' with no reference to any commonly accepted approaches used in the development of genetic algorithms for optimisation, and with no explanation of what exactly is optimised or how convergence is monitored.

No code implementation is provided, and therefore it is impossible to use this to understand any of the methodology, and renders it impossible to reproduce.

• Where mathematical notation is used it is incredibly confusing to read, using multiple symbols for different concepts, and not appearing to conform to any commonly accepted convention. In some cases, these are missing completely, for example on page 6, rendering it entirely impossible to follow.
• The results do not support the assertions made about the method.

No explanation of the alternative methods is given in section 3.1, nor why they are expected to perform the tasks chosen, or what the configuration of these models are and whether these have been optimised. In Table 2 many alternative methods are listed, however there is no explanation why only a small subset were chosen for comparison, nor what information the authors base their conclusions on (whether these were actually executed for this purpose, or whether they were interpreted from the paper).

Metrics such as 'accuracy' are not defined, and are the only numerical evaluation of the method, whereas one would expect considerably more detailed evaluation of the claims, such as in the CoSpar paper.

Section 2.4 mentions 'Details of scRNA-seq data processing and experimental methods are shown in the Supplementary Appendix 6 - Animal Processing.', however I have no supplementary material titled 'Appendix 6', and nothing at all that documents the scRNA-Seq pipeline.

Section 3.2 seems to describe a very manual procedure for identifying these clusters, and seems to bear no relation to the TOGGLE procedure defined previously, so it's not clear how good an indication this is of the performance of the algorithm. Furthermore, the subsequent results seem to rarely refer to the TOGGLE method at all, and lack any meaningful comparison to alternative methods or why TOGGLE is essential for obtaining these results.

In many cases the plots in this section are so distorted by compression that making out the text and the points is essentially impossible, and so I cannot comment on any of these.

I would strongly recommend that the methodology of the paper is greatly expanded to cover exactly what is done, such that it is possible to reproduce in its entirety. Asking a third party who is an expert in machine learning to read through the descriptions and the mathematics would also be highly beneficial to ensure their correctness. Furthermore, it is essential that all of the claims made in the introduction and throughout the paper be systematically and explicitly validated in the results. If this cannot be done on real data, where ground-truth labels and trajectories are hard to come by, some evidence for these claims could be acquired by evaluation on simulated data.

Significance

The inference of cell state and trajectories from single cell RNA sequencing is a timely and important task in computational biology, with many important downstream applications. The method described in this paper aims to distinguish functionally distinct cell populations that exhibit small differences in transcript counts. However, it is not precisely articulated why the complicated approach proposed here is advantageous over simpler more conventional approaches, such as graph clustering, random-walk based methods such as CoSpar, or trajectory inference based on ODE kinetics such as in scVelo.

Furthermore, the methods described are exceptionally vague and hard to follow, with mathematical descriptions and naming schemes that are inconsistent with the commonly accepted literature of the techniques referenced. Therefore it is also difficult for even a well-prepared reader to come to their own conclusions as to the performance and applicability of the proposed approach. This issue is compounded by the fact that there is very little in the way of validation of the specific claims made of the method, let alone in relation to alternative methods.

The study would be greatly improved by expanded methods sections, documenting in detail what is done at each stage. Where existing work is referenced without an exact description, how the implementation differs from the reference must be addressed. Most of the description is currently in text form only, which is wholly insufficient for the kind of complex mathematical operations described. Furthermore, many of the claims throughout the paper go unaddressed in the results, where there are only a few accuracy metrics and comparisons of results, and there is no attempt to rigorously demonstrate an advantage of any of the novel components presented (for example, in an ablation study). Expanding these numerical metrics and comparisons across all applications of the method is essential for demonstrating the assertions of the paper - for example, constructing a metric for the comparison of the TOGGLE and ground-truth UMAP comparisons. In cases where there is no real ground truth in the data, simulated datasets could be used to demonstrate the plausible performance of TOGGLE in ideal scenarios.

My expertise is in computational biology and machine learning, with a background in physics.

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Referee #1

Evidence, reproducibility and clarity

Overall Assessment

The manuscript addresses an important problem-inferring subtle functional states from single-time-point scRNA-seq. However, essential methodological details are missing, several claims lack rigorous support, and key computational steps cannot be reproduced from the current description. The biological experiments validate ferroptosis itself, but do not validate the correctness of the inferred trajectories or cluster boundaries.

Major Comments

1. In Step 1 of TOGGLE (Figure 1), the method employs graph diffusion and emphasizes that the resulting asymmetric distance matrix encodes additional information. In fact, the entire downstream TOGGLE framework is built upon this graph and its diffusion-based similarity. However, the manuscript currently lacks essential information regarding this core component: 1) it does not explain how the asymmetric distance matrix is generated, nor does it provide explicit formulas or computational steps; 2) it does not specify which type of diffusion operator is used; 3) it is unclear how the underlying graph is constructed from the expression matrix-e.g., whether a standard kNN graph is used and whether edge weights are normalized.
2. Although the manuscript demonstrates the biological usefulness of TOGGLE across several datasets and provides experimental validation in multiple systems, the method still lacks essential ablation analyses and performance benchmarking. These components are critical for establishing the stability, robustness, and necessity of each part of the proposed framework. Without systematic evaluation-such as comparisons to existing trajectory or state-inference methods, or ablations of key modules (diffusion construction, boundary detection, masking, GA-based merging)-it remains difficult to assess whether TOGGLE's improvements are due to the core algorithmic design or to dataset-specific behaviors. Incorporating these analyses would substantially strengthen the evidence supporting the method's reliability and generalizability.
3. I find the methodological description insufficiently clear. The overall algorithmic framework appears to be assembled from multiple existing computational components without a unified or coherent theoretical formulation. As a result, the rationale behind each module and the mathematical connections between them are not rigorously established. In addition, the mathematical expressions throughout the manuscript lack standardized notation and clarity. For example, vectors and matrices should be consistently denoted using bold symbols, and expressions such as "cov_D" are not appropriate for describing covariance matrices in a formal mathematical context. The absence of precise notation and properly structured equations makes it difficult for readers to understand, evaluate, or reproduce the proposed method. A clearer and more rigorous mathematical exposition is necessary to support the validity of the algorithmic design.
4. Key components (δ computation, binary assignment, recursion criteria, optimization objective) lack formal definitions or pseudocode. The "reinforcement-like" description is conceptual rather than methodological.
5. Both masking and GA introduce stochasticity and complexity. Their necessity is not demonstrated, and no ablation study tests whether they contribute to performance or stability.
6. Masking ratio, GA population size, mutation rate, stopping criteria, and the details of pseudotime usage are all unspecified, making the computational procedure difficult to reproduce. Moreover, given the presence of multiple stochastic components-including masking, genetic-algorithm iterations, and graph-related randomness-the manuscript should evaluate the stability of the method under different random seeds or bootstrap resampling. Without clearly defined parameters and robustness analyses, it is challenging to assess the reliability and reproducibility of the proposed framework.

Minor Comments

1. "cellular neighborhoods" requires a precise definition.
2. Some figures (e.g., Fig. 2) are schematic and would benefit from quantitative clarification.

Significance

Advancement：If clarified and rigorously validated, TOGGLE could become a useful tool for trajectory-free state inference. Currently, the novelty lies more in application breadth than in methodological rigor.

Audience: Likely audiences include computational biologists, neuroscientists studying ferroptosis, and researchers working on NSC epigenetics. Usage beyond these areas depends on methodological clarification.

Expertise: Keywords: single-cell transcriptomics, graph diffusion, clustering algorithms, trajectory inference, statistical modeling. I am comfortable evaluating the computational components; biological assays are evaluated from standard computational-biology perspective.

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Referee #3

Evidence, reproducibility and clarity

Guo et. al, Wnt/β-catenin in the muscle spindle

Guo and colleagues investigated a role of canonical wnt signaling in the muscle spindle. Muscle spindles are formed by myofibers upon innervation by proprioceptive sensory neurons. The signal for induction of the spindle, Nrg1, is provided by the proprioceptive neuron and induces the expression of immediate early genes like Egr3 in the emerging spindle. Subsequently, bag1/2 and chain fibers are formed, and a capsule is generated around the spindle. Besides the inducing signal, little is known about spindle development, and to my knowledge all other work remained descriptive.

To work with muscle spindles is demanding as the spindles are very rare in muscles. The authors have developed new approaches like collecting spindles for RNAseq analyses that allow them to molecularly analyze the spindle.

In the manuscript, the authors characterize wnt signaling in muscle spindle development. They show data from the Axin2-GFP mouse strain (Axin2 is a well-known target of canonical wnt signaling). Their data indicate that both extra- and intrafusal fibers express Axin2 at P0 and P5; at P25 and P40 Axin2 is maintained in bag2 fibers and capsule cells of spindles and downregulated in other myofibers. This indicates that canonical wnt signaling is initially active in all fibers, and subsequently restricted to bag1 fibers and capsule cells.

Two mouse strains are used to conditionally mutate β-catenin, the transducer of canonical wnt signals, in the spindle: the first strain relies on the use of Egr3-Cre (mutates β-catenin in intrafusal fibers and capsule cells; recombination sets in presumably shortly after E15.5). The second strain uses HSACreERT2 to mutate β-catenin (recombination is induced in all myofibers after tamoxifen treatment). In the data provided, tamoxifen was injected at P5 and the animals were analyzed at P25 or later. Molecular phenotyping is done on the Egr3-Cre strain using RNAseq showing around 750 down- and 300 upregulated genes in isolated muscle spindles from β-catenin mutants.

Other phenotyping data: Histology (Egr3-Cre):1) changes in the distribution of GLUT1 in the spindle, 2) VCAN downregulation in capsule cells of the mutant; 3) abnormal aggregation of nuclei in bag2 fibers, 4) abnormal annulospiral morphology, i.e. proprioceptive neuronal endings are abnormal.<br /> Histology (HSACreERT2): 1,2) GLUT1 and VCAN unaffected; 3) bag2 nuclear aggregation is normal; 4) abnormal annulospiral morphology, 5) abnormal gait. The authors assign the differences in phenotypes to the differences in cell type specificity of recombination (Egr3-Cre: intrafusal fibers and capsule cells; HSACreERT2: intra- and extrafusal fibers). This indicates that 1) Wnt/β-catenin affects annulospiral endings indirectly via a primary deficit in bag2 fibers and 2) nuclear aggregation phenotype in bag2 fibers is caused indirectly via a primary deficit in capsule cells and 3) a cell autonomous function Wnt/β-catenin exists in capsule cells. Overall, the work is carefully done, and the data are presented clearly. The phenotypes are relatively mild, in particular the behavioral consequences of the mutation.

I have some major points that should be discussed and taken into account in the writing of the paper.

1. Developmental phenotypes. The authors claim the phenotypes observed are caused by developmental deficits, but the animals are only analyzed at P25 (histology and RNAseq) or later time points. From the data shown it cannot be excluded that the spindle is formed correctly but that spindle maintenance is impaired. Additional time points would be needed to convincingly argue a developmental phenotype. Specifically, analysis of a time point when control and mutant spindles have similar histology is needed, in order to argue that subsequent developmental steps are impaired.
2. Differences in phenotypes in the two strains. Can the authors be sure that differences in phenotypes observed in Egr3-Cre and HSACreERT2 lines are exclusively due to cell type specificity of recombination, and not due to differences in recombination efficacies? This is particularly important for the syncytial fibers. Incomplete recombination in a fiber might allow nuclei that have not recombined to provide sufficient β-catenin for signaling in the entire fiber.
3. Please provide data that show that β-catenin is expressed in capsule cells.

Minor

The following sentence refers to the wrong figure (should refer to Fig. 4): While mutant loops had similar widths, loop number was reduced and the distance between loops increased (Figure 3G-G').

Significance

Guo and colleagues investigated a role of canonical wnt signaling in the muscle spindle. Muscle spindles are formed by myofibers upon innervation by proprioceptive sensory neurons. The signal for induction of the spindle, Nrg1, is provided by the proprioceptive neuron and induces the expression of immediate early genes like Egr3 in the emerging spindle. Subsequently, bag1/2 and chain fibers are formed, and a capsule is generated around the spindle. Besides the inducing signal, little is known about spindle development, and to my knowledge all other work remained descriptive.

To work with muscle spindles is demanding as the spindles are very rare in muscles. The authors have developed new approaches like collecting spindles for RNAseq analyses that allow them to molecularly analyze the spindle.

In the manuscript, the authors characterize wnt signaling in muscle spindle development. They show data from the Axin2-GFP mouse strain (Axin2 is a well-known target of canonical wnt signaling). Their data indicate that both extra- and intrafusal fibers express Axin2 at P0 and P5; at P25 and P40 Axin2 is maintained in bag2 fibers and capsule cells of spindles and downregulated in other myofibers. This indicates that canonical wnt signaling is initially active in all fibers, and subsequently restricted to bag1 fibers and capsule cells.

Two mouse strains are used to conditionally mutate β-catenin, the transducer of canonical wnt signals, in the spindle: the first strain relies on the use of Egr3-Cre (mutates β-catenin in intrafusal fibers and capsule cells; recombination sets in presumably shortly after E15.5). The second strain uses HSACreERT2 to mutate β-catenin (recombination is induced in all myofibers after tamoxifen treatment). In the data provided, tamoxifen was injected at P5 and the animals were analyzed at P25 or later. Molecular phenotyping is done on the Egr3-Cre strain using RNAseq showing around 750 down- and 300 upregulated genes in isolated muscle spindles from β-catenin mutants.

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Referee #2

Evidence, reproducibility and clarity

In their study the authors address an important aspect in developmental neurobiology. In particular, they investigate the molecular underpinnings of muscle spindle development in the mouse. Muscle spindles are essential components to transmit muscle stretch and proprioceptive feedback to the spinal cord. They first analyze preexisting muscle spindle specific gene expression patterns that have been established before. They find an intriguing enrichment of expression of components of the Wnt/beta-catenin pathway. Inspired by these findings the authors next genetically deleted specific components from capsule and intrafusal spindle fibers during embryogenesis. They found profound gene expression changes and morphological alterations in the spindle fibers but also at the sensory proprioceptive nerve endings. Finally, the authors deleted beta-catenin at postnatal stages and detected significant defects in proprioception function. Altogether, they conclude that beta-catenin signaling exerts important function in muscle spindle development through cell-autonomous (spindle intrinsic) and non-cell-autonomous (affecting nerve terminals and proprioceptive functions) mechanisms.

Overall the study is excellently conceived, the experiments performed at very high standards and the results were interpreted with great care. The manuscript is very well written and the data is presented neatly. In my opinion there are just a few very minor items that the authors could address to improve the reading experience.

1. In Figure 1B, the font color in the blue boxes are not clearly readable and I recommend to use darker color tone or even black.
2. Figure 1C-H, it would be useful to outline the capsule and fiber compartments in the fluorescent panels to improve the orientation and better appreciation of the expressed genes.
3. Figure 3C'-3C'', the authors should define the meaning of the red and black labelled gene names.
4. Figure 3C', the yellow writing is hard to read, I suggest to use darker color tone.
5. Figure 4, the authors should write the proper genotype in the boxes and in italic font.
6. Figure 5, the authors should write the proper genotype in the boxes and in italic font.
7. In the introduction, the authors could cite a few more (perhaps major reviews) about the Wnt/beta-catenin biochemical functions. Ideally after the first sentence in the respective paragraph.

Significance

Proprioception is an essential process for controlling postures and movement. The anatomical development of the muscle spindles, that are responsible for detecting muscle stretch and transmitting proprioceptive feedback to the spinal cord, has been quite well described. However, the molecular mechanisms that regulate the development of the muscle spindles with the attached proprioceptive nerve endings are not well understood. To address this gap in our knowledge the authors evaluated muscle spindle specific gene expression and probed the function of the Wnt/beta-catenin pathway (highly specifically expressed in spindle components) in muscle spindle development and function. They found striking and significant deficits in muscle spindle development and proprioception upon muscle spindle specific ablation of beta-catenin. Altogether, they conclude that beta-catenin signaling exerts important function in muscle spindle development through cell-autonomous (spindle intrinsic) and non-cell-autonomous (affecting nerve terminals and proprioceptive functions) mechanisms. Conclusively, the data and findings in the present study reflect a true advance and provide new insights into the molecular mechanisms that drive muscle spindle development and therefore proprioception.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors demonstrate the importance and roles of Wnt/β-catenin signalling in mammalian muscle spindle development and maintenance.

Major comments:

The paper is very well and clearly written with full details of the data and methods. The results, statistical analyses, and conclusions are convincing without any need for further experiments.

Minor comments:

• In the Introduction (paragraph 3) the authors state "Extensive morphological studies have shown that muscle spindle development begins around embryonic day (E) 14, when slow myofibers first contact proprioceptive axons and differentiate into intrafusal fibers in a sequential process." I would suggest "Extensive morphological studies have shown that muscle spindle development in the mouse begins around embryonic day (E) 14, when proprioceptive axons first contact primary myotubes initiating the differentiation of primary and secondary myotubes into intrafusal fibers in a sequential process." In the same paragraph it is stated that "Recent work has shown that Lrp4 expression in intrafusal fibers is necessary to maintain the sensory synapses of annulospiral endings..." Sensory endings, including those of muscle spindles are not usually, nor conventionally, regarded as synapses.
• Legend to Fig 1 (F,G; inset in G shows enlargement of Fzd2) Fzd2 to read Fzd10.
• Legend to Fig 2 (A) "Dotted lines demarcate equatorial region of spindles." I suggest "Dotted lines demarcate areas enlarged in B'-C', including equatorial regions of spindles."
• Paragraph beginning "Next, to associate these changes..." "Surprisingly, for intrafusal genes, the most enriched GO term was "neuron projection morphogenesis,..." Why is this surprising?
• Legend to Fig 4 "a shorter spindle height in mutants" This is unclear; I suggest "a smaller spindles diameter" would be clearer. Similarly "and shorter nucleus height" is unclear; I suggest "and smaller nuclear accumulation diameter".
• Legend to Fig 5 Again, I think "spindle height" would be clearer as "spindle diameter". Specific experimental issues that are easily addressable.
• The figures are all clear, in some cases when sufficiently enlarged, but careful attention needs to be paid to their final enlargements to ensure that the essential details remain clearly visible.

Referees cross-commenting

It is satisfying to see that all three reviewers agree on the importance of this paper, and that two reviewers clearly agree that no further experimental work is necessary to support the conclusions reached by the authors.

Significance

This is an important work of major significance in the area of muscle spindle studies, and in the wider field of the genetic basis of the integrated development of complex sense organs.

My expertise is in the structure, ultrastructure, immunohistochemistry, and physiology of muscle spindles.

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Reply to the reviewers

Point-by-point response to Reviewer comments:

We copied the Reviewer comments below in italics. Revisions we propose in response to Reviewer comments are underlined.

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

The manuscript by Yin et al investigates how epidermal cells shape somatosensory neuron (SSN) morphology and function through selective ensheathment in Drosophila. This study builds on earlier work by another group showing that the phagocytic receptor Draper (Drpr) as a crucial epidermal factor that is important for dendrite pruning and clearance. In the present study, the authors how that Drpr also functions in the epidermis to establish the characteristic stretches of epidermal ensheathment of dendrite arborization neurons in the fruit fly Drosophila melanogaster. This is particularly true for highly branched types of dendrites but ont dendrites that show simpler branching patterns. Overexpression of Drpr increases ensheathment and nociceptor sensitivity, linking molecular recognition to sensory modulation. Further, Drpr is known to recognize phosphatidylserine (PS) on neurites to promote ensheathment and the authors show localization of a reporter for PS with epidermal membranes. Genetic manipulations that reduce PS results in a reduction in epidermal sheaths and the chemokine-like protein Orion promoting Drpr/PS interactions is required for these processes. Overall, the manuscript is well written, although at times maybe primarily for a fly audience. Reach could be improved by making it more accessible to a non-fly audience. The observation that Drpr is not only required for removing damaged or degenerating dendrites but also for their correct ensheathment of highly branched dendrites presents an important finding that could be of interest for a wider audience provided the following points are adequately addressed:

1. • The Introduction could be further elaborated to help readers understand the significance of epidermal dendrite ensheathment. Addressing the following points may achieve this: (i) The Introduction would benefit from including details on developmental disorders and neurological diseases associated with defects or abnormalities in dendrite ensheathment.*

We appreciate this suggestion. We allude to possible connections between ensheathment defects and human disease in the discussion but agree that it would be appropriate for the introduction; we will underscore this possible connection more clearly in our revised manuscript. We note studies of epidermal ensheathment are limited in mammalian systems, so links between dysregulation of epidermal ensheathment and disease have not been firmly established.

(ii) In lines 74-79, it is unclear whether the described findings are conserved across evolution or were demonstrated in a specific model organism.

The Reviewer refers to our statement about similarities in the cellular mechanism of epidermal ensheathment and phagocytosis. Indeed, these features are evolutionarily conserved in vertebrates, and we agree that it is worthwhile to emphasize this point. We added a statement underscoring the evolutionary conservation of the morphogenetic mechanism along with the relevant citation.

(iii) Including a description of the known literature on phagocytosis in this process would help readers better understand the novelty and significance of this study.

We agree with the Reviewer. In our revised introduction we will include a more detailed description of key features of phagocytic engulfment and highlight the salient differences between ensheathment and phagocytosis including the failure to complete the endocytic event in ensheathment and the persistence of PIP2 at the membrane.

(iv) Details of published Draper function in Han et al 2014 should be elaborated along with unanswered question that is addressed in this study.

The Han et al 2014 study established that epidermal cells, not Drosophila hemocytes (professional phagocytes), are primarily responsible for phagocytic clearance of damaged dendrites in the periphery. Similarly, the Rasmussen et al 2015 study we cite established that skin cells in vertebrates (zebrafish) act as primary phagocytes in removal of damaged peripheral neurites. These studies demonstrate the phagocytic capacity of epidermal cells, particularly in recognition of somatosensory neurites, and the Han study demonstrates that Draper is required for this epidermal phagocytosis. Neither of these studies addresses mechanisms of epidermal ensheathment; we will clarify this point in our revised introduction.

• It is unclear why the authors focus exclusively on Drpr and Crq, without addressing emp and CG4006, both of which show higher expression levels than the former. Moreover, the conclusion that 14 out of 16 engulfment receptor genes have no role based solely on RNAi knockdown experiments is a very strong statement that may requires additional validation. The authors should provide evidence that the RNAi knockdowns achieved complete loss of gene function to support their claim about 16 engulfment receptors. In addition, at most the authors can conclude that the tested genes are individually not required.*

The Reviewer makes several points that warrant discussion. First, the Reviewer asks “why the authors focus exclusively on Drpr and Crq, without addressing emp and CG40066.” The rationale for focusing on Drpr and Crq in our discussion of the expression data is that both Drpr and Crq function in phagocytic engulfment of damaged neurites. Our focus on Drpr for the remainder of the study is guided by the knockdown phenotypes; if either emp, CG40066, or any other receptor showed robust and reproducible effects on ensheathment we would have discussed them at length. Indeed, we identified a potentially novel ensheathment phenotype for NimB4 and devote a small portion of our discussion to its possible function. However, our primary focus in this study was to identify phagocytic receptors required for epidermal ensheathment of somatosensory neurites and drpr was the top hit from our RNAi screen.

Second, we acknowledge that RNAi knockdown is often incomplete and without additional validation a negative result using RNAi is difficult to interpret. In our original text we state: “epidermal RNAi of 14/16 engulfment receptor genes had no significant effect on the extent of dendrite ensheathment in third instar larvae (Figure 1, F and G), consistent with the notion that most epidermal engulfment receptors are dispensable for dendrite ensheathment.” We do not claim that other receptors have “no role”, simply that our results are consistent with the interpretation that most receptors are dispensable. Furthermore, we acknowledge that multiple other receptors likely contribute to other aspects of ensheathment (lines 131-145; NimB4 knockdown causes an “empty sheath” phenotype). However, the Reviewer’s comments convince us that we should more clearly word our interpretation of the negative RNAi results more to reflect the limitations of the approach; we will incorporate this into our revision.

Third, the Reviewer brings up the very important point that receptor redundancy could mask phenotypes. Indeed, our studies suggest that additional pathways likely function in parallel with Drpr. We agree that potential redundancy is an important consideration and absolutely warrants discussion in this section of the results; we will add this to our revised text and we have already updated the statement in the results to read “most epidermal phagocytic receptors are individually dispensable for dendrite ensheathment.”

The final point the Review makes is that analysis of the knockdown efficacy is warranted if we want to make strong claims about gene function for other receptors. We agree that this would be an important first step, but in many cases protein perdurance masks RNAi phenotypes as well. So, efficient knockdown alone is not enough to make concrete conclusions about gene function in this developmental context.

• What kind of genes are crq and ea?*

Crq is a Scavenger receptor and Eater is a Nimrod-family receptor (indicated in Figure 1A).

• Comparing Figures 1C and 1E, it appears that drpr knockdown has a differential effect on epidermal dendrite ensheathment between main and secondary branches. If this observation is correct, separate quantification for each branch type would be more appropriate, along with an explanation for the observed differences.*

We agree with the Reviewer’s assessment that ensheathment appears to be largely absent on terminal dendrites following drpr knockdown but some ensheathment persists on major dendrites. In prior published studies we demonstrated that terminal branches are less extensively ensheathed than primary dendrites in wild-type larvae (Jiang et al 2019 eLife). We will provide this important context in our revised submission. We hypothesize that Drpr uniformly affects ensheathment across the arbor but agree with the Reviewer that quantification is warranted to evaluate this hypothesis. We will add this analysis to our revised submission.

• For Figure 1K, it would be informative to examine how drpr knockdown affects dendrite length in these neurons.*

We agree with the Reviewer. We demonstrate that drpr null mutants have exuberant terminal branching, but we have not yet analyzed effects of epidermal drpr RNAi. We will add this analysis to our revised manuscript.

• For Drpr expression (Figure 3), it would be valuable to highlight any differences in expression between primary and secondary dendritic branches.*

The Reviewer’s question about Drpr distribution at sites of ensheathment will be particularly relevant if we observe differential impacts of Drpr knockdown on ensheathment at primary and higher order dendrites. In our initial submission we showed that >70% of PIP2+ (Fig. 3B) and cora+ (Fig. 3D) epidermal sheaths also exhibited Drpr accumulation; we likewise showed that Drpr accumulation adjacent to dendrites only occurred at sites labeled by the sheath marker cora (Fig. 3G). In our revised submission, we will examine whether Drpr accumulation is more prevalent at sites of PIP2 accumulation on main branches compared to terminal branches.

• Removing drpr leads to excessive branching of SSN dendrites. Does overexpression of drpr affect dendrite morphology in the opposite manner?*

The Reviewer asks an intriguing question about effects of drpr overexpression. We have not examined effects of epidermal drpr overexpression on dendrite morphogenesis, but we will add these experiments to our revised manuscript.

• Although drpr role in dendrite ensheathment is well explored, the interactions between drpr and PS seem underexplored. For example, do the changes in ensheathment as a result of manipulating PS levels require drpr? Does changing PS levels affect Drpr localization or levels?*

The Reviewer raises two questions about the relationship between PS exposure and Drpr.

First, they inquire whether changes in ensheathment resulting from manipulating PS levels require Drpr. We show that overexpressing the ATP8a flippase in C4da neurons, which limits PS exposure, limits the extent of ensheathment. Similarly, we show that sheath formation requires Drpr. In principle, we could assay effects of simultaneously overexpressing ATP8a in neurons and inactivating Drpr (using the Drpr null mutation), but such an experiment will likely be difficult to interpret because the individual treatments cause an almost complete loss of sheaths. We did not investigate whether increasing PS exposure increases ensheathment because prior studies demonstrated that ectopic PS exposure induces membrane shedding in C4da dendrites.

Second, they inquire whether PS levels affect Drpr localization or levels. We demonstrate that inactivation of the PS bridging molecule Orion prevents Drpr localization at sheaths, hence we predict that neuronal overexpression of the ATP8a flippase should have a similar effect. In the revised manuscript, we will examine this possibility (monitoring Drpr distribution at epidermal contact sites with neurons overexpressing ATP8a).

Minor Points:

1. • Why there is no gene in bold category for hemocytes in Figure 1A*

The bold type was used to indicate the receptors that were selected for screening, using a relaxed criteria for identifying receptors that were “expressed”: any receptor detected at a level of 0.1 TPM. To this point, the figure legend states: “Epidermal candidate genes in bold exhibited a TPM value > 0.1 in at least one biological sample and were selected for inclusion in RNAi screen for epidermal phagocytic receptors required for ensheathment.”

We acknowledge that this is a relaxed criteria for “expression” and likely includes receptors that are not appreciably expressed in epidermal cells. Within the text we compare the repertoire of hemocyte and epidermal phagocytic receptors using a more standard (albeit still relatively relaxed) threshold of 0.5 TPM. We added shading to the histograms in Fig. 1A to facilitate comparison of phagocytic receptor gene expression in hemocytes and epidermal cells.

• Line 67: "neurons BEING the most extensively..."*

• Line 126: should read "epidermal engulfment receptors are INDIVIDUALLY dispensable"*

• Line 216: "THE DrprD 5 mutation had no significant..."*

• Line 230: "overexpression" instead of "overexpressed"*

• Line 385: similar "TO"*

These grammatical errors have been corrected. We thank the Reviewer for their careful reading of the manuscript.

Reviewer #1 (Significance (Required)):

This is an interesting study that adds to our understanding of the role of phagocytic receptors in shaping dendrites. Specifically, the role of Drpr (Draper) is studied, a gene previously known as an important for removal degenerating dendrites. The limitations of the manuscript as is is that it seems to be written primarily for a fly audience. Contextualizing the results and in the significance of this like conserved pathway could increase the significance.

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

Summary:

Innervation of the skin by somatosensory neurons is a conserved process that enables perception and discrimination of mechanical stimuli. How do molecules exposed by neurons and skin cells collaborate to promote neurite-induced epidermal sheath formation? Here, the authors combine fruit fly molecular and genetic tools with high resolution imaging to address this fundamental question. Based on morphological similarity between phagocytosis and SSN ensheathment, the authors hypothesized that one or more phagocyte receptors might promote ensheathment through ligand-driven interactions with neurites. To test this hypothesis, the authors systematically screened phagocytic receptors expressed in the epidermis for functional roles in ensheathment. Through this screening approach, the authors found that the Draper (Drpr) receptor functions in epidermal cells as a significant factor required to promote ensheathment. They support this conclusion using a suite of cell- and tissue-specific RNAi tools and mutant fly lines in conjunction with elegant mechanistic work that establishes a role for the conserved "eat-me" signal phosphatidylserine (PS) in driving ensheathment.

Major comments:

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

The seven key claims presented in the abstract are strongly supported by experimental data and analyses presented in the manuscript. At least one experimental result displayed in a main figure in support of the indicated key claim is summarized below. This summary does not present a comprehensive list of all data in support of a particular claim. Rather, it is an effort to confirm that each key result presented to the readership in the abstract is supported by at least one rigorously analyzed experimental result.

We concur with the Reviewer’s interpretations of our work and appreciate the clarity of their summaries below.

1. • Drpr functions in epidermal cells to promote ensheathment: Expressing a Draper RNAi under control of a larval epidermal driver (A58) led to significant reduction in total sheath length (Fig 1H), average sheath length (Fig 1I), and fraction ensheathed (Fig 1J). Similar results were obtained using two different Draper RNAi constructs.*

The argument presented through RNAi results in Fig 1 is bolstered by data using an existing validated Draper mutant line in Fig 2A-E. A question of interest to this reviewer upon receiving the paper was whether Draper functions at initial stages of sheath formation, maintenance of existing sheaths, or both. The timelapse data in Fig 2F suggests that Draper activity is dispensable for maintaining existing sheaths.

• ...that Draper accumulates at sites of epidermal ensheathment but not contact sites of unsheathed neurons:*

Immunostaining experiments demonstrate that Drpr immunoreactivity is enriched at PIP2-positive membrane domains in epidermal cells (Fig 3A-B). Is this accumulation selective for epidermal sheaths? Yes. In Fig. 3E-G, the authors show that Drpr enrichment overlaps with the sheath marker cora but not with dendrites of C1da neurons or from unsheathed portions of C4da dendrite arbors. The authors confirm specificity of Drpr immunoreactivity through control experiments using a Drpr mutant (Supplementary Fig 2).

• ...that Drpr overexpression increased ensheathment:*

Enforced overexpression of Draper in epidermal cells via Epidermal GAL4 driving UAS-Drpr (Fig 5A) shows significantly higher levels of ensheathment of C4da neurons as compared to controls. The authors demonstrate specificity by showing that epidermal Drpr overexpression did not induce ectopic sheath formation in C1da neurons (Fig 5E-G).

• ...that extracellular PS accumulates at sites of ensheathment:*

Using a previously developed secreted AnnV-mScarlet reporter (Ji et al. 2023 https://doi.org/10.1073/pnas.2303392120), the authors demonstrate that PLC-PH-GFP labeled stretches were also labeled by AnnV-mScarlet (Fig 6A-B), consistent with their model that ensheathment by Drpr is mediated by PS exposure on dendrites.

• ...that overexpression of the PS Flippase ATP8a blocks ensheathment:*

This claim is supported by demonstrating that overexpression of ATP8A, a protein that drives drives unidirectional PS translocation from the outer to the inner leaflet of the plasma membrane, impacts C4da neurite ensheathment. Selective overexpression of ATP8A in C4da neurons using a ppk-GAL4 induced a significant reduction in epidermal sheaths (Fig 6C).

• ...that Orion is required for sheath formation:*

Inactivation of the chemokine-like PS bridging molecule Orion significantly reduces fraction of ensheathment (Fig 6I-L).

• Overexpression of Draper enhanced nociceptor sensitivity to mechanical stimulus*

Consistent with a functional role for epidermal ensheathment in responses to mechanical stimuli, the authors report a significant reduction in nocifensive responses in a behavioral assay presented in Fig 6H.

In conclusion, the authors' claims are supported by the data as presented in this version of the manuscript.

• Please request additional experiments only if they are essential for the conclusions. Alternatively, ask the authors to qualify their claims as preliminary or speculative, or to remove them altogether.

n/a

• If you have constructive further reaching suggestions that could significantly improve the study but would open new lines of investigations, please label them as "OPTIONAL".

n/a

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated time investment for substantial experiments.

n/a

• Are the data and the methods presented in such a way that they can be reproduced?

Yes. The quality of the cell imaging data presented in the figures is high. The figure legends are sufficient to follow the investigators' conceptual approach and technical progress as they build their model. Transparent presentation of the screening data in Fig. 1 F-G was particularly appreciated by these reviewers.

Are the experiments adequately replicated and statistical analysis adequate?

Yes. We specifically commend the table outlining all statistical tests presented in the supplementary methods and linked to each figure.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Minor comments:

1. Could the authors further clarify Drpr's anticipated window of activity during sheath formation and/or speculate further on this point in the discussion? Live imaging in Fig. 2 suggest that Drpr is dispensable for maintenance of existing sheaths. Given that Drpr is proposed to be activated through transient phosphorylation that recruits the binding partner Shark (PMCID PMC2493287), it might be useful to clarify Drpr's window of activation (ie transient or constitutive) for an audience more familiar with Drpr's canonical functions in engulfment. The section prior to speculation about a possible role for negative regulators of phagocytosis (Line 360) might be a possible location for this addition.

We appreciate the insightful suggestion. As the Reviewer notes, our results are consistent with a model in which Drpr is required for formation but not maintenance of sheaths. Our original hypothesis was that Drpr would transiently localize to sheaths and be largely absent from mature sheaths. However, our antibody staining suggests that Drpr persists at mature sheaths (signal from endogenously labeled Drpr protein was too dim for live imaging in our hands). We therefore favor a model in which Drpr is transiently activated to promote sheath assembly.

In the context of engulfment, Src42A-dependent tyrosine phosphorylation of Draper promotes association of Shark and Draper pathway activation. Src42A activation is regulated by integrins and RTKs, providing a potential point of crosstalk with other pathway(s) likely involved in ensheathment. Intriguingly, membrane recruitment and activation of Talin depends in part on PIP2, and Talin promotes both Integrin activation and recruitment of PIP2-prodicing PIP5K Kinases, providing a potential feed-forward mechanism for increasing PIP2 accumulation, Talin recruitment, and Integrin activation, which can promote Src42A activation. In our revised discussion we will provide a more thorough treatment of mechanism(s) of Drpr activation.

• The authors might consider developing their conclusion a bit further for a broad audience. For example, the gesture to Piezo dependence in the current final sentence might provide an opening to discuss an exciting future avenue focused on integrating molecular mechansensors into a comprehensive model of selective SSN ensheathment important for the perception and discrimination of touch and pain.*

We appreciate the suggestion and agree that it is worthwhile to expand on the potential links between ensheathment and sensory neuron function in our revised discussion. Our studies thus far have largely explored mechanosensation, but it’s worth noting that the nociceptive neurons under study here are polymodal, and other functional classes of somatosensory neurons are ensheathed to differing degrees, so an intriguing open question is whether ensheathment selectively potentiates the function of mechanosensors or more generally enhances functional coupling of somatosensory neurons to the epidermis. Our finding that ensheathment levels can be bidirectionally regulated by drpr levels provides an entry point to more broadly characterizing functions for ensheathment.

• Word missing or extra "in" in Line 69 after ECM?*

Corrected.

• In Fig 1 and Fig 3, the PLC(delta)-PH-GFP reporter contains the delta symbol, in other throughout the paper it does not. In addition, Fig 5 is denoted "PIP2 (PLC-PH-GFP)". For consistency the authors might consider using PLC(delta)-PH-GFP across all figures.*

As suggested, we updated the figures and text to include the delta symbol in the reporter PLC(delta)-PH-GFP.

• Fig 6P - do the authors suggest Orion is distributed at high concentration throughout the entire upper portion of the figure? Perhaps the coloration could be changed if Orion binding is suggested to occur between Drpr and PS.*

We have not examined Orion distribution in the periphery, though prior studies demonstrate that it is secreted into the hemolymph from multiple sources. Our schematic focuses on sites of contact between epidermal cells and dendrites but omits the hemolymph, muscle, and other cell types in the periphery. In our initial schematic epidermal cells and Orion were shaded similarly; in our revision we chose a different color for epidermal cells to prevent confusion.

Optional suggestions for consideration to provide further context for a broad audience:

Optional 6. The authors might consider placing their work in the context of an emerging literature focused developmental roles for immune cell signaling molecules/other phagocyte receptors at steady state. While the present study focused on epidermal ensheathment of SSNs stands on its own as a notable contribution and does not require these citations to support its conclusions, context from an emerging literature bridging immunity and development might be of interest to a broad readership. Should the authors wish to strengthen the link between their work and findings from other systems indicating a shared role in immunity and development for key immunoreceptors and their binding partners, they might consider adding citations/phrasing indicating that Draper's molecular collaborator Shark kinase (PMCID PMC2493287) was initially discovered as a developmental gene required for dorsal closure (PMCID PMC316420). They might also consider highlighting the role of Draper's mammalian orthologs Megf10/Megf11 in regulating mosaic spacing of retinal neurons (PMCID PMC3310952).

We appreciate the Reviewer’s suggestions, in particular the value of further highlighting relevant links between immunity and development. Not including Megf10/Megf11 (Drpr vertebrate orthologue) in our discussion was an oversight as we predict that Megf10/Megf11 serves a similar role in ensheathment of vertebrate somatosensory neurons. In our revised manuscript we will incorporate a more thorough discussion of the emerging literature bridging immunity and development.

Optional 7. The authors might consider tying their extended discussion of integrins (~Line 320-Line 335) into their overall argument in a more cohesive manner. For example, how (if at all) do the authors see Drpr collaborating with other receptors to regulate initiation versus maintenance of sheaths? Is a model in which Drpr initiates ensheathment maintained by other molecules possible? Speculation on this point in the discussion might integrate other molecules into the authors' model in a cohesive manner and/or bolster the authors' discussion of Drpr's window of activation/deactivation during ensheathment.

Indeed, we envision a model in which Drpr cooperates with other receptors; we discussed one possible connection to integrins above and will incorporate a fuller treatment of the possible crosstalk between these pathways in our discussion. Regarding a model in which Drpr initiates ensheathment maintained by other molecules: yes, we agree that this is possible, but our results suggest that additional receptors likely participate in sheath initiation as well. Drpr inactivation substantially reduces but does not totally eliminate ensheathment, however the sheaths that form in drpr mutants are structurally distinct from mature sheaths (shorter, narrower, appear to recruit less Cora). Hence, we favor a model in which drpr signaling cooperates with a parallel, partially redundant pathway for initiating sheath formation in response to sheath-promoting signals. Integrin signaling is a plausible candidate for this parallel pathway for reasons we discuss in our original submission (and above); in our revised discussion we will more extensively discuss the potential cross-talk between Drpr signaling and Integrin signaling in initiation and maintenance of epidermal sheaths.

Reviewer #2 (Significance (Required)):

This study provides a new link between a conserved phagocyte receptor (Drpr) and epidermal ensheathment of somatosensory neurons, an important process at the heart of the regulated development and function of the nervous system. As such, the Yin et al. submission is a significant contribution to a rapidly moving research area of broad interest to an intellectually diverse readership interested in the molecular and cellular basis of neurodevelopment and interactions between the nervous system and the immune system.* *

An important strength of this study is the striking degree of the epidermal ensheathment phenotypes observed when normal Drpr expression is disrupted either through depletion, mutation, or targeted overexpression. For example, depletion of Drpr via RNAi induces a ~three fold reduction in total sheath length (Fig 1F - ~1.45 mm in controls as compared to ~0.5 mm with Drpr RNAi). Notably, epidermal enforced overexpression of Drpr induces a notable increase in the fraction of ensheathed neurons (Fig 5A-D). This strength of phenotype enables the investigators to deploy an elegant sequence of molecular and genetic tools to further probe mechanism and implicate extracellular PS in this process.* *

Reviewer area keywords as requested: phagocytes, immune cell signaling, signal transduction

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

The study by Yin and colleagues investigates how epidermal cells recognize and ensheath somatosensory neuron (SSN) dendrites in Drosophila larvae. The authors identify the phagocytic receptor Draper (Drpr) as a key mediator of selective epidermal ensheathment and demonstrate that this process relies on phosphatidylserine (PS) exposure on dendrites and the bridging molecule Orion. The work significantly advances our understanding of neuron/epidermis interactions and reveals a novel role for phagocytic recognition pathways in non-glial ensheathment.

The manuscript is clearly written, methodologically solid and supported by compelling data. The authors combine genetic, imaging and functional approaches to uncover a mechanism of structural and functional modulation of nociceptive neurons. The results will interest researchers studying neuronal morphogenesis, epithelial biology and non-glial phagocytic pathways.

Specific Critiques:

While the study is strong and timely, several issues should be addressed prior to acceptance:

Figure 1: The authors refer to the receptors as "engulfment receptors." I recommend calling them "phagocytic receptors" since not all are required for the engulfment step (e.g., Crq).

The Reviewer makes an important distinction. We have updated our manuscript to reflect this point, replacing “engulfment receptor” with “phagocytic receptor” in the text and in our title.

Figure 2: The title states "Drpr is required in epidermal cells..." yet the authors analyze a drpr null mutant, which lacks Drpr in all expressing cells (glia, macrophages and epidermal cells). The rationale for using the null mutant instead of epidermal-specific RNAi should be explained.

The increased dendrite number in drpr RNAi larvae should also be noted here.

We agree – the title is not appropriate for this version of the figure; we changed the title to better reflect the experiments being portrayed.

Our RNAi experiments in Figure 1 and 2 demonstrate that drpr is cell autonomously required in epidermal cells for dendrite ensheathment. Here, we include analysis of an amorphic drpr allele to (1) provide further genetic support underscoring the requirement for drpr in dendrite ensheathment and (2) to underscore the observation that a small number of immature sheaths form in the complete absence of drpr, arguing for the presence of an additional pathway that contributes to sheath formation.

Effects of epidermal drpr RNAi on dendrite number is not something we evaluated with our time-lapse studies in Figure 2. Instead, we monitored the effects of drpr knockdown on growth behavior of epidermal sheaths and found that epidermal drpr RNAi triggered an increase in the frequence of sheath retraction events and a decrease in sheath growth events.

Figure 3: Explain the numbers on the X-axis in panels B and D. Add a panel without blue dashed outlines to better visualize Drpr expression. Adjust the red boxes to precisely match the enlarged regions.

Each bar represents a single neuron; the numbers denote the number of sheaths sampled from each neuron. We added this to the figure and figure legend in our manuscript. We thank the Reviewer for identifying this oversight.

We appreciate the Reviewer’s perspective on the blue hatched lines; we removed the hatched lines from the ROI and adjusted the position of the red hatched box.

Figure 4: Why is the drpr mutant used here rather than RNAi? Please clarify the reasoning for choosing mutants in some experiments and knockdown in others.

In Figure 2, we show analysis of the amorphic allele to further corroborate our RNAi studies, as described above. We chose to use the drpr amorphic mutant for these studies because we have no GAL4-independent reporter to label C1da neurons for analysis of dendrite arborization patterns. Although we could use HRP staining in combination with epidermal drpr RNAi, live imaging of dendrite arbors labeled by a C1da neuron GAL4 driver provides a more sensitive and reliable readout for morphogenesis studies.

In our revised manuscript we will add analysis of C4da dendrite patterns in larvae expressing drpr RNAi in epidermal cells to evaluate whether the dendrite defects reflect epidermal requirements for drpr function.

Figure 5: Correct the placement of white boxes in panels E-F′.

We thank the Reviewer for identifying the mismatch. We corrected the placement to match the size of the ROIs.

*Figure 6: AnnV staining in B is difficult to detect. Please add a version of the panel showing AnnV alone. *

In our initial submission we include the overlay of PLC-PH-GFP and AnnV-mScarlet (B), an image showing the PLC-PH-GFP alone (B’) and an image showing the AnnV-mScarlet alone (B”).

AnnV labeling appears weak on sheaths. Since epidermal membranes are strongly labeled, confirm PS exposure on dendrites with a commercial fluorescent Annexin V reagent.

We appreciate the suggestion to use a commercial fluorescent Annexin V reagent and agree that it would strengthen our findings if such a reagent labeled sheaths. However, we intentionally prioritized analysis using the in vivo reporter because numerous studies indicate that epidermal sheaths are inaccessible to large molecules in solution (in the absence of detergent). One of the first assays used to monitor the in vivo distribution of sheaths was based on the inaccessibility of antibodies to ensheathed neurites (Kim et al, Neuron, 2012; also Tenenbaum et al, Current Biology, 2017; Jiang et al, eLife, 2019). More recently, we demonstrated that 10kDa dextran dyes are excluded from epidermal sheaths (Luedke et al, PLoS Genetics, 2024). Nevertheless, as part of our revision we will examine whether commercially available Annexin V reagents label sheaths.

In F and F" sheaths are labeled in areas without visible dendrites. Please clarify.

We note that although C4da dendrites are the most extensively ensheathed among da neurons, other neurons (most prominently C3da neurons) also exhibit significant ensheathment (Jiang et al, eLife, 2019). We use established markers of epidermal sheaths (Cora immunoreactivity in this panel; PIP2 reporters and/or Cora-GFP localization in other panels), hence Drpr accumulates at Cora+ sheaths on C4da neurons and Cora+ sheaths that form on other da neurons. We will clarify this point in the text of our revised manuscript.

In O and P, show Drpr staining without blue dashed sheath outlines.

We have removed the blue dashed outlines from the figure panels.

The legend contains numerous labeling errors: there is no B′ or B"; C-G should be E-G; G-I should be H-J; I-L should be K-N; M-O should be O-R. Please revise carefully.

The labeling errors have been corrected.

Sup Fig 1: Add a panel with only c4da labeling to visualize dendrites.

We have added a panel displaying only C4da dendrites to this figure.

Sup Fig 2: The anti-Drpr signal is unexpected in the null mutant. Validate with an additional antibody (e.g., mouse monoclonal anti-Drpr from the DSHB).

We appreciate the suggestion and have already tested the mouse monoclonal anti-Drpr antibody from DSHB and found that it is unsuitable for use in our preparations (ie, no Drpr-dependent immunoreactivity, even in specimens overexpressing Drpr).

With respect to the comment about the unexpected signal in the null mutant, we note that the antibody is a rabbit polyclonal and is not purified. In our experience it is not uncommon for rabbit serum (even pre-immune serum) to recognize multiple antigens in the larval skin. Nevertheless, our control studies demonstrate that Drpr immunoreactivity is eliminated at epidermal sheaths in Drpr null mutants.

Sup Fig 3: No panels A or B are shown; no PIP2 marker is present despite the legend. Please revise. Drpr overexpression appears to increase Cora levels in some cell. Could Drpr affect Cora expression or distribution? This should be addressed. Also dendrite number appears higher in Drpr-overexpressing larvae. Please state whether this is significant.

The labeling errors in the legend have been corrected; the corresponding studies with the PIP2 marker are presented in Figure 5.

All epidermal drivers we have characterized exhibit a low level of variegation in expression within a hemisegment that we have previously documented (Jiang et al 2014 Development; Jiang et al 2019 eLife), and we suspect that it may be related to epidermal endoreplication (epidermal cells do not synchronously endoreplicate). However, we have not observed any systematic difference in epidermal GAL4 driver or Cora-GFP expression in larvae overexpressing Drpr. We note that a single cell in the field of view in Supplemental Figure 3 exhibits a higher level of GFP fluorescence. We occasionally observe this, independent of background genotype.

All gene names must be italicized and lowercase (e.g., drpr), including in figure labels and legends.

All protein names must be capitalized and non-italic (e.g., Drpr, Cora).

We appreciate the Reviewer’s feedback. We used Drpr in keeping with many recent reports, but the Reviewer is correct in outlining the standard naming conventions. We have changed the gene names to reflect convention (lowercase, italics for genes that were initially identified according to phenotypic characterization; uppercase, italics for genes named according to homology to orthologues in other species such as NimB4 and ATP8A)

Define ROI on first use.

Done. We defined ROI in the methods section.

Ensure consistent phrasing: use "anti-Cora or anti-Drpr immunoreactivity" uniformly.

We have done so.

There a few typos which must be corrected:

• • Line 196: "containing" → "contain"*

• • Line 205: "antibodies Drpr" → "antibodies to Drpr" or "anti-Drpr antibodies"*

• • Line 331: "predominan" → "predominant"*

• • Line 353: "phagocyting" → "phagocytic"*

• • Line 385: "similar the effect" → "similar to the effect"*

• • Line 432: Title should be underlined*

• • Line 544: "drpr∆5" is missing the 5*

• • Line 569: "immunoreactivity a" → "immunoreactivity of"*

The typographical errors have been corrected. We thank the Reviewer for the close reading of the manuscript.

Reviewer #3 (Significance (Required)):

The manuscript makes a meaningful contribution to the field of neuron/epidermal cells interactions by demonstrating that recognized phagocytic machinery components can be co-opted for ensheathment of sensory neurites. This not only expands our understanding of skin innervation and mechanosensation but also raises intriguing implications for how similar mechanisms might operate in vertebrates (e.g., epidermal/nerve interactions, peripheral neuropathy). Given the functional link to nociceptive sensitivity, the work may have broader relevance for pain biology and sensory disorders.

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Referee #3

Evidence, reproducibility and clarity

The study by Yin and colleagues investigates how epidermal cells recognize and ensheath somatosensory neuron (SSN) dendrites in Drosophila larvae. The authors identify the phagocytic receptor Draper (Drpr) as a key mediator of selective epidermal ensheathment and demonstrate that this process relies on phosphatidylserine (PS) exposure on dendrites and the bridging molecule Orion. The work significantly advances our understanding of neuron/epidermis interactions and reveals a novel role for phagocytic recognition pathways in non-glial ensheathment. The manuscript is clearly written, methodologically solid and supported by compelling data. The authors combine genetic, imaging and functional approaches to uncover a mechanism of structural and functional modulation of nociceptive neurons. The results will interest researchers studying neuronal morphogenesis, epithelial biology and non-glial phagocytic pathways.

While the study is strong and timely, several issues should be addressed prior to acceptance: Figure 1: The authors refer to the receptors as "engulfment receptors." I recommend calling them "phagocytic receptors" since not all are required for the engulfment step (e.g., Crq).

Figure 2: The title states "Drpr is required in epidermal cells..." yet the authors analyze a drpr null mutant, which lacks Drpr in all expressing cells (glia, macrophages and epidermal cells). The rationale for using the null mutant instead of epidermal-specific RNAi should be explained. The increased dendrite number in drpr RNAi larvae should also be noted here.

Figure 3: Explain the numbers on the X-axis in panels B and D. Add a panel without blue dashed outlines to better visualize Drpr expression. Adjust the red boxes to precisely match the enlarged regions.

Figure 4: Why is the drpr mutant used here rather than RNAi? Please clarify the reasoning for choosing mutants in some experiments and knockdown in others.

Figure 5: Correct the placement of white boxes in panels E-F′.

Figure 6: AnnV staining in B is difficult to detect. Please add a version of the panel showing AnnV alone. AnnV labeling appears weak on sheaths. Since epidermal membranes are strongly labeled, confirm PS exposure on dendrites with a commercial fluorescent Annexin V reagent. In F and F" sheaths are labeled in areas without visible dendrites. Please clarify. In O and P, show Drpr staining without blue dashed sheath outlines. The legend contains numerous labeling errors: there is no B′ or B"; C-G should be E-G; G-I should be H-J; I-L should be K-N; M-O should be O-R. Please revise carefully.

Sup Fig 1: Add a panel with only c4da labeling to visualize dendrites. Sup Fig 2: The anti-Drpr signal is unexpected in the null mutant. Validate with an additional antibody (e.g., mouse monoclonal anti-Drpr from the DSHB). Sup Fig 3: No panels A or B are shown; no PIP2 marker is present despite the legend. Please revise. Drpr overexpression appears to increase Cora levels in some cell. Could Drpr affect Cora expression or distribution? This should be addressed. Also dendrite number appears higher in Drpr-overexpressing larvae. Please state whether this is significant.

All gene names must be italicized and lowercase (e.g., drpr), including in figure labels and legends. All protein names must be capitalized and non-italic (e.g., Drpr, Cora). Define ROI on first use. Ensure consistent phrasing: use "anti-Cora or anti-Drpr immunoreactivity" uniformly. There a few typos which must be corrected:

• Line 196: "containing" → "contain"
• Line 205: "antibodies Drpr" → "antibodies to Drpr" or "anti-Drpr antibodies"
• Line 331: "predominan" → "predominant"
• Line 353: "phagocyting" → "phagocytic"
• Line 385: "similar the effect" → "similar to the effect"
• Line 432: Title should be underlined
• Line 544: "drpr∆5" is missing the 5
• Line 569: "immunoreactivity a" → "immunoreactivity of"

Significance

The manuscript makes a meaningful contribution to the field of neuron/epidermal cells interactions by demonstrating that recognized phagocytic machinery components can be co-opted for ensheathment of sensory neurites. This not only expands our understanding of skin innervation and mechanosensation but also raises intriguing implications for how similar mechanisms might operate in vertebrates (e.g., epidermal/nerve interactions, peripheral neuropathy). Given the functional link to nociceptive sensitivity, the work may have broader relevance for pain biology and sensory disorders.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Innervation of the skin by somatosensory neurons is a conserved process that enables perception and discrimination of mechanical stimuli. How do molecules exposed by neurons and skin cells collaborate to promote neurite-induced epidermal sheath formation? Here, the authors combine fruit fly molecular and genetic tools with high resolution imaging to address this fundamental question. Based on morphological similarity between phagocytosis and SSN ensheathment, the authors hypothesized that one or more phagocyte receptors might promote ensheathment through ligand-driven interactions with neurites. To test this hypothesis, the authors systematically screened phagocytic receptors expressed in the epidermis for functional roles in ensheathment. Through this screening approach, the authors found that the Draper (Drpr) receptor functions in epidermal cells as a significant factor required to promote ensheathment. They support this conclusion using a suite of cell- and tissue-specific RNAi tools and mutant fly lines in conjunction with elegant mechanistic work that establishes a role for the conserved "eat-me" signal phosphatidylserine (PS) in driving ensheathment.

Major comments:

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

The seven key claims presented in the abstract are strongly supported by experimental data and analyses presented in the manuscript. At least one experimental result displayed in a main figure in support of the indicated key claim is summarized below. This summary does not present a comprehensive list of all data in support of a particular claim. Rather, it is an effort to confirm that each key result presented to the readership in the abstract is supported by at least one rigorously analyzed experimental result.

1. Drpr functions in epidermal cells to promote ensheathment: Expressing a Draper RNAi under control of a larval epidermal driver (A58) led to significant reduction in total sheath length (Fig 1H), average sheath length (Fig 1I), and fraction ensheathed (Fig 1J). Similar results were obtained using two different Draper RNAi constructs. The argument presented through RNAi results in Fig 1 is bolstered by data using an existing validated Draper mutant line in Fig 2A-E. A question of interest to this reviewer upon receiving the paper was whether Draper functions at initial stages of sheath formation, maintenance of existing sheaths, or both. The timelapse data in Fig 2F suggests that Draper activity is dispensable for maintaining existing sheaths.
2. ...that Draper accumulates at sites of epidermal ensheathment but not contact sites of unsheathed neurons: Immunostaining experiments demonstrate that Drpr immunoreactivity is enriched at PIP2-positive membrane domains in epidermal cells (Fig 3A-B). Is this accumulation selective for epidermal sheaths? Yes. In Fig. 3E-G, the authors show that Drpr enrichment overlaps with the sheath marker cora but not with dendrites of C1da neurons or from unsheathed portions of C4da dendrite arbors. The authors confirm specificity of Drpr immunoreactivity through control experiments using a Drpr mutant (Supplementary Fig 2).
3. ...that Drpr overexpression increased ensheathment: Enforced overexpression of Draper in epidermal cells via Epidermal GAL4 driving UAS-Drpr (Fig 5A) shows significantly higher levels of ensheathment of C4da neurons as compared to controls. The authors demonstrate specificity by showing that epidermal Drpr overexpression did not induce ectopic sheath formation in C1da neurons (Fig 5E-G).
4. ...that extracellular PS accumulates at sites of ensheathment: Using a previously developed secreted AnnV-mScarlet reporter (Ji et al. 2023 https://doi.org/10.1073/pnas.2303392120), the authors demonstrate that PLC-PH-GFP labeled stretches were also labeled by AnnV-mScarlet (Fig 6A-B), consistent with their model that ensheathment by Drpr is mediated by PS exposure on dendrites.
5. ...that overexpression of the PS Flippase ATP8a blocks ensheathment: This claim is supported by demonstrating that overexpression of ATP8A, a protein that drives drives unidirectional PS translocation from the outer to the inner leaflet of the plasma membrane, impacts C4da neurite ensheathment. Selective overexpression of ATP8A in C4da neurons using a ppk-GAL4 induced a significant reduction in epidermal sheaths (Fig 6C).
6. ...that Orion is required for sheath formation: Inactivation of the chemokine-like PS bridging molecule Orion significantly reduces fraction of ensheathment (Fig 6I-L).
7. Overexpression of Draper enhanced nociceptor sensitivity to mechanical stimulus Consistent with a functional role for epidermal ensheathment in responses to mechanical stimuli, the authors report a significant reduction in nocifensive responses in a behavioral assay presented in Fig 6H.

In conclusion, the authors' claims are supported by the data as presented in this version of the manuscript.

• Please request additional experiments only if they are essential for the conclusions. Alternatively, ask the authors to qualify their claims as preliminary or speculative, or to remove them altogether.

n/a - If you have constructive further reaching suggestions that could significantly improve the study but would open new lines of investigations, please label them as "OPTIONAL".

n/a - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated time investment for substantial experiments. n/a - Are the data and the methods presented in such a way that they can be reproduced?

Yes. The quality of the cell imaging data presented in the figures is high. The figure legends are sufficient to follow the investigators' conceptual approach and technical progress as they build their model. Transparent presentation of the screening data in Fig. 1 F-G was particularly appreciated by these reviewers.

Are the experiments adequately replicated and statistical analysis adequate?

Yes. We specifically commend the table outlining all statistical tests presented in the supplementary methods and linked to each figure.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Minor comments:

1. Could the authors further clarify Drpr's anticipated window of activity during sheath formation and/or speculate further on this point in the discussion? Live imaging in Fig. 2 suggest that Drpr is dispensable for maintenance of existing sheaths. Given that Drpr is proposed to be activated through transient phosphorylation that recruits the binding partner Shark (PMCID PMC2493287), it might be useful to clarify Drpr's window of activation (ie transient or constitutive) for an audience more familiar with Drpr's canonical functions in engulfment. The section prior to speculation about a possible role for negative regulators of phagocytosis (Line 360) might be a possible location for this addition.
2. The authors might consider developing their conclusion a bit further for a broad audience. For example, the gesture to Piezo dependence in the current final sentence might provide an opening to discuss an exciting future avenue focused on integrating molecular mechansensors into a comprehensive model of selective SSN ensheathment important for the perception and discrimination of touch and pain.
3. Word missing or extra "in" in Line 69 after ECM?
4. In Fig 1 and Fig 3, the PLC(delta)-PH-GFP reporter contains the delta symbol, in other throughout the paper it does not. In addition, Fig 5 is denoted "PIP2 (PLC-PH-GFP)". For consistency the authors might consider using PLC(delta)-PH-GFP across all figures.
5. Fig 6P - do the authors suggest Orion is distributed at high concentration throughout the entire upper portion of the figure? Perhaps the coloration could be changed if Orion binding is suggested to occur between Drpr and PS.

Optional suggestions for consideration to provide further context for a broad audience: Optional 6. The authors might consider placing their work in the context of an emerging literature focused developmental roles for immune cell signaling molecules/other phagocyte receptors at steady state. While the present study focused on epidermal ensheathment of SSNs stands on its own as a notable contribution and does not require these citations to support its conclusions, context from an emerging literature bridging immunity and development might be of interest to a broad readership. Should the authors wish to strengthen the link between their work and findings from other systems indicating a shared role in immunity and development for key immunoreceptors and their binding partners, they might consider adding citations/phrasing indicating that Draper's molecular collaborator Shark kinase (PMCID PMC2493287) was initially discovered as a developmental gene required for dorsal closure (PMCID PMC316420). They might also consider highlighting the role of Draper's mammalian orthologs Megf10/Megf11 in regulating mosaic spacing of retinal neurons (PMCID PMC3310952).

Optional 7. The authors might consider tying their extended discussion of integrins (~Line 320-Line 335) into their overall argument in a more cohesive manner. For example, how (if at all) do the authors see Drpr collaborating with other receptors to regulate initiation versus maintenance of sheaths? Is a model in which Drpr initiates ensheathment maintained by other molecules possible? Speculation on this point in the discussion might integrate other molecules into the authors' model in a cohesive manner and/or bolster the authors' discussion of Drpr's window of activation/deactivation during ensheathment.

Significance

This study provides a new link between a conserved phagocyte receptor (Drpr) and epidermal ensheathment of somatosensory neurons, an important process at the heart of the regulated development and function of the nervous system. As such, the Yin et al. submission is a significant contribution to a rapidly moving research area of broad interest to an intellectually diverse readership interested in the molecular and cellular basis of neurodevelopment and interactions between the nervous system and the immune system.

An important strength of this study is the striking degree of the epidermal ensheathment phenotypes observed when normal Drpr expression is disrupted either through depletion, mutation, or targeted overexpression. For example, depletion of Drpr via RNAi induces a ~three fold reduction in total sheath length (Fig 1F - ~1.45 mm in controls as compared to ~0.5 mm with Drpr RNAi). Notably, epidermal enforced overexpression of Drpr induces a notable increase in the fraction of ensheathed neurons (Fig 5A-D). This strength of phenotype enables the investigators to deploy an elegant sequence of molecular and genetic tools to further probe mechanism and implicate extracellular PS in this process.

Reviewer area keywords as requested: phagocytes, immune cell signaling, signal transduction

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Yin et al investigates how epidermal cells shape somatosensory neuron (SSN) morphology and function through selective ensheathment in Drosophila. This study builds on earlier work by another group showing that the phagocytic receptor Draper (Drpr) as a crucial epidermal factor that is important for dendrite pruning and clearance. In the present study, the authors how that Drpr also functions in the epidermis to establish the characteristic stretches of epidermal ensheathment of dendrite arborization neurons in the fruit fly Drosophila melanogaster. This is particularly true for highly branched types of dendrites but ont dendrites that show simpler branching patterns. Overexpression of Drpr increases ensheathment and nociceptor sensitivity, linking molecular recognition to sensory modulation. Further, Drpr is known to recognize phosphatidylserine (PS) on neurites to promote ensheathment and the authors show localization of a reporter for PS with epidermal membranes. Genetic manipulations that reduce PS results in a reduction in epidermal sheaths and the chemokine-like protein Orion promoting Drpr/PS interactions is required for these processes. Overall, the manuscript is well written, although at times maybe primarily for a fly audience. Reach could be improved by making it more accessible to a non-fly audience. The observation that Drpr is not only required for removing damaged or degenerating dendrites but also for their correct ensheathment of highly branched dendrites presents an important finding that could be of interest for a wider audience provided the following points are adequately addressed:

1. The Introduction could be further elaborated to help readers understand the significance of epidermal dendrite ensheathment. Addressing the following points may achieve this:

(i) The Introduction would benefit from including details on developmental disorders and neurological diseases associated with defects or abnormalities in dendrite ensheathment.

(ii) In lines 74-79, it is unclear whether the described findings are conserved across evolution or were demonstrated in a specific model organism.

(iii) Including a description of the known literature on phagocytosis in this process would help readers better understand the novelty and significance of this study.

(iv) Details of published Draper function in Han et al 2014 should be elaborated along with unanswered question that is addressed in this study. 2. It is unclear why the authors focus exclusively on Drpr and Crq, without addressing emp and CG4006, both of which show higher expression levels than the former. Moreover, the conclusion that 14 out of 16 engulfment receptor genes have no role based solely on RNAi knockdown experiments is a very strong statement that may requires additional validation. The authors should provide evidence that the RNAi knockdowns achieved complete loss of gene function to support their claim about 16 engulfment receptors. In addition, at most the authors can conclude that the tested genes are individually not required. 3. What kind of genes are crq and ea? 4. Comparing Figures 1C and 1E, it appears that drpr knockdown has a differential effect on epidermal dendrite ensheathment between main and secondary branches. If this observation is correct, separate quantification for each branch type would be more appropriate, along with an explanation for the observed differences. 5. For Figure 1K, it would be informative to examine how drpr knockdown affects dendrite length in these neurons. 6. For Drpr expression (Figure 3), it would be valuable to highlight any differences in expression between primary and secondary dendritic branches. 7. Removing drpr leads to excessive branching of SSN dendrites. Does overexpression of drpr affect dendrite morphology in the opposite manner? 8. Although drpr role in dendrite ensheathment is well explored, the interactions between drpr and PS seem underexplored. For example, do the changes in ensheathment as a result of manipulating PS levels require drpr? Does changing PS levels affect Drpr localization or levels?

Minor Points:

1. Why there is no gene in bold category for hemocytes in Figure 1A
2. Line 67: "neurons BEING the most extensively..."
3. Line 126: should read "epidermal engulfment receptors are INDIVIDUALLY dispensable"
4. Line 216: "THE DrprD 5 mutation had no significant..."
5. Line 230: "overexpression" instead of "overexpressed"
6. Line 385: similar "TO"

Significance

This is an interesting study that adds to our understanding of the role of phagocytic receptors in shaping dendrites. Specifically, the role of Drpr (Draper) is studied, a gene previously known as an important for removal degenerating dendrites. The limitations of the manuscript as is is that it seems to be written primarily for a fly audience. Contextualizing the results and in the significance of this like conserved pathway could increase the significance.

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I thank the Referees for their...

Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

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Referee #2

Evidence, reproducibility and clarity

In this study, Wang et al. use Difteria Toxin (DT) to cause hair cell (HC) death in transgenic mice expressing the DT receptor in the HC of the inner ear. This model is assumed to cause HC loss in a selective way. The lesioned mice are assessed for translational vestibulo-ocular reflex (tVOR), vestibular sensory evoked potential (VsEP), rotational vestibulo-ocular reflex (rVOR), and single-unit recordings of vestibular afferents from cristae and maculae. Numbers of surviving HC, including total HC, type I HC (HCI) and type II HC (HCII) were also obtained at short and long times after DT exposure. By comparing the functional and histological results, the authors conclude that DT cause dose-dependent HC loss and vestibular function loss, that limited but significant HC regeneration occurs and that vestibular organs display variable but ample redundancy because robust physiological responses were obtained despite loss of high percentages of HCs.

However, there are several limitations in the experimental design, methodological choices and analysis of the results that weaken the conclusions stated by the authors. Also, some important aspects of the work are not clear enough for an in deep scrutiny.

The following list of weaknesses is not arranged in order of importance.

1. Choice and use of the Pou4f3DTR/+ transgenic on FVB and C57/Bl6 backgrounds.

1.a. Literature descriptions of the Pou4f3-DTR model used C57/Bl6 and CBA/J backgrounds and low mortality rates were found after DT administration. The present study generated Pou4f3-DTR mice on a FVB background and found that DT cause high mortality rates in this background. Comparison of the C57/Bl6 and FVB backgrounds are included in Figures 1 and 2 and the conclusion was that the C57/Bl6 background is more suitable for studying vestibular HC degeneration/regeneration. However, data are presented in Figures 3 to 7 without informing the reader whether these are from C57/Bl6 or FVB animals. Because of the information given in table 1, at least part of the data in these Figures is from the less suitable FVB mice. It is also possible that some data sets contain unbalanced numbers of animals from each strain in the different experimental conditions, with a potential impact on the robustness of the results. The strain identity of animals should be clarified across all data sets.

1.b. Why the Pou4f3-DTR transgene was introduced in the FVB strain? The FVB strain is frequently used in transgenesis because the prominent pronuclei in their fertilized eggs and large litter size. While generation of transgenic lines in FVB mice is common, why would you want to bring an already established transgenic modification to a FVB background? It is known that FVB mice become blind by wean age due to a mutation in the Pde6b gene. Were the authors trying to have the Pou4f3-DTR model in a strain of blind animals? It is anomalous that the rationale for the FVB derivation is not provided and that the blindness of this strain is not even mentioned in an article containing VOR data. 2. Toxicity of the DT.

2.1. The non-HC toxicity of DT is not evaluated. One of the stated reasons of the choice of the Pou4f3-DTR model to ablate HC is that other alternative models (aminoglycosides, cisplatin, IDPN) cause other toxic effects besides HC toxicity. However, the lack of evidence of other toxicities in Pou4f3-DTR mice after DT administration may simply be due to lack of assessment. Besides the inner ear, Pou4f3 is expressed in several structures including the genitourinary system, the retina, Merkel cells and subsets of somatosensory and brain neurons (https://www.ncbi.nlm.nih.gov/datasets/gene/18998/; PMID: 20826176; PMID: 22262898; PMID: 34266958; PMID: 33135183), so one would expect DT toxicity in these Pou4f3 expressing cells. Also, DT may cause other toxicities not explored in the model. The fact that the DT treatment is toxic beyond the intended HC toxicity is proven by the high (strain-dependent) mortality rate recorded in this study. A more detailed analysis of the effects of DT in the Pou4f3-DTR mice is needed before stating that the treatment is selective for the inner ear HCs. By the way, hyperactivity is not an additional toxic effect of ototoxic chemicals, it is a consequence of the vestibular function loss.

2.2. The dose-response relationship of the DT treatment is unclear. The authors state that DT caused a dose-dependent loss of HC. However, the effects across different DT doses were not compared directly. Instead, each DT dose was compared with a different set of controls, and then the percentage of HC loss was qualitatively compared without statistical comparison. Looking at the numbers, the percent loss after the 35x2 dose is greater than that recorded after the 50x2 dose, contradicting the conclusion of a dose-dependent effect. One possible explanation is that the DT treatment has an inverted-U dose-response relationship, and the 25x2, 35x2 and 50x2 doses draw the bottom of the U. Alternatively, you have a dose-dependent effect with a dose causing a moderate effect (15) and 3 doses (25x2, 35x2, 50x2) causing near-maximal effects with differences among these groups more related to experimental variability than to dose-dependency. <br /> 3. Experimental design, use of animals, role of batch-to-batch variability in apparent results.

3.a. The number of animals used in each experimental condition, their assignment to each assessment and participation in each dataset must be clarified. The reader is not informed on whether the animals used for physiological and histological analyses were the same or separate sets of animals were used. Also, the distribution of animals in different batches is not clarified and this may have originated apparent results through experimenter-generated bias. For instance, the HC count data are presented as two different, independent experiments, one evaluating different doses in the two strains at 14 days after exposure (Figures 1 and 2) and a second one comparing the HC counts at 2 weeks and 6 months after exposure (Figures 3 and 4). However, these were not separate experiments because at least some animals were shared in the two "experiments". This is demonstrated by the duplicate images between figures 1 and 2 and figures 3 and 4 (for instance, images D to D' in Figure 1 are the same than images C to C' in Figure 3). Therefore, at least part of the data for 2-week animals in Figure 3 have already been used as data of day-14 animals in Figure 1. This makes this reviewer suspect that 6-month animals in Figure 3 were treated with DT at different dates than 2-month animals in the same figure. Therefore, the small but significant "regeneration" could be simply due to differences in experimental outcome due to batch-to-batch experimental variability. In this kind of models, batch-to-batch experimental variability may be large and generate apparent group differences. For instance, in Figure 1, HC loss seems to be deeper after 35x2 than after 50x2. Although no statistical comparison is made between these groups, there seems to be an inversion of the dose-effect relationship that may simply depend on experimental (batch-to-batch) variability.

3.b. The aim of revealing the relationship between HC loss and function retention should ideally be addressed using an experimental design providing subject-based data for comparison. That is, you cause the lesion, next you evaluate the function, and then you obtain the tissues for histological assessment, so the individual functional values can be matched to the individual HC numbers for a robust assessment of the relationship. In this work, group data from functional analyses are compared to group data from histological analyses, but no information is given on whether the same or different animals were used. If the same animals were used, the lack of direct comparison of the individual data is surprising and suggest that perhaps the comparison was made and conflicting results were observed. Alternatively, if different sets of animals were used, the conclusions on the "redundancy" of the vestibular organs are severely weakened because batch-to-batch variability in the extent of the lesion may be large and the lesions in the animals used for physiological assessment were in fact not assessed. As noted above, the possibility of a large batch-to-batch variability in the extent of the lesion is supported by the observation that lesions in 35x2 mice were deeper than lesions in 50x2 mice.<br /> 4. The conclusions on HC regeneration needs a deeper scrutiny and the conclusion on its dose-dependency is not supported by the data.

4.1. The animals used for the experiments are too young to sustain claims on adult HC regeneration. DT was administered in "4-6 weeks old" animals. In rats and mice, many HC are generated at the early postnatal days and they mature over the first month. At 4 weeks after birth (postnatal day 28), the number of immature HCs in the rat utricle is small but significantly higher than at day 60 (PMID: 38895157). Therefore, 4-week-old animals may contain a higher reserve of immature cells to show up as "new HC" after damage than 6-week or 8-week-old animals. One possible origin of the differences between 2-week and 6-month DT animals would be that the 6-month group included more animals treated at 4 weeks while the 2-week group included more animals treated at 6 weeks.

4.2. The conclusions on regeneration are based on percentages of HC densities. In the first 2-week experiment the area of the epithelium is assessed, but areas are not taken into consideration when comparing HC densities at 2 weeks and 6 months after DT. Is it possible that the increase in HC density is caused by epithelial shrinkage rather than by emergence of new HC?

4.3. The spontaneous HC regeneration is stated to be "dose-dependent", meaning that more extensive lesions caused more vigorous regeneration. However, this is only an apparent effect caused by the use of percent data. Thus, the increase in HC counts in the utricle is said to represent a 52% after 25X2 and 118% after 50X2. However, if you look at the numbers instead of percentages, the mean number of HCs is 130 vs 86 (an increase of 44) after 25X2 and 78 vs 36 (an increase of 42) after 50X2. So, the cell counts indicate tat a similar number of "new" HCs appear after either dose. 5. The use of antibodies and the exact methodology for HC counts is unclear and perhaps defective.

5.1. The immunohistochemical protocol did not include a specific marker for HCI, so HCI were defined as MYO7A+/Sox2- cells, HCII were MYO7A+/Sox2+ cells and supporting cells were MYO7A-/ Sox2+cells. The use of additional markers for the HCI (Spp1) or the calyx (Caspr1, tenascin-C) would have provided a more robust dataset. Also, striola/central versus peripheral regions were simply defined by approximate anatomical comparison, when positive markers of the central region are available (oncomodulin, calretinin+ calyces).

5.2. The primary and secondary antibodies listed do not match. Two Myosin7a antibodies were used (mouse monoclonal from DSHB and rabbit polyclonal from Proteus) and a goat anti-Sox2. However, the secondaries listed are one anti-goat and two anti-rabbits. No anti-mouse is listed.

5.3. In the figures, the reader is not informed whether the data are from the mouse anti-MYO7A or the rabbit anti-MYO7A, or whether the figure includes mixed data from both antibodies. This is highly relevant because MYO7A was used as the only positive marker for HCI, MYO7A expression may be reduced in stressed HCs (PMID: 37195449), and the two anti-MYO7A antibodies have different affinity for the target. Thus, if the 2-week samples were labelled with the mouse anti-MYO7A and the 6-month samples were labelled with the rabbit antibody, added to the possibility of reduced MYO7A expression at 2 weeks, then the apparent regeneration may be simply apparent, not real regeneration.

5.4. The images were similarly obtained with the 63X objective in both the utricle and the crista. Why two different measures (per 10,000 square micrometres in utricle and per 2500 in crista) were computed if the original area used for counts was the same? The counts are said to be derived from these 63X square images or from merged images spanning the whole utricle. However, the results section does not include the information on the particular kind of image used for any of the counts, and all are presented similarly. The method used to obtain each count should be indicated and valid comparisons should only include counts obtained with the same method. 6. The presentation of the results and its interpretation is biased. Unbiased interpretation of the results do not support conclusions such as "we found that utricle function is largely preserved until hair cell loss exceeded 90%".

6.1. "...a trend of increase....1.2+/-0.4 to 2.7+/-0.6...". These are similar very low numbers, close to zero, not a trend of increase.

6.2. The reader is informed that VsEP "is particularly dependent...striolar type I hair cells". However, the next sentence stresses that measures "remained unchanged at low dose (15 ng/g), with 54% HC survival in striola" when the percentage survival of HCI was 62.7 %. The 54% survival was for total HCs.

6.3. Lack of statistical significance is interpreted as lack of significant biological effect, when this may simply result from lack of power of the experimental design. For instance, it is concluded that the 15 ng/g dose has no effect on VsEP amplitudes, because control and DT animals did not sow statistically significant differences in this parameter. However, the comparison was made using only 4 control animals, with one of them showing a value much lower than the other 3. Also, 7 of the 8 DT animals had amplitude values below these 3 control values, and the mean value in the DT group was about 30-40% lower than the control mean. Clearly, larger groups were necessary to conclude that the 15 DT dose had no effect. Or, as suggested above, use individual animal-based comparisons to compare HC loss to loss of function. Lack of statistical significance in experiments with an insufficient number of controls can't be used to conclude that responses "were intact".

6.4. "At 25 ng/g x2.....Notably, only 3 out of 13 exhibited elevated VsEP thresholds at this dose". However, looking at Fig 5C it seems more accurate to say that 8 out of 13 exhibited elevated thresholds. "At the highest dose (35 ng/g x2), 53.8% (7 out of 13) of the animals showed elevated VsEP thresholds", but in fact all 13 DT animals showed thresholds above the mean threshold value in the control group. 7. A total of 198 vestibular afferents were measured in 5 DT mice and 195 afferents in 4 control mice. An explanation is lacking about the representativeness of these populations, whether they represent a biased or unbiased representation of the total population of afferents. 8. Information of vehicle and volume of injection of DT is lacking. 9. Vestibular organs were "harvested". How? In PBS, fixative?<br /> 10. Why was the anterior crista used for HC counts? The VOR test used examines the reflexes generated in the lateral crista, and the lateral crista is easier to image. 11. There are several reference errors, including formal errors (duplicate o missing references) and content errors (references that do not include the information that you would expect from the text where they are cited).

Referees cross-commenting

While Referee #1 states that the experiments were carefully executed, in my opinion there are many details of the experimental design and execution that need to be better explained before this statement can be made.

Significance

The question addressed is of great interest for several reasons. To explain one, the degree of redundancy in the system greatly influences the possibilities of significant functional recovery that can be achieved by therapeutic interventions aimed at triggering HC regeneration after HC loss from any cause. The DT/transgenic mouse model is certainly an interesting model to address the question.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Wang et al. presents a detailed analysis of dose‑dependent vestibular hair cell damage induced by diphtheria toxin (DT) in Pou4f3‑DTR knock‑in mice. The authors examine type I and type II hair cell survival, vestibular functional outcomes, single‑unit recordings from vestibular ganglion neurons, and dose‑dependent regenerative responses. Two mouse strain backgrounds were compared, revealing similar vestibular phenotypes but markedly different survival rates. The authors conclude that ancient vestibular functions are redundant with respect to surviving hair cells across vertebrate systems.

The experiments are carefully executed, and the data are consistent with their previous work using the same model. I recommend publication after the authors address the following minor points:

1. Synaptic Damage Not Addressed<br /> No data are presented regarding synaptic integrity, despite the well‑established vulnerability of hair‑cell synapses across ototoxic and genetic models. Because single‑unit recordings cannot resolve synaptic morphology, additional discussion is needed-beyond the brief mention on Page 16, line 4-regarding potential synaptic loss, its expected relationship to hair‑cell degeneration, and how it might influence the interpretation of afferent responses.
2. Higher DT Dose (50 ng/g ×2) Producing Less Damage<br /> In several datasets, the highest DT dose appears to induce less damage than the 35 ng/g ×2 dose. The authors should comment on possible explanations, such as DT solubility limits, receptor saturation, nonlinear pharmacodynamics, or strain‑specific physiological responses.
3. Clarification of Redundancy Concept (Page 13, lines 13-15)<br /> The manuscript states that the increase in DT‑induced unresponsive afferents supports the redundancy concept. The logic behind this connection is not fully explained. Please elaborate on how the presence of unresponsive afferents aligns with or strengthens the argument for functional redundancy in vestibular systems.
4. Therapeutic Potential of Reactivating Silent/Reserve Hair Cells<br /> The idea of reactivating silent or reserve hair‑cell populations is intriguing but underdeveloped. Expanding this section-perhaps by discussing potential molecular pathways, precedents in other sensory systems, or feasibility in mammalian vestibular organs-would strengthen the translational relevance of the work.
5. Different DT Doses Used Between Strains (e.g., Fig. 2E-G)<br /> Although the two strains are described as having similar vestibular phenotypes, some figures use 25 ng/g ×2 for one strain and 50 ng/g ×2 for the other. Please clarify the rationale for using different doses-whether due to survival differences, pilot data, or strain‑specific sensitivity.
6. Typographical Error (Page 8, line 8)<br /> A closing parenthesis appears to be missing.
7. Define IDPN at First Mention<br /> Please spell out IDPN (β‑iodopropionitrile) at its first appearance in the text.

Significance

The manuscript by Wang et al. presents a detailed analysis of dose‑dependent vestibular hair cell damage induced by diphtheria toxin (DT) in Pou4f3‑DTR knock‑in mice. The authors examine type I and type II hair cell survival, vestibular functional outcomes, single‑unit recordings from vestibular ganglion neurons, and dose‑dependent regenerative responses. Two mouse strain backgrounds were compared, revealing similar vestibular phenotypes but markedly different survival rates. The authors conclude that ancient vestibular functions are redundant with respect to surviving hair cells across vertebrate systems.

The experiments are carefully executed, and the data are consistent with their previous work using the same model. I recommend publication after the authors address the suggested minor points.

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Reply to the reviewers

Manuscript number: RC-2022-01578R

Corresponding author(s): Sabine Costagliola

1. General Statements

We are pleased to submit the revised version of our manuscript entitled “____Foxe1 deficiency impairs thyroid fate while supporting a lung differentiation program____” (Review Commons Refereed Preprint #RC-2022-01578R).

We are grateful for the careful and constructive evaluation provided by the reviewers. Their insightful comments have significantly strengthened the manuscript, both conceptually and experimentally.

We sincerely apologize for the delay in submitting this revision. Addressing the reviewers’ comments required additional experimental work, and during this period, the postdoctoral researcher who initiated and led the project completed her training and left the laboratory, requiring a reorganization of responsibilities within the team to ensure rigorous completion of the requested studies. We appreciate your patience and believe that the manuscript has been considerably strengthened as a result.

Collectively, these modifications move the manuscript beyond a descriptive study and provide new mechanistic insight into the role of Foxe1 in thyroid specification, late chromatin regulation of Pax8 expression, and the permissive state originated in the Foxe1 absence leading to Nkx2.1 differentiation into lung.

In addition, we would like to inform you that the author order has been modified in this revised version to accurately reflect contributions made during the revision process. As a result, Mírian Romitti has been moved to co–last author. All authors have reviewed and approved this change as well as the final version of the manuscript.

We are excited to resubmit this substantially improved version and believe it now provides a clearer and more mechanistically grounded contribution to the field.

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.

• *

We would like to thank all reviewers for their constructive comments and valuable suggestions, which have helped us improve the quality and clarity of our manuscript. Below, we provide a point-by-point response to all comments. The corresponding revisions have been incorporated into the transferred manuscript.

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

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Summary

The authors investigate the effect of Foxe1KO primarily on thyroid differentiation of mouse ES cells following a previously established protocol based on sequential endoderm induction, Nkx2-1/Pax8 overexpression and stimulation of the TSHR/cyclicAMP pathway. Silencing of Foxe1 expression significantly suppresses the generation of functional thyroid follicles. By single cell profiling a great number of Foxe1 targeted genes are identified, some confirmed from previous studies and some are new candidates. Embryonic bodies lacking Foxe1 instead accumulate various lung lineage cells characterized by known cell type markers, which appear to organize in lung tissue-like structures. Based on these findings, it is suggested that Foxe1 might be involved in endoderm cell fate decisions.

• *

Major comments

The title and abstract hold promise that Foxe1 is also a regulator of lung development, and that Foxe1 transcriptional activity might be decisive for thyroid versus lung fate decisions. However, there are no experimental support suggesting that one and the same ES cells at a certain critical time point may switch fate from thyroid to lung (or vice versa). Since lung markers are induced in Nkx2-1/Pax8/cAMP+ ESC it is likely that "control" organoids with maintained Foxe1 expression already contain lung lineage cells, which might expand simply by clonal selection as the thyroid lineage is suppressed by subsequent Foxe1 deletion. Although authors discuss some in this direction, it is not obvious to readers without very careful reading that this possibility and explanation is feasible and should be considered and problematized.

We thank the reviewer for this important and thoughtful comment. We agree that our data do not demonstrate a direct fate switch of individual ES cells from thyroid to lung identity at a defined developmental time point. We have revised the title, abstract, and discussion to clarify that our findings support a model of lineage stabilization and transcriptional competition rather than active binary fate conversion.

Our chromatin accessibility data argue against induction of a de novo lung program upon Foxe1 loss. In Foxe1 KO cells, we observe:

• A marked reduction in chromatin accessibility at the Pax8 locus (see Figure 6B)
• No significant gain in accessibility at canonical lung program loci (see Figure 6F) Thus, lung gene activation does not require establishment of new accessible chromatin regions. Instead, lung-associated loci appear to be in a permissive chromatin configuration in Nkx2-1+ foregut progenitors.

Importantly, quantitative lineage analysis further supports destabilization of thyroid commitment rather than emergence of a new lineage. In wild-type organoids, approximately 80% of Nkx2-1+ cells co-express Pax8, indicating strong thyroid commitment. In contrast, in Foxe1 KO organoids, only ~20% of Nkx2-1+ cells retain Pax8 expression (see data below). This substantial reduction in Nkx2-1⁺/Pax8⁺ double-positive cells indicates collapse of thyroid lineage reinforcement, leaving a larger fraction of Nkx2-1-positive cells transcriptionally permissive and capable of engaging alternative Nkx2-1-dependent programs such as lung.

Mechanistically, our data support the following model:

1. Early during differentiation, Pax8 induces Foxe1 expression.
2. Foxe1 subsequently becomes required to sustain chromatin accessibility at the Pax8 locus (supported by Figure 6B and predicted biding site, Foxe1 motif, Table S1).
3. In Foxe1 KO cells, accessibility at the Pax8 locus collapses, reducing Pax8 expression and weakening thyroid super-enhancer activity.
4. As the thyroid transcriptional network destabilizes, Nkx2-1, still expressed, can cooperate with lung-associated cofactors at already accessible lung loci.
5. Lung transcription increases without requiring de novo chromatin opening, consistent with redistribution of limiting transcriptional machinery. Supporting a more direct regulatory role, motif analysis revealed a predicted Foxe1 binding site within regulatory regions of the Pax8 locus (Table S1). This is consistent with the possibility that Foxe1 directly binds Pax8-associated enhancers, potentially recruiting chromatin remodelers and/or stabilizing enhancer-promoter interactions required to maintain high Pax8 expression. While functional validation of this binding will require future studies, this observation further supports a model in which Foxe1 actively maintains Pax8 chromatin accessibility rather than indirectly affecting thyroid identity.

Interestingly, our newly added data (Figure S8A-C) show that complete absence of Pax8 (Pax8KO mESCs) does not result in the same phenotype, displaying a complete absence of thyroid or lung organoids. This finding reinforces the hypothesis that Foxe1 is not regulating Pax8 expression at early stages of thyroid specification.

Furthermore, our previous single-cell RNA-seq analysis of mouse thyroid organoids (Romitti et al., Frontiers in Endocrinology, 2021) did not reveal substantial lung cell population under wild-type conditions, with only a small Nkx2.1-Krt5 cluster, called non-thyroid epithelial cells being identified. This suggests that high Pax8 levels in the presence of Foxe1 effectively commit most Nkx2.1+ progenitors toward thyroid fate.

Despite this, we agree that expansion of rare lung-competent cells, even if unlikely, cannot be formally excluded. Definitive resolution of whether a bipotent Nkx2.1+ progenitor with dual thyroid and lung potential exists would require dedicated lineage tracing at single-cell resolution. Such experiments would be necessary to distinguish between fate conversion and expansion of lineage-competent progenitors and lie beyond the scope of the current study.

Ultimately, we have extensively revised the manuscript to clarify these points and to avoid implying direct fate switching. Our data instead support a model in which Foxe1 stabilizes thyroid commitment by maintaining Pax8 enhancer accessibility, thereby functionally restricting Nkx2.1 from engaging alternative foregut programs.

All the above-mentioned information and discussion have been incorporated to the new version of the manuscript

Observations that Foxe1KO did not at all influence gene expression in expanding lung-like cells are consistent with the idea that lung and thyroid specification in the model are independent phenomena, and argue against the existence of a common bipotent progenitor. If authors disagree, this issue and question should be more thoroughly discussed and argued for with more supporting experimental data than found in the current manuscript version

We thank the reviewer for this important comment. As stated above, we agree that our current data do not formally demonstrate the existence of a common bipotent progenitor, and we have revised the manuscript to avoid overinterpretation in this regard.

Regarding lung genes expression, we observe significant differences between WT and Foxe1 KO organoids at day 22, as assessed by qPCR (see Figure S3). In addition, single-cell RNA sequencing reveals the presence of distinct lung cell populations in the Foxe1 KO condition, characterized by high expression of specific lung lineage markers (see Figure 4). Importantly, these lung populations were not detected in our previous single-cell RNA-seq analysis of WT thyroid organoids (Romitti et al., Frontiers in Endocrinology, 2021), except for a small population of Nkx2-1+Krt5+ cluster, indicating that their emergence is specifically associated with Foxe1 loss.

Despite the appearance of these lung-like cell types in Foxe1 KO organoids, ATAC-seq analysis does not reveal increased chromatin accessibility at canonical lung regulatory loci compared to WT (see Figure 6). This suggests that Foxe1 does not act as a direct negative regulator of the lung program. Rather, our data support a model in which Foxe1 primarily maintains thyroid lineage stability by sustaining chromatin accessibility at the Pax8 locus. In its absence, Pax8 expression is reduced, thyroid enhancer activity collapses, and thyroid differentiation is compromised.

Consequently, Nkx2-1+ cells remain in a transcriptionally permissive state in which lung-associated loci, already epigenetically accessible in foregut-derived progenitors, can be engaged. Thus, lung differentiation appears to arise not through active induction by Foxe1 loss, but through destabilization of the thyroid program, allowing Nkx2-1 to cooperate with alternative cofactors within an already permissive chromatin landscape.

To prevent misunderstanding, we have modified the title and substantially clarified the results and discussion sections to better reflect this model and to avoid implying direct lineage instruction or proven bipotency.

Minor comments

What is the fraction of. Nkx2-1+ cells that organize into follicles vs lung structures? Based on provided overview images (e.g. Figs. S1, S4) the general impression is that most cells do not form 3D-structures (i.e. do not differentiate). Please explain this and provide information in paper.

We thank the reviewer for this helpful comment and for the opportunity to clarify this point.

First, the images shown in Figs. S1B–C correspond to day 7 and Fig. S4E to day 10 of the differentiation protocol. As indicated in the figure legends, these represent early stages of the culture during which cells are still a pool of progenitor-like cells. At these time points, organized 3D thyroid follicles or lung-like epithelial structures are not yet formed. We have revised the figure legends to ensure this is clearly stated and to avoid the impression that full differentiation has already occurred at these stages.

Regarding the fraction of Nkx2-1⁺ cells that organize into follicles vs. lung structures at later stages, we acknowledge that we are not able to provide an exact quantitative proportion. Due to the 3D nature of the culture system and the size heterogeneity of the structures, precise counting of all Nkx2-1⁺ cells within organoids are technically challenging. However, based on representative images (e.g., Fig. 1C) and repeated observations across independent experiments, a subset of Nkx2-1⁺ cells clearly organize into epithelial 3D structures, while others remain unorganized or in less structured aggregates.

In the Foxe1 KO condition, the larger size and morphology of the epithelial structures suggest that a substantial proportion of Nkx2-1⁺ cells contribute to lung-like structures. Morphologically, these structures are typically larger (approximately 70–600 µm) compared to thyroid follicles (approximately 30–50 µm), supporting the impression that lung-like structures represent a significant fraction of organized epithelia in the KO condition.

Importantly, our single-cell RNA-seq data provide additional support for epithelial organization within defined clusters. The Nkx2-1/lung clusters express high levels of epithelial markers such as Epcam and Cdh1 (E-cadherin), consistent with structured epithelial identity. In contrast, only the Thyroid 1 cluster expresses these epithelial markers robustly, whereas the Thyroid 2 and Nkx2-1⁺/Pax8⁻ clusters show low or absent expression, suggesting that not all Nkx2-1⁺ cells acquire a fully organized epithelial state.

Fig. 1C: Supposed follicles are not shown in this graph.

We thank the reviewer for pointing this out. We agree that, due to the low magnification, individual follicular structures are not clearly discernible in Fig. 1C. The purpose of these images was not to illustrate fully formed thyroid follicles, but rather to highlight the relative proportion of Nkx2-1⁺/Pax8⁺ double-positive cells in control versus Foxe1 KO conditions.

To avoid confusion, we have revised the figure legend and the text and replaced the term “thyroid follicles” with “thyrocytes,” which more accurately reflects what is shown at this magnification. We believe this clarification better aligns the description with the intent of the figure.

Why does not thyroglobulin accumulate in lumen (which if present would be a good means for quantification by counting follicles)?

We thank the reviewer for this valuable suggestion and agree that luminal thyroglobulin (Tg) accumulation would, in principle, represent an informative readout for follicle quantification.

However, our organoids display a fetal-like developmental state and exhibit heterogeneity in maturation and functional competence (as expected in vivo at early development). As we have previously demonstrated (Carvalho et al., Advanced Healthcare Materials, 2023), even in highly mature thyroid organoid systems, not all morphologically defined follicles are functionally active. Thus, the absence or variability of luminal Tg or iodinated Tg (Tg-I) accumulation does not necessarily indicate absence of follicle formation at this developmental stage. In other words, Tg accumulation is not a fully reliable surrogate marker for follicle presence in this context. Here we included an example of Tg staining in mouse thyroid organoids, where we can observe some regions with Tg accumulated in the lumen, while most of the cells also show (or exclusively) cytoplasmatic staining. This image further confirms the variability in Tg accumulation among derived organoids.

To more accurately identify follicular structures, we relied on epithelial polarity and architectural markers. Specifically, we used E-cadherin and ZO-1 staining in combination with Pax8 to define organized epithelial thyroid structures. In addition, we employed an iodinated-thyroglobulin antibody (mouse anti–Tg-I, gift from C. Ris-Stalpers) and improved the quality of the Tg-I staining in Fig. 1E. This was further complemented by the Tg-EGFP reporter signal to better visualize thyroid follicular organization.

Nevertheless, due to the intrinsic 3D nature of the culture system and structural heterogeneity of the organoids, precise quantitative assessment remains technically challenging.

Indeed, follicles should be quantified to estimate induction success. Please also explain rounded structures in Foxe1KO image (are they distal lung buds?). Or are Control and Foxe1KO images confused in this panel?!?

We thank the reviewer for this important comment and for raising the need for quantitative assessment.

To estimate induction efficiency and directly compare control and Foxe1 KO conditions, we quantified Nkx2-1⁺ and Nkx2-1⁺/Pax8⁺ populations by flow cytometry (Fig. S6A-B), using the Nkx2-1_mKO2 reporter in combination with Pax8 antibody staining. We observed a marked reduction in the total number of Nkx2-1⁺ cells in Foxe1 KO organoids compared to controls, beginning at day 11 and becoming progressively more pronounced over time. By day 21, approximately 40-50% of cells in the control condition are Nkx2-1⁺, whereas only ~10-15% are Nkx2-1⁺ in the Foxe1 KO.

Importantly, co-staining with Pax8 further revealed that in control organoids, the majority of Nkx2-1⁺ cells are also Pax8⁺ (41.9% of total cells), consistent with efficient thyroid commitment. In contrast, in Foxe1 KO organoids, only 3.1% of total cells are double positive, indicating a profound reduction in thyroid lineage. These quantitative data provide a robust measure of induction success and lineage specification efficiency.

Regarding the rounded structures shown in Fig. 1D in the Foxe1 KO condition, the images are correctly assigned and not confused. These rounded epithelial structures represent the few thyroid follicles that form in the absence of Foxe1, as confirmed by Pax8 and Tg positivity. Although markedly reduced in frequency, follicle formation is not completely abolished in the KO condition. However, as highlighted in Fig. 1D, these self-organized follicles are not functionally mature, as evidenced by the absence of Nis/Slc5a5 expression. An additional example of a follicle derived in the Foxe1 KO condition is shown in Fig. S5B.

Fig. 1E: text on Fig. legend is erroneously given under (F), whereas a dedicated and relevant text for (F) is missing.

We thank the reviewer for this careful observation. The figure legend has been corrected to properly assign the text to panel (E), and a dedicated legend describing panel (F) has now been added. In addition, we have ensured that the corresponding figure panels are appropriately referenced in the main text.

Fig. 1F. Immunostaining of iodinated thyroglobulin (Tg-I) is very poor. Is it due to a bad antibody (does it work well in in vivo thyroid stainings?) or is organification simply inefficient? Again, poor content of Tg in lumen (as also suggested by Fig. S5A), it is puzzling. Or are in vitro-generated follicles leaky (i.e. do not behave as natural thyroid follicles)?

We thank the reviewer for this helpful comment. Following this suggestion, we have improved the quality of the iodinated thyroglobulin (Tg-I) immunostaining and included new images at higher quality and different magnifications in Fig. 1E. These revised images more clearly show the accumulation of Tg-I within the luminal compartment, particularly in the WT control condition.

Regarding the apparent variability in Tg accumulation, we believe this reflects the fetal-like developmental state of the organoids and the heterogeneity in their maturation and functional competence. As discussed above, not all follicles generated in vitro reach the same level of functional maturity, which may influence the degree of Tg accumulation within the lumen.

Importantly, we do not believe that the in vitro–derived follicles are structurally leaky. First, the luminal localization of iodinated Tg is clearly detectable in Fig. 1E, indicating that Tg can accumulate within the follicular lumen. Second, functional assays presented in Fig. 1F demonstrate robust iodide uptake and organification, supporting the presence of an active thyroid hormone biosynthetic machinery in these organoids.

Figs. 2A-E: Comments on lung cell markers. A: E-cad is unspecific, Sox9 would better label branching morphogenesis

We thank the reviewer for this helpful comment. The purpose of the first panel in Fig. 2 (A) was to highlight the presence of Nkx2-1⁺ cells organizing into epithelial structures, as indicated by E-cadherin staining. In this context, E-cadherin was used to visualize epithelial organization rather than to specifically identify lung lineage cells. This also allowed us to emphasize the clear morphological differences between thyroid follicles, which are typically smaller, and the larger epithelial structures observed in the Foxe1 KO condition that are consistent with lung-like structures.

The presence and identity of specific lung cell populations are further addressed in the subsequent panels of Fig. 2 (B-H) and more comprehensively in the single-cell RNA-seq dataset presented in Fig. 4.

While we agree that Sox9 staining would provide an additional marker for bud tip progenitors and branching morphogenesis, our single-cell RNA-seq analysis shows Sox9 expression within the Nkx2-1⁺/Epcam⁺/Pax8⁻/Tg⁻ population in Foxe1 KO organoids (Fig. 4B), supporting the presence of this lung progenitor population in our system.

Finally, it is important to note that our culture system (media) is not designed to promote lung development in vitro, which probably impairs the proper physiological lung tissue formation and differentiation progress observed in optimal systems and in vivo. In addition, we believe that we have fetal-like lung organoids in vitro, as comparison to scRNAseq of E17.5 suggests. These aspects were also discussed in the new version of the manuscript.

C: co-staining for E-cad would help differentiate cell types. D: Goblet cells seem Nkx2-1 negative, please explain.

We thank the reviewer for these helpful comments.

Regarding the suggestion to include E-cadherin co-staining to better distinguish cell types, we agree that this would provide additional spatial information. However, due to technical limitations related to the species of the primary antibodies used for several lung lineage markers, we were unable to include E-cadherin co-staining in many of the panels. To address epithelial identity at the transcriptomic level, in our single-cell RNA-seq analysis we specifically filtered for Nkx2-1⁺ cells that were also Epcam⁺, thereby focusing the analysis on epithelial populations present in the organoids (Fig. 4A). Consistent with this approach, the lung-related clusters identified in the dataset (Fig. 4B) show clear expression of epithelial markers, including Epcam and Cdh1 (E-cadherin) (Fig. 3E), supporting their epithelial nature.

Regarding the observation that goblet cells appear Nkx2-1 negative, we note that the Muc5ac staining shown in Fig. 2D primarily reflects secreted mucin that accumulates within the lumen of the lung-like epithelial structures rather than intracellular staining confined to individual goblet cells. As a result, the signal is predominantly detected in the luminal space, which may give the impression that it is not associated with Nkx2.1-expressing cells. To clarify this point, we provide images highlighting Muc5ac accumulation within epithelial structures that express Nkx2.1 (Fig. 2D) and Sox2 (Fig. 2F). In addition, Fig. S5C shows a large Nkx2-1_mKO2⁺/Sox2⁺ epithelial structure with clear Muc5ac accumulation in the lumen, supporting the presence of goblet-like secretory activity within these Nkx2.1–derived lung structures.

E: Diffuse pattern. Are assumed club cells really Nkx2-1 pos? CC10 immunostaining might help.

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We thank the reviewer for this helpful comment. The diffuse pattern observed in Fig. 2E is largely due to the 3D reconstruction of the image, which can reduce the apparent sharpness of individual cellular boundaries. Nevertheless, the image indicates that Scgb3a2+ cells are located within epithelial structures containing Nkx2.1–expressing cells.

Following the reviewer’s suggestion, we have now included additional immunostaining for Cc10/Scgb1a1 in the revised manuscript (Fig. 2G), which further supports the presence of club-like cells in the organoids. Although we were unable to show direct co-staining with Nkx2-1, our single-cell RNA-seq analysis confirms that all Scgb3a2⁺ and Scgb1a1/Cc10⁺ cells identified in the organoids belong to a Nkx2-1⁺/Epcam⁺ epithelial population (Fig. 4A–B and Fig. S7A). This is further illustrated in the corresponding UMAP plots shown below.

Together, these data support the interpretation that the Scgb3a2⁺ and Cc10⁺ cells detected in the organoids correspond to Nkx2.1-derived epithelial club-like cells.

F: I doubt that SEM is conclusive for identification of specific (lung) cell types unless tissue architecture (e.g. proximal-distal positions) is considered for comparison to the natural branching process of the developing lung.

We agree with the reviewer that SEM alone is not sufficient for the definitive identification of specific lung cell types. In this study, SEM was used to visualize ultrastructural features and morphological characteristics suggestive of differentiated epithelial cell types, based on comparisons with SEM images from human/mouse lungs. Importantly, our organoids do not represent adult lung tissue, but most likely fetal stages of lung development, this is an important aspect since cells might not display full features of adult lungs; e.g. ciliated cells show rather short cilia, compatible with early development. Similar aspect is observed with alveolar structures, that are most likely developing-alveolar sacs. This important aspect of developmental stage is now described in the figure legend (Fig. 2H).

To improve the clarity of our SEM images, we modified the figure and replaced images that had not very clear features by new ones. We included a new image showing mucus accumulation in the luminal compartment, a larger view of developing-alveolar sacs and alveolar cells, with a zoomed image of AT2 cell. In addition, epithelium containing secretory cells and mucus blobs was included.

Importantly, cell identity in our study was not inferred from SEM alone. We used several complementary approaches, including immunostaining, qPCR analysis, and single-cell RNA sequencing, to support the identification of the different lung epithelial populations present in the organoids.

Nevertheless, we have decided to retain instead improving the SEM images in Fig. 2H, as they provide valuable ultrastructural characterization of the organoids and illustrate morphological features consistent with differentiated lung epithelial cells.

Line 161: Is it really "spontaneous" generation? Please rephrase.

We thank the reviewer for this suggestion. The term “spontaneous” has been replaced with “unexpected” to more accurately describe the generation of these structures.

Fig. S3A. According to Major Comment above, please explain in more detail why and how lung marker expression is evident in induced "Controls" (i.e. organoids without Foxe1KO). Is it due to parallel/independent lung and thyroid differentiation? Is phenotype of rather Foxa1KO a matter of clonal selection?

Back to our previous response, the low lung marker expression observed in control organoids likely reflects the presence of Nkx2-1⁺ foregut progenitors that remain transcriptionally permissive to alternative Nkx2.1–dependent programs. In wild-type conditions, the majority of Nkx2.1⁺ cells co-express Pax8 (~80%), indicating robust thyroid commitment, still with around 20% of the cells not committing to thyroid, what could explain an “inefficient” parallel lung differentiation in presence of Foxe1. In contrast, in Foxe1 KO organoids this proportion drops to ~20%, reflecting destabilization of the thyroid transcriptional network rather than induction of a new lineage. Consistent with this, chromatin accessibility analyses show reduced accessibility at the Pax8 locus in Foxe1 KO cells without significant gain at canonical lung loci. Together, this process could allow the expansion of the non-thyroid committed progenitors and acquisition of lung cell fate due to the permissive state of the chromatin. While expansion of rare lung-competent progenitors cannot be formally excluded, distinguishing between lineage plasticity and clonal expansion would require dedicated lineage-tracing experiments beyond the scope of this study.

Figs. S3B-M. Scanning electron micrographs. Are these from one single (lung-like) structure imaged at different angles and magnitude or selected from multiple/different structures? If the latter, there a bias of selection that raises concern about cell identity. See similar SEM comment above.

We thank the reviewer for this important point. The SEM images in the old Figures S3B–M did represent distinct lung-like structures rather than multiple angles of a single organoid, as we could not obtain representative images of all cell types from the same structure. However, the SEM data presented in Figure 2 already sufficiently highlight the distinct cell types and structures. To avoid redundancy, we have therefore removed panels S3B-M in the revised version of the figure.

Line 181: Text states that cells additionally were visualized by microscopy, but this is not shown in Fig. 4.

We thank the reviewer for pointing this out. The sentence has been revised to clarify that the reporter fluorescence can be used to track differentiation by microscopy, while the efficiency of Nkx2.1⁺ cell generation is quantified by flow cytometry, as shown in Figure S4D–E rather than Figure 4. The updated sentence reads:

“The reporter fluorescence allowed tracking the Nkx2-1+ cells appearance by microscopy and quantification of the differentiation efficiency by flow cytometry (Figure S4D-E).”

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Fig. 4. Data based/biased on computationally Pax8-negative selected Foxe1KO cells. Are Pax8 negative cells present in "Control" (Foxe1+) organoids and a potential source of enrichment independent of the thyroid lineage?

We thank the reviewer for raising this important point, which prompted us to further examine the Nkx2.1⁺/Pax8⁻ cell populations in both control and Foxe1 KO samples. Flow cytometry analysis (shown below) indicates that the proportion of Pax8+ and Pax8- cells among mKO2⁺ (Nkx2-1⁺) cells was comparable between control and Foxe1 KO organoids at day 9, two days after completion of doxycycline induction. This suggests that both thyroid and lung lineages were initially induced at similar levels in the two cell lines.

This trend persists until day 12, when a clearer divergence between thyroid and lung fates begins to emerge in control versus Foxe1 KO organoids. Overall, these results indicate that Foxe1 expression reinforces thyroid lineage specification, whereas Foxe1 knockout results in an expansion of Nkx2.1+/Pax8- cells. Importantly, the PCA analysis of ATAC-seq data presented in Fig. 5G supports this conclusion.

The paper by Fagman et al. (Am J. Pathol, 2004), which shows aberrant/ectopic thyroid differentiation in airway respiratory epithelium in ShhKO mouse embryos, may by cited and discussed with reference to the possible existence of bipotent lung/thyroid progenitors/stem-like cells in vivo.

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We thank the reviewer for this valuable suggestion and apologize for not citing this highly relevant study in the previous version of the manuscript. We have now incorporated a discussion of this work in the final paragraph of the revised manuscript.

Added text in the manuscript: "In conclusion, the present work advances our understanding of the critical role of Foxe1 in initiating and sustaining proper thyroid tissue formation and function, while also highlighting novel molecular players for future investigation in thyroid biology. Beyond the thyroid, our findings underscore the intricate relationships among endodermal lineages during differentiation, particularly between thyroid and lung. Supporting this concept, in vivo studies by Fagman and collaborators (2004) showed that loss of Shh signaling during early organogenesis leads to thyroid dysgenesis and the appearance of aberrant thyrocytes expressing Nkx2-1, Foxe1, and Tg in the presumptive trachea, emphasizing the need to repress inappropriate thyroid programs in non-thyroid anterior foregut endoderm (Fagman et al., 2004). Building on this, it is intriguing to speculate that transient thyroid/lung bipotent progenitors may exist in vivo, analogous to the transient bipotent progenitors described during liver and pancreas development (Deutsch et al., 2001; Xu et al., 2011). Future studies using lineage tracing approaches could directly test the existence and fate of such progenitors, providing a deeper understanding of early endodermal plasticity and the mechanisms that safeguard lineage fidelity."

Reviewer #1 (Significance (Required)):

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The results are indeed of great value mainly for developmental biologist interested in regenerative medicine and specifically concerning in vitro systems for lung and thyroid differentiation. The provided single cell data sets of thyroid progenitors undergoing differentiation and the impact of Foxe1KO are a major achievement and resource.

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This reviewer´s expertise is mainly in vivo thyroid development.

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

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Summary: This study by Fonseca et al investigated how the specification of mouse ESCs towards thyroid lineage was regulated by the presence or absence of Foxe1, a thyroid specific transcriptional factor. Compromised thyroid induction was observed when Foxe1 was knocked out. Interestingly, the author found increased induction of lung cells in the absence of Foxe1, suggesting its role in regulating the balance of thyroid-versus-lung specification. While interesting, the main issue with this study is the lack of quantitative analysis of cellular specification, and the lack of comprehensiveness regarding the markers used to characterize each cell lineage, especially for the lung lineages.

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Major points:

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For analyzing the outcome of lineage specification in the comparison of with and without Dox or in the comparison of control versus Foxe1 KO, the only quantitative readout is qPCR. The author should perform additional characterization using flow cytometry for NKX2.1, Pax8, Tg, Tg-I, Ecad, and ZO-1 to reveal more clear mechanism: reduced number/percentage of cellular specification into thyroid lineage, or immature phenotypes in specified thyroid cells.

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We thank the reviewer for raising this important point. We agree that incorporating quantitative analyses is essential to confirm the phenotype driven by the loss of Foxe1 expression. To address this comment, we have added additional flow cytometry analyses at different time points throughout the culture in the revised manuscript (Fig. S6A–B). Specifically, we now include quantification of Nkx2.1/mKO2⁺ cells and Tg/GFP reporter⁺ cells in both control and Foxe1KO organoids from day 7 to day 21 of the differentiation protocol.

These data show that up to day 10 there is no significant difference in the proportion of Nkx2.1⁺ cells generated under the two conditions. However, from day 11 onwards the trajectories diverge clearly: in control organoids, Nkx2.1⁺ cells reach approximately 50% of the population, whereas only 10–15% of cells become Nkx2.1⁺ in the Foxe1KO condition (Fig. 6A and Fig. S6B). These findings are consistent with the reduced proportion of Nkx2.1⁺Pax8⁺ cells observed in Foxe1KO organoids (Fig. 6B and Fig. S6B), confirming the impairment in thyroid cell generation caused by the loss of Foxe1 expression. In addition, although not the most precise measure, we also observed a similar reduction in the proportion of Tg-GFP⁺ cells in the Foxe1KO condition compared with controls (Fig. 6A).

While these new results provide additional quantitative insight, accurately assessing the maturation state of the generated thyroid cells by flow cytometry remains challenging due to several technical limitations:

1. Tg quantification: Despite testing several anti-thyroglobulin antibodies for flow cytometry, we were unable to obtain reliable staining. For this reason, we included quantification of the Tg/GFP reporter described above. Despite the clear reduction in Tg+ cells among Foxe1 KO organoids, we previously demonstrated (Romitti and Eski et al., 2021; Fig. 2E) that the GFP reporter captures only a fraction of the Tg⁺ cell population present in the culture, not being the most accurate method for quantification.
2. Tg-I and ZO-1 quantification: Due to their intraluminal and apical localization within thyroid follicles, quantification of Tg-I is not possible by FC and ZO-1 staining has demonstrated to be technically difficult and did not yield reliable results.
3. Assessment of immature vs. mature thyrocytes: We believe that the combined datasets presented in Fig. 1 and the scRNA-seq analysis (Fig. 3) provide sufficient evidence to interpret the Foxe1KO phenotype. Together, these results indicate that: (i) Foxe1KO organoids show a reduced efficiency in generating thyrocytes and Nkx2.1+ cells compared with the control line; and (ii) the few thyrocytes that form in the absence of Foxe1 display impaired maturation.

The authors claimed that in the absence of Foxe1, lung organoid can be observed. Quantitative analysis, such as organoid count or flow cytometry, should be provided to assess this comparing organoid identities in the presence and absence of Foxe1.

We thank the reviewer for this important comment and we agree that a precise quantification would reinforce our findings on organoid identities. As described above, we performed flow cytometry analyses to track Nkx2.1/Pax8 cell populations over time in both WT and Foxe1KO conditions. In the WT condition, approximately 80% of Nkx2.1⁺ cells are also Pax8⁺, consistent with thyroid lineage specification. In contrast, in the Foxe1KO condition, only ~20% of Nkx2.1⁺ cells co-express Pax8, indicating a strong reduction in thyroid lineage commitment.

Although this approach does not directly quantify lung organoids, our scRNA-seq data show that the majority of Nkx2.1⁺Pax8⁻ cells in the Foxe1KO condition display an epithelial transcriptional profile, with a substantial proportion exhibiting a lung-like signature.

Regarding a direct quantification of the proportions of each organoid type, we encountered several technical limitations inherent to organoid systems. In particular, variability between wells and differentiations, combined with the three-dimensional complexity of the cultures, makes reliable counting of distinct organoid identities challenging.

With respect to flow cytometry-based quantification of lung identity, the diversity of lung epithelial cell types represents an additional challenge. Available markers often label only specific subpopulations and can overlap with thyroid markers. For example, Sox2 labels airway epithelial cells but not alveolar cells, whereas Sox9, which can mark distal lung progenitors, is also highly expressed in thyrocytes. Similarly, assays with secretory cell markers (Scgb3a2, Scgb1a1, and Muc5ac) did not yield reliable staining in our system. Hopx, an alveolar marker, is also detected in the thyroid population. Although thyroid cells can be specifically identified by Pax8 staining, this overlap further complicates the combination of markers required for reliable flow cytometry quantification of lung lineages.

Taken together, and considering that in our previous work we demonstrated by scRNA-seq that lung differentiation is not clearly observed in the control line, with only a small subset of Nkx2-1+Krt5+ cluster been detected (Romitti and Eski et al., 2021), our quantitative analyses rely primarily on Nkx2.1/Pax8 flow cytometry together with the transcriptional evidence provided by scRNA-seq.

In Figure 2, the claim of lung cell identities is not well supported. (1) SEM data on alveolar and goblet cells is not conclusive;

We agree with the reviewer that SEM alone is not sufficient for the definitive identification of specific lung cell types. In this study, SEM was primarily used to visualize ultrastructural features and morphological characteristics suggestive of differentiated epithelial cell types, based on comparisons with previously reported SEM images of human and mouse lung tissue.

Importantly, our organoids do not represent adult lung tissue but rather likely correspond to early developmental stages of lung formation. This is an important consideration, as cells at these stages may not display all the morphological hallmarks observed in mature lungs. For example, the ciliated cells observed in our organoids present relatively short cilia, which is consistent with early stages of airway epithelial development. Similarly, the structures resembling alveoli are more consistent with developing alveolar sacs rather than fully mature alveoli. This developmental context is now clarified in the figure legend (Fig. 2H).

To improve the clarity and interpretability of the SEM data, we revised the figure and replaced images in which the features were not sufficiently clear. The updated panel now includes images showing mucus accumulation within the luminal compartment, a broader view of developing alveolar sac–like structures, and a higher-magnification image highlighting cells with morphology consistent with alveolar type II–like cells. In addition, we included images of epithelial regions containing secretory cells and mucus deposits.

Importantly, cell identity in our study was not inferred from SEM alone. Instead, we used several complementary approaches, including immunostaining, qPCR analyses, and single-cell RNA sequencing, to support the identification of the different lung epithelial populations present in the organoids.

For these reasons, we chose to retain the SEM data in Fig. 2H while improving the image selection and annotations, as these images provide valuable ultrastructural information and illustrate morphological features consistent with differentiated lung epithelial structures.

In addition, it’s important to note that our system is not designed (culture media composition) for optimal generation of lung organoids and we believe that despite of the indications of fetal-like lung organoids generated they might not follow the expected physiological path observed in vitro optimal models and in vivo. It could impact the maturity and the proportions of the cells derived. This discussion is also now present in the updated version of the manuscript.

(2) Alveolar type 1 cells should be characterized by AGER and AQP5 besides HOPX

We thank the reviewer for this valuable suggestion and agree that additional markers such as AGER and AQP5 would further support the identification of alveolar type I (AT1) cells. Following the reviewer’s recommendation, we performed additional immunostainings using AQP5 and AGER antibodies. However, we were unfortunately unable to obtain reliable staining that would clearly demonstrate AT1 cells in our organoid system.

Nevertheless, both AQP5 and AGER transcripts are detected in the lung-like populations in our scRNA-seq dataset (Fig. 4 and examples shown below). Interestingly, their expression is not restricted to a single well-defined cluster, which may reflect the transitioning/immature state of the lung-like cells present in the organoids. Additional comparison to in vivo dataset suggests an enrichment in AT1 signature in cluster 0, which contains Foxe1KO-derived cells, however it might not reflect fully maturation of this cell type.

Taken together, these observations further reinforce that while lung epithelial populations are present, the organoids likely represent an early developmental stage of lung differentiation rather than fully mature lung tissue, and therefore may not yet exhibit the clear marker segregation characteristic of adult alveolar cell types.

(3) Alveolar types 2 cells should be characterized by NKX2.1 and SFTPC co-staining;

Dear reviewer, as mentioned in the previous comment, we encountered similar technical difficulties when attempting SFTPC immunostaining, and we were unfortunately unable to obtain reliable staining in our organoid system.

In contrast to Aqp5 and Ager, Sftpc transcripts were not detected in our scRNA-seq dataset. However, several other markers commonly associated with AT2 cells, such as Napsa, Abca3, and Lpcat1, are expressed in the lung-like populations (examples shown below). In addition, comparative analyses with an in vivo mouse lung dataset indicate transcriptomic similarities between E17.5 AT2 cells in vivo and a subset of cells present in the Foxe1KO organoids (Fig. 4C). This analysis also highlights the possible presence of AT2 precursors, reinforcing the immaturity of the system.

Taken together, these observations suggest the presence of AT2-like cells at an early developmental stage, rather than fully differentiated or functional AT2 cells. This interpretation is consistent with the overall developmental immaturity of the lung-like structures observed in our organoid system.

(4) For showing proximal lung identities, it would be helpful if the authors can co-stain more than one lineage, such as basal cell together with goblet cell/ciliated cells to reveal potential pseudostratified epithelium.

We thank the reviewer for this insightful suggestion. Addressing the spatial organization of proximal lung epithelial cell types within the organoids is indeed an interesting aspect. Based on our observations, multiple epithelial cell types do not appear to consistently coexist within the same organoid structure.

Our analyses indicate that many organoids co-express basal cell markers (p63 and Krt5) together with Sox2, but not together with Muc5ac, a marker of goblet cells. This observation may suggest that the in vitro system does not fully recapitulate the progressive epithelial maturation and spatial organization seen in vivo, such as the formation of a pseudostratified airway epithelium.

Ideally, this question would be addressed through three-dimensional immunostaining within individual organoid structures to visualize the spatial arrangement of the different epithelial lineages. However, despite several attempts, we were unable to obtain images that would allow reliable interpretation of such co-localization.

Regarding ciliated cells, analysis of the scRNA-seq dataset indicates that they represent a relatively rare population in our cultures, which likely further limits the ability to visualize their spatial organization within organoids.

Minor points:

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All characterization of in vitro induced thyroid cells should be accompanied by parallel analysis of native thyroid cells (from in vivo mice) that serve as a benchmark for the maturity of the induced cells. Some staining, such as Fig 1F on Tg-I remains quite different from what is reported from in vivo findings.

We thank the reviewer for this important comment. In our previous work (Antonica et al., Nature, 2012), the characterization of thyroid organoids was extensively performed in direct comparison with native mouse thyroid tissue, and all antibodies used in the study were benchmarked using mouse thyroid as a positive control. Regarding the maturity of the thyroid organoids generated in vitro, we previously demonstrated both in vitro and in vivo thyroid hormone (TH) production, confirming the functional capacity of the derived thyroid cells. Although a certain degree of heterogeneity in maturation is observed within WT thyroid organoids, likely reflecting their fetal-like developmental state, these findings support the presence of functionally mature thyrocytes.

To further address the reviewer’s concern, we have now included new Tg-I staining images in Fig. 1F, which more clearly illustrate the accumulation of the thyroid hormone precursor within the luminal compartment of follicles derived from WT mESCs.

In addition, we would like to note that the specificity and suitability of the antibodies used to stain native mouse thyroid cells have been validated in several previous studies, including Dathan et al., Dev Dyn, 2002; Gérard et al., Am J Pathol, 2008; Hartog et al., Endocrinology, 1990.

The labeling of panel E and F in Figure.1 should be switched.

We thank the reviewer for bringing this to our attention. The labeling of panels E and F in Fig. 1 has been corrected accordingly in the revised manuscript.

Reviewer #2 (Significance (Required)):

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This study provided direct in vitro evidence regarding the critical role of Foxe1 for thyroid lineage induction, and suggested its role in balancing thyroid versus lung fate determination. It is thus important to the field of both thyroid and lung developmental and stem cell biology. However, the significance of this study in hindered by the lack of comprehensiveness in the analysis.

We thank the reviewer for the positive evaluation of our study and for recognizing its relevance to both thyroid and lung developmental biology. To address the concern regarding the comprehensiveness of the analysis, we have carefully revised the manuscript to improve clarity and to better present and discuss the results of our analyses. We believe that these revisions have strengthened the manuscript and improved the overall quality of the study.

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

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Costagliola et al. have demonstrated that Foxe1, a transcription factor, plays a key role in the proper differentiation of Nkx2-1 (+) cells into thyroid follicles. They have also revealed that some Foxe1-null/Nkx2-1 (+) cells differentiate into the lung, including airway and alveolar epithelia, in their ES cell-derived organoid system. Although it has already been appreciated that Foxe1 contributes to the thyroid development in mice and humans, this excellent study has clarified that its absence, as a result, enhances the differentiation of Nkx2-1 (+) cells into the lung. I have no serious criticisms regarding methodology, results, and interpretation of results. I' d like you to elucidate whether similar findings are obtained even from human ES cell lines in the future.

We would like to express our sincere gratitude to Reviewer #3 for the positive feedback on our work. We fully agree that it will be important to determine whether similar findings can also be observed using human embryonic stem cell (ESC) systems.

While the mouse model used in this study was first reported in 2012 (Antonica et al., Nature, 2012), our group has more recently developed a corresponding system to generate functional thyroid follicular cells from human pluripotent stem cells (Romitti et al., Nature Communications, 2022). Using this human platform, we are currently investigating the role of FOXE1, as well as other genes associated with congenital hypothyroidism, in human thyroid development. We anticipate that these studies will provide further insight into the mechanisms controlling thyroid lineage specification and will be the focus of future work.

Minor comment:

1. • Fig 3C-E, Fig 6B, D, and F: These figures are so small that the words are almost illegible.*

We thank the reviewer for bringing this to our attention. The figures have been revised to improve readability, and the font sizes have been increased in Fig. 3C–E and Fig. 6B, D, and F in the updated version of the manuscript.

Reviewer #3 (Significance (Required)):

I'm a pathologist who specialize in lung cancer and the stem cells in the distal airway. This paper will probably attract those who are interested in the development of the thyroid or the lung, because the authors have revealed that 1) Foxe1 contributes to the proper thyroid development, and 2) its absence consequently enhances the differentiation of Nkx2-1 (+) cells into the lung.

We thank the reviewer for this thoughtful comment and for highlighting the potential interest of our study for researchers working in thyroid and lung development. We agree that our findings provide new insight into the role of Foxe1 in thyroid lineage specification and suggest that its absence can shift the differentiation potential of Nkx2.1⁺ progenitors toward a lung epithelial fate. We hope that these results will contribute to a better understanding of the mechanisms regulating cell fate decisions within the anterior foregut endoderm and will be of interest to both the thyroid and lung developmental biology communities.

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

Costagliola et al. have demonstrated that Foxe1, a transcription factor, plays a key role in the proper differentiation of Nkx2-1 (+) cells into thyroid follicles. They have also revealed that some Foxe1-null/Nkx2-1 (+) cells differentiate into the lung, including airway and alveolar epithelia, in their ES cell-derived organoid system. Although it has already been appreciated that Foxe1 contributes to the thyroid development in mice and humans, this excellent study has clarified that its absence, as a result, enhances the differentiation of Nkx2-1 (+) cells into the lung. I have no serious criticisms regarding methodology, results, and interpretation of results. I' d like you to elucidate whether similar findings are obtained even from human ES cell lines in the future.

Minor comment:

1. Fig 3C-E, Fig 6B, D, and F: These figures are so small that the words are almost illegible.

Significance

I'm a pathologist who specialize in lung cancer and the stem cells in the distal airway. This paper will probably attract those who are interested in the development of the thyroid or the lung, because the authors have revealed that 1) Foxe1 contributes to the proper thyroid development, and 2) its absence consequently enhances the differentiation of Nkx2-1 (+) cells into the lung.

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

Summary:

This study by Fonseca et al investigated how the specification of mouse ESCs towards thyroid lineage was regulated by the presence or absence of Foxe1, a thyroid specific transcriptional factor. Compromised thyroid induction was observed when Foxe1 was knocked out. Interestingly, the author found increased induction of lung cells in the absence of Foxe1, suggesting its role in regulating the balance of thyroid-versus-lung specification. While interesting, the main issue with this study is the lack of quantitative analysis of cellular specification, and the lack of comprehensiveness regarding the markers used to characterize each cell lineage, especially for the lung lineages.

Major points:

For analyzing the outcome of lineage specification in the comparison of with and without Dox or in the comparison of control versus Foxe1 KO, the only quantitative readout is qPCR. The author should perform additional characterization using flow cytometry for NKX2.1, Pax8, Tg, Tg-I, Ecad, and ZO-1 to reveal more clear mechanism: reduced number/percentage of cellular specification into thyroid lineage, or immature phenotypes in specified thyroid cells.

The authors claimed that in the absence of Foxe1, lung organoid can be observed. Quantitative analysis, such as organoid count or flow cytometry, should be provided to assess this comparing organoid identities in the presence and absence of Foxe1.

In Figure 2, the claim of lung cell identities is not well supported. (1) SEM data on alveolar and goblet cells is not conclusive; (2) Alveolar type 1 cells should be characterized by AGER and AQP5 besides HOPX; (3) Alveolar types 2 cells should be characterized by NKX2.1 and SFTPC co-staining; (4) For showing proximal lung identities, it would be helpful if the authors can co-stain more than one lineage, such as basal cell together with goblet cell/ciliated cells to reveal potential pseudostratified epithelium.

Minor points:

All characterization of in vitro induced thyroid cells should be accompanied by parallel analysis of native thyroid cells (from in vivo mice) that serve as a benchmark for the maturity of the induced cells. Some staining, such as Fig 1F on Tg-I remains quite different from what is reported from in vivo findings.

The labeling of panel E and F in Figure.1 should be switched.

Significance

This study provided direct in vitro evidence regarding the critical role of Foxe1 for thyroid lineage induction, and suggested its role in balancing thyroid versus lung fate determination. It is thus important to the field of both thyroid and lung developmental and stem cell biology. However, the significance of this study in hindered by the lack of comprehensiveness in the analysis.

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

Summary

The authors investigate the effect of Foxe1KO primarily on thyroid differentiation of mouse ES cells following a previously established protocol based on sequential endoderm induction, Nkx2-1/Pax8 overexpression and stimulation of the TSHR/cyclicAMP pathway. Silencing of Foxe1 expression significantly suppresses the generation of functional thyroid follicles. By single cell profiling a great number of Foxe1 targeted genes are identified, some confirmed from previous studies and some are new candidates. Embryonic bodies lacking Foxe1 instead accumulate various lung lineage cells characterized by known cell type markers, which appear to organize in lung tissue-like structures. Based on these findings, it is suggested that Foxe1 might be involved in endoderm cell fate decisions.

Major comments

The title and abstract hold promise that Foxe1 is also a regulator of lung development, and that Foxe1 transcriptional activity might be decisive for thyroid versus lung fate decisions. However, there are no experimental support suggesting that one and the same ES cells at a certain critical time point may switch fate from thyroid to lung (or vice versa). Since lung markers are induced in Nkx2-1/Pax8/cAMP+ ESC it is likely that "control" organoids with maintained Foxe1 expression already contain lung lineage cells, which might expand simply by clonal selection as the thyroid lineage is suppressed by subsequent Foxe1 deletion. Although authors discuss some in this direction, it is not obvious to readers without very careful reading that this possibility and explanation is feasible and should be considered and problematized. Observations that Foxe1KO did not at all influence gene expression in expanding lung-like cells are consistent with the idea that lung and thyroid specification in the model are independent phenomena, and argue against the existence of a common bipotent progenitor. If authors disagree, this issue and question should be more thoroughly discussed and argued for with more supporting experimental data than found in the current manuscript version.

Minor comments

What is the fraction of. Nkx2-1+ cells that organize into follicles vs lung structures? Based on provided overview images (e.g. Figs. S1, S4) the general impression is that most cells do not form 3D-structures (i.e. do not differentiate). Please explain this and provide information in paper.

Fig. 1C: Supposed follicles are not shown in this graph. Why does not thyroglobulin accumulate in lumen (which if present would be a good means for quantification by counting follicles)? Indeed, follicles should be quantified to estimate induction success. Please also explain rounded structures in Foxe1KO image (are they distal lung buds?). Or are Control and Foxe1KO images confused in this panel?!?

Fig. 1E: text on Fig. legend is erroneously given under (F), whereas a dedicated and relevant text for (F) is missing.

Fig. 1F. Immunostaining of iodinated thyroglobulin (Tg-I) is very poor. Is it due to a bad antibody (does it work well in in vivo thyroid stainings?) or is organification simply inefficient? Again, poor content of Tg in lumen (as also suggested by Fig. S5A), it is puzzling. Or are in vitro-generated follicles leaky (i.e. do not behave as natural thyroid follicles)?

Figs. 2A-E: Comments on lung cell markers. A: E-cad is unspecific, Sox9 would better label branching morphogenesis C: co-staining for E-cad would help differentiate cell types. D: Goblet cells seem Nkx2-1 negative, please explain. E: Diffuse pattern. Are assumed club cells really Nkx2-1 pos? CC10 immunostaining might help. F: I doubt that SEM is conclusive for identification of specific (lung) cell types unless tissue architecture (e.g. proximal-distal positions) is considered for comparison to the natural branching process of the developing lung.

Line 161: Is it really "spontaneous" generation? Please rephrase.

Fig. S3A. According to Major Comment above, please explain in more detail why and how lung marker expression is evident in induced "Controls" (i.e. organoids without Foxe1KO). Is it due to parallel/independent lung and thyroid differentiation? Is phenotype of Foxa1KO rather a matter of clonal selection?

Figs. S3B-M. Scanning electron micrographs. Are these from one single (lung-like) structure imaged at different angles and magnitude or selected from multiple/different structures? If the latter, there a bias of selection that raises concern about cell identity. See similar SEM comment above.

Line 181: Text states that cells additionally were visualized by microscopy, but this is not shown in Fig. 4.

Fig. 4. Data based/biased on computationally Pax8-negative selected Foxe1KO cells. Are Pax8 negative cells present in "Control" (Foxe1+) organoids and a potential source of enrichment independent of the thyroid lineage?

The paper by Fagman et al. (Am J. Pathol, 2004), which shows aberrant/ectopic thyroid differentiation in airway respiratory epithelium in ShhKO mouse embryos, may by cited and discussed with reference to the possible existence of bipotent lung/thyroid progenitors/stem-like cells in vivo.

Significance

The results are indeed of great value mainly for developmental biologist interested in regenerative medicine and specifically concerning in vitro systems for lung and thyroid differentiation. The provided single cell data sets of thyroid progenitors undergoing differentiation and the impact of Foxe1KO are a major achievement and resource.

This reviewer´s expertise is mainly in vivo thyroid development.

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

Ruby Ponnudurai

Scientific Editor

Review Commons

February 16th, 2026

Dear Dr. Ponnudurai,

Please see below for a detailed response to reviewers for manuscript #RC-2025-03108: "Short chain fatty acids regulate the chromatin landscape and distinct gene expression changes in human colorectal cancer cells".

__Authors' Summary: __We thank all the reviewers for the constructive and immensely helpful reviews of our manuscript. We have revised the manuscript addressing the reviewers' comments, which we feel has substantially strengthened our paper. Please see below for our point-by-point responses to the comments, which are all indicated in blue text. All changes in the manuscript are also indicated in blue text.

Reviewer #1 Evidence, reproducibility and clarity

In this manuscript, Kabir et al. explore the impact of microbiota-derived short-chain fatty acids (SCFAs) on chromatin structure and gene expression in human cells. They show that SCFAs, particularly butyrate, contribute to specific histone modifications such as butyrylation at H3K27, detectable in human colon tissue. Additional modifications like acetylation, butyrylation, and propionylation at H3K9 and H3K27 respond to SCFA levels and are enriched at active regulatory regions in colorectal cancer cells. Treatment with individual or combined SCFAs mimicking gut conditions alters gene expression patterns, with butyrate playing a dominant regulatory role. Butyrate's effects on gene expression are claimed to be independent of HDAC inhibition and instead rely on the p300/CBP complex through histone butyrylation. These findings underscore SCFAs as crucial modulators of epigenetic regulation in the human colon and highlight butyrate's dominant role in shaping chromatin and gene regulation beyond its known metabolic functions.

The authors used two human cell lines and an in vivo murine model paired with RNA and ChIP sequencing approaches to identify target genes and chromatin modifications in response to SCFAs.

While the findings are interesting and could provide important insights into the epigenetic influence of SCFAs in human cells, the study would benefit from additional experiments to strengthen the conclusions. Comments and suggestions are listed below:

Response: We sincerely thank the reviewer for their thoughtful and constructive comments. In addition, we appreciate the recognition of the potential impact of our findings. We have addressed all comments below.

1. Figure 1: The H3K27bu expression in human biopsies highlights the clinical significance of the current study. However, the authors need to provide more information on the human colon samples, e.g., how many total patients were analyzed, and what were the age and/or sex. Only the methods mention the use of benign TMA; this should also be clarified in the figure legends. It would also be helpful to show histone butyrylation levels in normal vs. cancer human tissues.

Response: We completely agree that analysis of additional patient samples is important. In light of this comment, we have expanded our analysis of human colon samples. In the original manuscript, we showed IF images from patient intestinal sections. Patient demographic information (age and sex) is now included in the figure legend. While we analyzed two patients by IF, we realized that images from only one patient are shown. We also felt it was important to add additional rigor to our patient analysis. Therefore, we have incorporated additional patient samples and performed H3K27bu staining using IHC across normal and colon cancer sections obtained from 40 different patients. This is now included as Supplemental Figure 1. In addition, we have included information about age, sex, staging, and grading in Supplemental Figure 1C. Interestingly, we observed that adenocarcinoma patients have significantly decreased levels of H3K27bu compared to normal colon or normal adjacent tissues (Supplemental Figure 1B). We speculate that this may be due to alterations with the microbiota composition and dysbiosis associated with colorectal cancer (PMIDs: 26515465, 25758642, 25699023). Very interestingly, this is in contrast to reports of elevated H3K27ac in colon cancer samples (PMID: 24994966). We are excited to explore this further, and this is something we plan to follow-up on in future studies.

1. Figure 1: In addition, given that the butyrate level descends towards the base of the colonic crypt (with the highest at the top of the crypt where mature intestinal epithelial cells reside) (Kaiko et al., 2016), it is important to show how the H3K27bu signature is distributed along the crypt. This data would further emphasize the clinical relevance of this study, given that most colorectal cancers (CRCs) arise from stem and progenitor cells.

Response: We agree that this is an important question and recognize the elegant study by Kaiko et al. However, our human samples are obtained from commercially available tissue microarrays and the sectioning is not consistent across samples, resulting in a minimal amount of samples that we could analyze for staining patterns from crypt to villi (please see Supplemental Figure 1A for example sections). This unfortunately prevents us from completing rigorous image analysis. In future studies, we plan to perform this analysis after we obtain an IRB protocol that will allow us to answer this question in the most rigorous way possible.

Throughout the manuscript: The rationale for selecting the two CRC cell lines (HCT 116 and Caco2) should be explained. While commonly used, providing background on their genetic differences (e.g., driver mutations) is important, as this could greatly influence the PTM landscape.

Response: We chose to use both HCT-116 and Caco-2 cancer cell lines throughout our studies, since as noted these cells are the most commonly used lines in the literature. In addition, having consistent results across distinct genetic backgrounds strengthens our results: using both cell lines tells us whether observed PTM patterns are conserved across genetically diverse CRC contexts, as HCT-116 is characterized by mutations in KRAS and PIK3CA, while Caco-2 has mutations in APC and TP53 (PMIDs: 17088437, 24755471, and 16418264). We have added this information into the text in lines 106-107.

The study lacks additional controls, such as a normal colon epithelial cell line and a non-colonic cell type. Including these would help determine whether the observed butyrate effects are tissue- or disease-specific. This data would also help assess whether SCFA effects, and specifically butyrate's effects, on histone acylation and gene expression are systemic or local.

Response: Thank you for this insightful comment. We have now included additional data using normal colon cells in the form of mouse colon organoids and a distinct non-intestinal cell line, the embryonic kidney cell line HEK 293T. Importantly, we observe similar changes to chromatin after treatments with different SCFAs in both colon organoids and HEK 293T cells as shown in the cancer cell lines (Figure 1E, 1F). Interestingly, we also observe that the colon cancer cell lines have visible signal of histone butyrylation without treatment, while we only observe these modifications in HEK 293T cells following treatment.

As for understanding systemic vs. local effects of butyrate on chromatin, we additionally treated cells with different concentrations reflecting the intestinal lumen or serum concentrations of SCFAs: 5 mM and 5 µM, respectively. While the concentrations of SCFAs can vary across individuals, we felt that these numbers reflected differences in intestinal vs. serum levels based on the literature (summarized in PMID: 27259147). Importantly, we observe that only the 5 mM SCFA treatment reflecting levels in the intestinal lumen results in induction of histone acetylation and butyrylation, while the 5 µM treatment reflecting serum SCFA levels failed to induce increased levels of these histone modifications (Figure 1F).

Together, this data suggests that the response on chromatin to SCFAs is more universal at high concentrations. However, based on local vs. systemic concentrations throughout the body, we expect that responses on chromatin will largely be restricted to the intestine or in other areas or conditions where high concentrations of metabolites are localized.

Figure 2: The authors show ChIP-seq results in the HCT 116 cell line. To exclude the possibility that the demonstrated chromatin signatures are cell line-specific, results from Caco2 should also be shown. In addition, the 2D environment and multiple passaging alter gene expression in cell lines; using human colonic organoids would provide a more clinically and physiologically relevant model.

Response: We have now added Cut&Run analysis for the histone acyl marks of interest in Caco-2 cells, which is a technique analogous to ChIP to map genomic localization. Please see now Figure 2C-D. Importantly, we observe very similar localization of these histone modifications across the different cell lines. We also agree that the question of how 2D vs. 3D environment may impact localization of these modifications is important. In organoids, ChIP-seq and Cut&Run are technically difficult. In addition, we feel that using human organoids is currently beyond the scope of our manuscript. However, we previously characterized H3K27bu and H3K27ac occupancy from primary epithelial cells isolated from the mouse intestine (PMID: 38413806). Importantly, in this study we observed similar genomic enrichment of H3K27bu and H3K27ac. This suggests that the general patterns of localization of these modifications across species and across cells isolated from both 2D vs. 3D systems are similar.

Figure 4 is very confusing. Entinostat itself, as an HDAC inhibitor (iHDAC), increases butyrylation. The data shown are insufficient to draw conclusions. First, the authors should use additional iHDACs, and second, they should illustrate the overlap in gene expression changes between all treatments using a Venn diagram to clarify which genes/signatures are specific to each treatment.

Response: We agree that testing additional iHDACs is important. We have now included an additional iHDACs (Tucidinostat) in our studies to make more widespread conclusions beyond the activity of Entinostat. We have performed additional treatments, demonstrating that all iHDACS tested increase both histone butyrylation and acetylation (Supplemental Figure 8A-B). We also have performed qPCR for candidate differential genes and demonstrated that expression changes following our treatments with Tucidinostat phenocopy changes observed with Entinostat (Figure 5F). These dynamic gene changes show examples of genes that are responsive to butyrate treatment and p300/CBP inhibition, yet differ from other iHDAC treatment. As requested, we have additionally added a Euler plot to Figure 4 depicting the overlap between treatments in this figure (Figure 5C).

Figure 4: The authors use an HDAC inhibitor to rule out butyrate's effect on gene expression via HDAC inhibition. However, butyrate can also modulate gene expression through activation of GPR109a. Using GPR109a antagonists is necessary to address this possibility. These data are essential to validate the specific role of histone butyrylation in gene regulation.

Response: We thank you for this comment and completely agree that butyrate can act through multiple mechanisms, including activation of GPR109a. However, it has previously been demonstrated that this receptor is silenced via DNA methylation in human colon cancer samples and colon cancer cell lines, including HCT-116 (PMID: 19276343). Supporting this notion, we observed very low expression levels of this receptor in our HCT-116 cells (please note the very low TPM values), with minimal differences in response to butyrate treatment (Supplemental Figure 6E, included below). We have additionally included gene expression data for two other potential GPCRs activated by butyrate or other SCFAS (FFAR2 and FFAR3), and also observe very low expression of these genes. Therefore, we concluded that the butyrate effects on gene expression independent of HDAC inhibition in our data are not likely to be dependent on GPR109A or FFAR2/3 signaling.

New ____Supplemental Figure 6E____: mRNA expression of GPCR genes that are known SCFA targets. Levels of mRNA expression (transcript per million, TPM) as assayed by RNA-seq of GPR109A (official gene name HCAR2), FFAR2, and FFAR3 in HCT-116 cells. Expression levels related to Figure 3. Statistical significance was determined using ANOVA adjusting for multiple comparisons with p

Supplementary Figure 4 and manuscript: There is no in vivo methods section describing the tributyrin-gavaged mice. The authors should clarify how the experiment was performed, how cells were isolated, whether sorting was performed, and which markers were used.

Response: We apologize for this confusion. The in vivo data is from previously published work that is publicly available (PMID: 38413806). We analyzed data from mice that were gavaged with tributyrin, where non-sorted IECs were analyzed for RNA-seq. We have clarified this and have added this information in the figure legend (now Supplemental Figure 6).

Supplementary Figure 4: The GO analysis results show that lipid catabolism is among the top differentially enriched pathways. Butyrate is a known PPARγ agonist (Litvak et al., 2018), and activation of PPARγ is known to drive expression of genes involved in lipid metabolism. The authors need to rule out this function of butyrate before attributing this signature solely to histone butyrylation.

Response: We appreciate this point and have performed additional analysis to identify whether canonical PPARγ target genes are enriched or not in our data. Additionally, we recognize that our data may reflect the combined effects of both PPARγ activation and histone butyrylation. In Supplemental Figure 6 (Supplemental Figure 4 in the previous version), we especially acknowledge that the differential genes changing may be due to varied mechanisms of butyrate action. Therefore, to address this comment, we performed additional analysis on data related to Figure 5 (previously Figure 4), where we have additional treatments including using a p300/CBP inhibitor to identify potentially more chromatin related mechanisms of action.

We have now extended our analysis of RNA-seq data related to Figure 5 to include gene ontology enrichment that is not dependent on clustering (Supplemental Figure 9A). While we do not observe PPARγ target genes as top enriched categories, we have also specifically tested the enrichment of PPARg-related MsigDb groups using publicly available datasets (Supplemental Figure 9B). Here, we observe some enrichment of different gene sets related to PPARγ activity across different tissue systems. Together, this new data suggests that some PPARg targets are enriched with our different cell treatments, including butyrate, but they are not the predominant gene categories that we observe changing.

Most PPARg target genes have been identified in tissue systems beyond the gut, such as adipose tissue and immune cells. To specifically analyze genes in the intestine that are PPARg-dependent, we identified select genes in the literature (PMIDs: 29182565, 28798125, and 28798125). In PMID: 29182565, these genes include lipid transport (Cd36), lipolysis (Hsl, and Atgl), and various lipid metabolism pathways (Cact, Fasn, Mlycd, Dgat2, and Agpat9). In PMID: 28798125, these genes include HMOX1, PDK4, ANGPTL4, UCP2, AQP8, and PLIN2 as butyrate/ PPARg targets. PMID: 28798125 identified Nos2 as a butyrate and PPARg target. Their expression levels following butyrate and other treatments in Figure 5 (formerly Figure 4) are now included as Supplemental Figure 9C (also included below). Interestingly, these genes respond differently compared to the other iHDAC tested (Entinostat) and are only mildly impacted by p300/CBP inhibition (please see A485_Butyrate column vs. Butyrate alone). This suggests that the major impacts on this pathway are not through p300/CBP activity or histone butyrylation, but may be due to other mechanisms of butyrate action. We have also included additional discussion of butyrate and potential roles of PPARg signaling in lines 243-256.

New Supplemental Figure 9C.

It would be helpful to include a table of differentially abundant genes as a supplement to the heatmaps and GO analysis.

Response: We are happy to include tables of differentially expressed genes from all our analysis as supplemental files. This is now included as Supplemental Table 1.

Significance

This study explores how microbiota-derived SCFAs, particularly butyrate, influence histone acylation and gene regulation. While the topic is relevant, the work lacks important controls (e.g., normal epithelial and non-colonic cells) and omits mechanistic validation (e.g., GPR109a signaling, PPARγ involvement). The rationale for cell line selection is unclear, and in vivo methods are insufficiently described.

Audience: The study will mainly interest specialists in microbiota-chromatin interaction. Broader impact is limited by the narrow model scope and underdeveloped mechanistic insight.

My Expertise:

Cancer biology, in vivo models, microbiota-host interactions.

Response: We sincerely thank the reviewer for their very helpful comments. We hope that the above point-by-point responses adequately addresses concerns regarding controls, mechanistic validation, and methods description. We really appreciate their note that the topic is relevant, yet we also feel that our work will have broader impacts due to the interdisciplinary nature of the research and the inclusion of additional model systems (intestinal organoids and additional cell lines) and mechanistic experiments.

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

This study presents a novel finding that short-chain fatty acids (SCFAs) produced by microbial metabolism regulate gene transcription in human colon cancer cells by modulating histone H3K9 and H3K27 butyrylation and propionylation, both of which are associated with an open chromatin state. The authors further reveal that the major effect of the SCFA mixture is driven by butyrate and identify p300/CBP-dependent, rather than HDAC inhibition-dependent, gene regulation by butyrate. Overall, this is a well-organized study that provides valuable insight into the role of metabolites in human cells.

Response: Thank you for your positive review of our manuscript. We really appreciate the reviewer pointing out the novelty and organization of our study. Please see below for point-by-point responses to your comments.

Major comments:

1. In Figures 1C and 1D, why did the SCFA mixture not increase histone butyrylation or propionylation to the same level as single butyrate treatment? Response: Thank you for this question. We believe that this effect is observed due to differences in butyrate concentrations, as we aimed to keep the total concentration of SCFAs equal across all treatments at 5 mM. In the single treatment, butyrate is at 5 mM while in the mixtures, butyrate is at 1.67 mM (1:1:1) or 1 mM (3:1:1). In addition, in Figure 3A we included a 15 mM mixture for RNA-seq analysis, where butyrate and the other SCFAs are all at 5 mM concentrations. Since we observed highly similar patterns of gene expression with 15 mM or 5 mM final SCFA mixture concentrations, we did not include the 15 mM treatment in our other experiments.

In Figure 3B, how does butyrate block the effects of acetate and propionate on transcription?

Response: This is a great question, but we are not necessarily claiming that butyrate is blocking effects of acetate and propionate on transcription. For example, it is also possible that butyrate induces more gene expression changes compared to acetate or propionate, as the number of differentially expressed genes is greater in butyrate-treated cells (Response Table 1).

Comparison vs. vehicle

__Upregulated __

(log2FC > 0)

__Downregulated (log2FC

__Upregulated __

(log2FC > 1)

__Downregulated (log2FC

Acetate

3160

3518

433

352

Propionate

3402

3854

1304

735

Butyrate

4600

4539

2082

1727

__Response Table1. Number of differentially expressed genes for each SCFA treatment group, related to Figure 3. __RNA-seq was performed on HCT-116 cells grown in DMEM and treated with 5 mM of single SCFAs for 6 hours. Differential genes were identified using DESeq2 Wald test and statistically significant genes were defined using a padj To fully understand mechanistic differences of butyrate vs. acetate or propionate, we would need to perform additional experiments that we feel are beyond the scope of this current manuscript. However, we speculate that several mechanisms could account for these differences: for example, different histone acylations could have differential impacts on chromatin structure, reader binding, or transcription factor recruitment. As for blocking effects, select longer acylations (butyrylation and crotonylation) have been demonstrated to have repressive effects in transcription or reader protein binding in specific cell contexts (example PMIDs: 27105113, 31676231, 37311463). These are important future studies for our group and will likely shed light on additional mechanistic insights of different histone acylation functions. We have highlighted some of these concepts in the discussion (lines 301-310):

"We also observe that butyrate and propionate treatment have both overlapping and distinct effects on gene regulation (Figure 3, Supplemental Figure 4, Supplemental Figure 8D). Propionate appears to have more modest effects compared to butyrate, as it induces a smaller number of differential gene changes and these genes do not display enrichment in ATP and nucleotide metabolism categories. These differences in gene regulatory responses to the different SCFA treatments could be due to multiple mechanisms. For example, we speculate that there could be chromatin-independent functions through distinct alterations in metabolic or signaling pathways or chromatin-dependent mechanisms through potential distinct structural effects on chromatin or differences in reader protein binding."

Which pathways are associated with acetate- and propionate-specific DEGs?

Response: Thank you for this insightful question. We have performed gene ontology analysis for acetate and propionate DEGs. Interestingly, there is largely overlap between the different SCFA treatments (Supplemental Figure 4A). However, propionate treatment fails to enrich for select gene ontology categories that we observe in acetate treatment (Supplemental Figure 4B, __included below). For example, by gene set enrichment analysis, acetate enriches for gene categories related to nucleotide and ATP synthesis, while propionate does not. However, both acetate and propionate (and all SCFA treatments) are enriched in categories related to the ribosome and rRNA (__Supplemental Figure 4B-C). We have added this analysis to the manuscript as Supplemental Figure 4 and included additional discussion of this analysis in the text in lines 163-171 (included below), as well as additional speculation about differences between propionylation and butyrylation in lines 301-310 (included above).

*"We further analyzed gene programs changing with different SCFA treatments. All SCFA treatments regulated largely overlapping gene programs including those related to RNA metabolism, ATP synthesis, and ribosome function (Supplemental Figure 4a). Since butyrate overlapped greatly with the combination SCFA treatment, we specifically analyzed acetate and propionate gene programs (Supplemental Figure 4b-c). Interestingly, propionate treatment failed to enrich for select gene ontology categories that we observe in other SCFA treatments. Specifically, propionate-dependent gene programs did not include those related to ATP and nucleotide metabolism, highlighting some differences in gene expression changes following different SCFA treatments." *

• *

New__ Supplemental Figure 4B.__

Which genes are related to growth inhibition in butyrate-treated cells? Does the 1:1:1 SCFA mixture have a similar impact on cell growth as single butyrate treatment?

Response: Butyrate has previously been shown to inhibit cell growth in colon cancer cells (PMIDs 9125124, 33017771, 38398853). These include differential regulation of key cell cycle regulators, such as p21 and Cyclin D1. We have included both GO term enrichment for the 1:1:1 SCFA mix and gene expression data for select cell cycle regulators in Supplemental Figure 7C-D (7D also included below). This demonstrates that both butyrate and the SCFA mixtures, and to a lesser extent propionate, differentially regulate key cell cycle genes including CDKN1C, CDK2, CDK4, WEE1, and RB1. We have additionally performed a GLO assay for the 1:1:1 SCFAs treatment to investigate its impact on growth inhibition, which is now included as Supplemental Figure 7B. Here, we observe that the 1:1:1 and 3:1:1 mixtures of SCFAs significantly decrease cell viability. However, this is not to the same extent as butyrate treatment alone. Together, this data suggest that butyrate reduces cell viability at least in part through altering key cell cycle genes. This effect is mimicked with the SCFA mixture treatments, but to a lesser extent compared to butyrate alone.

New Supplemental Figure 7D.

Reviewer #2 (Significance (Required)):

General assessment: This study clearly demonstrates the role of butyrate in gene regulation and elucidates its underlying regulatory mechanisms. However, it does not provide insight into how butyrate counteracts the effects of acetate and propionate, despite these metabolites often being detected together. In addition, it remains unclear which specific histone PTMs are associated with the distinct gene expression changes induced by different short-chain fatty acids. Lastly, the observation that histone butyrylation and propionylation correlate with active transcription is not novel.

Advance: This study advances understanding of short-chain fatty acids in chromatin and gene regulation, highlighting butyrate's dominant role and its p300/CBP-dependent rather than HDAC inhibition-dependent mechanism.

Audience: This work may attract significant interest in both the epigenetics and metabolism fields.

My expertise: histone acetylation, HATs, transcriptional regulation, cancer.

Response: We very much appreciate all of these thoughtful comments. We are thankful for the recognition that this story advances our understanding of SCFA function through chromatin and may be of significant interest to the epigenetics and metabolism fields. We hope that we have now provided additional insight into roles of propionate and acetate (Supplemental Figure 4). We also recognize that similar to other studies, we observe colocalization of the different histone marks and it is difficult to tease apart specific functions. We plan to further address this important question in future studies.

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

Summary: The authors explore the effects of short-chain fatty acids (SCFAs) acetate, propionate, and butyrate on chromatin and gene expression in human colon cancer cells. The authors first characterize the presence of histone propionylation and histone butyrylation in different colon cancer cell lines as a function of SCFA treatments. Then, they perform ChIP-seq to determine the genomic localization of these marks and observe that these marks are deposited on euchromatic regions similar to H3K4Me3 and to one another, consistent with previous reports. The authors then performed gene expression analysis to determine the contribution of the SCFAs. Interestingly, they observe that butyrate treatment alone mimicked the gene expression profile of an equimolar mixture of short-chain fatty acids treatment, at least in the tested cell lines. Finally, the authors designed an experiment to try to separate the functions of butyrate on gene expressions that are dependent on p300/CBP and are independent of the HDAC inhibition property. The following aspects of the paper need addressing-

Response: We sincerely thank the reviewer for their very helpful and constructive comments. We appreciate the notes on interesting aspects of our study. We hope that we have addressed all concerns as described below.

Major comments

1. There is no confirmation of the validity of the results seen from ChIP-seq (Figure 2) and RNA-seq (Figure 3). The majority of the findings of the paper are derived from ChIP-seq and RNA-seq data, and hence, experiments validating such results need to be established. ChIP-qPCR for representative gene(s) with adequate controls needs to be performed for different acyl marks (H3K27bu, H3K27pr, H3K4Me3, H3K9pr, H3K9bu) to support the ChIP-seq results, and RT-qPCR for representative gene(s) for different treatment conditions (vehicle, acetate, propionate, butyrate, and 5 mM 1:1:1 mixture) for validating RNA-seq results. Response: We are happy to include validation by qPCR of our ChIP and RNA-seq results. The qPCR validation for Figure 3 is now included as Figure 3F and qPCR validation for ChIP-seq is included as Figure 4C. We have selected genes that are differentially expressed and also display occupancy of different histone acyl marks. In addition, we performed additional qPCR validation for our RNA-seq data related to Figure 5 (previously Figure 4), which is now included as Figure 5F-G. Lastly, we performed orthogonal analysis of ChIP using Cut&Run in Caco-2 cells, which is now included as Figure 2C-D. This further supports our findings with HCT-116 cells.

The authors describe an interesting strategy to differentiate the different functions of butyrate (Figure 4). The authors propose that differential genes that change with p300/CBP inhibitor treatment, that are separate from HDAC inhibitor treatment, are potential genes that are a function of histone butrylation. An important control that is missing in this experiment is cells treatment with propionate. In their previous findings (Figure 1C-D), they note that both propionate and butyrate treatments elevate the levels of histone acetylation, propionylation, and butyrylation. But the HDAC inhibitory activity of propionate is not very well established, and performing experiments to prove it is are beyond the scope of this paper. Importantly, p300/CBP has been shown to catalyze histone propionylation with higher efficiency compared to histone butyrylation (PMID: 27820805, PMID: 29070843). Therefore, it would be ideal to include differentially expressed genes from propionate-treated cells in the analysis to rule out any discrepancy.

Response: Thank you for this insightful comment. We agree that propionate also elevates histone butyrylation and may have important effects. We have therefore included our differentially expressed genes with propionate treatment from Figure 3 in our analysis related to HDAC inhibition: we have plotted these differentially expressed genes in a matched, ordered column to our clustering analysis in Figure 4 (now Figure 5) as Supplemental Figure 8D (also included below). This demonstrates that overall propionate has similar gene expression changes to butyrate, but the extent of these changes is less pronounced compared to butyrate. In addition, our qPCR validation analysis in Figure 3F demonstrates that propionate similarly regulates some differentially expressed genes affected by butyrate (such as PHOSPHO1 and HOXB9) but fails to differentially regulate other targets (such as CYSRT1). This suggests that propionate and butyrate have both overlapping and distinct targets, which is consistent with our global analyses in Figure 3A-D. Lastly, we now have included specific analysis of gene program changes related to propionate treatment (Supplemental Figure 4). Interestingly, there is largely overlap between the different SCFA treatments (Supplemental Figure 4A). However, propionate treatment fails to enrich for select gene ontology categories that we observe in other SCFA treatments (Supplemental Figure 4A-B). For example, by gene set enrichment analysis, other SCFA treatments enrich for gene categories related to nucleotide and ATP synthesis, while propionate does not. However, all SCFA treatments are enriched in categories related to the ribosome and rRNA (Supplemental Figure 4B-C). Together, this data suggests that propionate has largely similar effects to butyrate treatment in regulating gene expression programs with some distinct differences.

New Supplemental Figure 8D.

Along the same lines as comment #2, other possible "functions" of propionate and/or butyrate that could explain why treatment with them increase histone acetylation, propionylation, and butyrylation are not discussed. This work was not cited/discussed: PMID 34677127 despite being very closely related and relevant. Indeed, there seems to be some redundancy of efforts between that paper (2021) and this one even in terms of the specific experiments performed.

Response: Thank you for this comment, and we sincerely apologize for our oversight in not citing this important work. We are very familiar with this paper, and this was an unfortunate accidental oversight. We have now cited it throughout the text in lines 51, 123, and 330. In addition, we expanded our discussion about how our single treatments of butyrate or propionate increase levels of multiple histone acyl marks including acetylation, butyrylation, and propionylation. We now include activation of p300 as a potential mechanism for this observation in lines 327-330: "This is consistent with the role of butyryl-CoA and propionyl-CoA functioning as activators of p300 acetyltransferase activity, where these molecules can directly stimulate p300 auto-acylation and acetylation activity on histones and other substrates12" Lastly, while we agree that many of our treatments are similar to this paper, we also feel that our downstream analysis is distinct, as we are focusing on genomic localization and gene expression changes, in addition to changes in levels of the histone marks themselves. We believe that this distinction lessens the redundancy between our papers and may be of interest to the chromatin field.

An analysis for correlations between the ChIP-seq data for H3K27bu (Fig 2) and RNA-seq data following butyrate treatment (Fig 3) would provide further insights into whether the genes/pathways that are enriched/downregulated in H3K27bu ChIP-seq data correlate with genes/pathways that are upregulated/downregulated in RNA-seq data.

Response: We really appreciate this suggestion and agree that this analysis would add important additional insights. We have therefore performed this analysis through binning genes by expression level and analyzed occupancy of H3K27bu according to gene expression quartiles, which is now included as Figure 4B. Additionally, we included the other histone butyrylation and propionylation marks that are the focus of our manuscript. We have found that levels of H3K27bu occupancy are correlated with high gene expression quartiles. Importantly, this is also consistent with our earlier work in primary mouse intestinal cells (PMID: 38413806).

Minor comments

1. All the images appear to be very low resolution. This could be due to the online submission system. Response: We apologize for this issue and believe it is due to the submission system.

For Fig 2, the caption says "...treated with different SCFAs for 24 hours," but it is unclear precisely what the treatment was. Were the cells treated with the SCFA mix, and then ChIP-seq was performed for the 5 different marks tested? Or were there different SCFA treatments performed for each mark that was ChIPed?

Response: We have revised the text of the figure legend to make it clear that we treated cells with individual SCFAs (propionate for propionylation marks and butyrate for butyrylation marks).

Line 99-100: "Treatment with butyrate, propionate, or a mixture of all three SCFAs resulted in a global increase in histone butyrylation or propionylation" is misleading. The authors test only specific sites on Histone H3 using site-specific antibodies and do not test whether these treatments increase global levels of acylation on other histones and sites using pan-acyl antibodies. So, this sentence needs to be rephrased to clearly indicate that the treatments only increased at the tested sites.

Response: Thank you for this comment. We understand this was misleading and that was not our intention at all. By writing "global levels," we simply meant levels of immunoblotting signal at these specific lysine residues. We have therefore revised the text to make it clearer (now in lines 102-104): "Treatment with butyrate, propionate, or a mixture of all three SCFAs resulted in significant increases of histone butyrylation and propionylation at select residues of histone H3, as assayed by immunoblotting".

Reviewer #3 (Significance (Required)):

Strengths and limitations: The experiments in the study were performed with a high degree of rigor, including appropriate controls. The discussion of the -seq data in Figs 2-4 avoided focusing on or following up on specific genes, which limited the conclusions from these data to being very broad. A key paper (that was not recent) was missing from the context presented in the paper, weakening the discussion of the data presented.

Advance: The advance is pretty conceptually incremental. Similar experiments as in Fig 1-3 in similar models have been performed in other papers already (e.g., PMID 39789354 in 2025 and PMID 34677127 in 2021), although Fig 4 was an interesting experiment that helps differentiate the work from existing literature.

Audience: This work would be interesting to a chromatin audience as well as a microbiome audience, but the scope of the conclusions from this paper, and it's redundancy with other literature, will limit its profile.

My expertise is in histone PTM biochemistry and biology, including non-canonical histone acyl PTMs.

Response: We really appreciate the thoughtful and constructive comments and the recognition that this story may be of interest to the chromatin and microbiome audiences. In addition, we acknowledge other similar recent work that is also very interesting, but we also feel that our manuscript is distinct in several important ways from these studies. In particular, the analysis of gene expression changes that we propose to be histone butyrylation dependent vs. through HDAC inhibition (Figure 5, previously Figure 4) and the finding that butyrate drives SCFA combination gene expression changes (Figure 3). We are very grateful for the recognition of these interesting findings by this reviewer. Furthermore, we also want to highlight that we have expanded our analysis of human tissues (Supplemental Figure 1), which adds additional novelty to this work.

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Referee #3

Evidence, reproducibility and clarity

Summary: The authors explore the effects of short-chain fatty acids (SCFAs) acetate, propionate, and butyrate on chromatin and gene expression in human colon cancer cells. The authors first characterize the presence of histone propionylation and histone butyrylation in different colon cancer cell lines as a function of SCFA treatments. Then, they perform ChIP-seq to determine the genomic localization of these marks and observe that these marks are deposited on euchromatic regions similar to H3K4Me3 and to one another, consistent with previous reports. The authors then performed gene expression analysis to determine the contribution of the SCFAs. Interestingly, they observe that butyrate treatment alone mimicked the gene expression profile of an equimolar mixture of short-chain fatty acids treatment, at least in the tested cell lines. Finally, the authors designed an experiment to try to separate the functions of butyrate on gene expressions that are dependent on p300/CBP and are independent of the HDAC inhibition property. The following aspects of the paper need addressing-

Major comments

1. There is no confirmation of the validity of the results seen from ChIP-seq (Figure 2) and RNA-seq (Figure 3). The majority of the findings of the paper are derived from ChIP-seq and RNA-seq data, and hence, experiments validating such results need to be established. ChIP-qPCR for representative gene(s) with adequate controls needs to be performed for different acyl marks (H3K27bu, H3K27pr, H3K4Me3, H3K9pr, H3K9bu) to support the ChIP-seq results, and RT-qPCR for representative gene(s) for different treatment conditions (vehicle, acetate, propionate, butyrate, and 5 mM 1:1:1 mixture) for validating RNA-seq results.
2. The authors describe an interesting strategy to differentiate the different functions of butyrate (Figure 4). The authors propose that differential genes that change with p300/CBP inhibitor treatment, that are separate from HDAC inhibitor treatment, are potential genes that are a function of histone butrylation. An important control that is missing in this experiment is cells treatment with propionate. In their previous findings (Figure 1C-D), they note that both propionate and butyrate treatments elevate the levels of histone acetylation, propionylation, and butyrylation. But the HDAC inhibitory activity of propionate is not very well established, and performing experiments to prove it is are beyond the scope of this paper. Importantly, p300/CBP has been shown to catalyze histone propionylation with higher efficiency compared to histone butyrylation (PMID: 27820805, PMID: 29070843). Therefore, it would be ideal to include differentially expressed genes from propionate-treated cells in the analysis to rule out any discrepancy.
3. Along the same lines as comment #2, other possible "functions" of propionate and/or butyrate that could explain why treatment with them increase histone acetylation, propionylation, and butyrylation are not discussed. This work was not cited/discussed: PMID 34677127 despite being very closely related and relevant. Indeed, there seems to be some redundancy of efforts between that paper (2021) and this one even in terms of the specific experiments performed.
4. An analysis for correlations between the ChIP-seq data for H3K27bu (Fig 2) and RNA-seq data following butyrate treatment (Fig 3) would provide further insights into whether the genes/pathways that are enriched/downregulated in H3K27bu ChIP-seq data correlate with genes/pathways that are upregulated/downregulated in RNA-seq data.

Minor comments

1. All the images appear to be very low resolution. This could be due to the online submission system.
2. For Fig 2, the caption says "...treated with different SCFAs for 24 hours," but it is unclear precisely what the treatment was. Were the cells treated with the SCFA mix, and then ChIP-seq was performed for the 5 different marks tested? Or were there different SCFA treatments performed for each mark that was ChIPed?
3. Line 99-100: "Treatment with butyrate, propionate, or a mixture of all three SCFAs resulted in a global increase in histone butyrylation or propionylation" is misleading. The authors test only specific sites on Histone H3 using site-specific antibodies and do not test whether these treatments increase global levels of acylation on other histones and sites using pan-acyl antibodies. So, this sentence needs to be rephrased to clearly indicate that the treatments only increased at the tested sites.

Significance

Strengths and limitations: The experiments in the study were performed with a high degree of rigor, including appropriate controls. The discussion of the -seq data in Figs 2-4 avoided focusing on or following up on specific genes, which limited the conclusions from these data to being very broad. A key paper (that was not recent) was missing from the context presented in the paper, weakening the discussion of the data presented.

Advance: The advance is pretty conceptually incremental. Similar experiments as in Fig 1-3 in similar models have been performed in other papers already (e.g., PMID 39789354 in 2025 and PMID 34677127 in 2021), although Fig 4 was an interesting experiment that helps differentiate the work from existing literature.

Audience: This work would be interesting to a chromatin audience as well as a microbiome audience, but the scope of the conclusions from this paper, and it's redundancy with other literature, will limit its profile.

My expertise is in histone PTM biochemistry and biology, including non-canonical histone acyl PTMs.

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Referee #2

Evidence, reproducibility and clarity

This study presents a novel finding that short-chain fatty acids (SCFAs) produced by microbial metabolism regulate gene transcription in human colon cancer cells by modulating histone H3K9 and H3K27 butyrylation and propionylation, both of which are associated with an open chromatin state. The authors further reveal that the major effect of the SCFA mixture is driven by butyrate and identify p300/CBP-dependent, rather than HDAC inhibition-dependent, gene regulation by butyrate. Overall, this is a well-organized study that provides valuable insight into the role of metabolites in human cells.

Major comments:

1.In Figures 1C and 1D, why did the SCFA mixture not increase histone butyrylation or propionylation to the same level as single butyrate treatment? 2.In Figure 3B, how does butyrate block the effects of acetate and propionate on transcription? 3.Which pathways are associated with acetate- and propionate-specific DEGs? 4.Which genes are related to growth inhibition in butyrate-treated cells? Does the 1:1:1 SCFA mixture have a similar impact on cell growth as single butyrate treatment?

Significance

General assessment: This study clearly demonstrates the role of butyrate in gene regulation and elucidates its underlying regulatory mechanisms. However, it does not provide insight into how butyrate counteracts the effects of acetate and propionate, despite these metabolites often being detected together. In addition, it remains unclear which specific histone PTMs are associated with the distinct gene expression changes induced by different short-chain fatty acids. Lastly, the observation that histone butyrylation and propionylation correlate with active transcription is not novel.

Advance: This study advances understanding of short-chain fatty acids in chromatin and gene regulation, highlighting butyrate's dominant role and its p300/CBP-dependent rather than HDAC inhibition-dependent mechanism.

Audience: This work may attract significant interest in both the epigenetics and metabolism fields.

My expertise: histone acetylation, HATs, transcriptional regulation, cancer

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Kabir et al. explore the impact of microbiota-derived short-chain fatty acids (SCFAs) on chromatin structure and gene expression in human cells. They show that SCFAs, particularly butyrate, contribute to specific histone modifications such as butyrylation at H3K27, detectable in human colon tissue. Additional modifications like acetylation, butyrylation, and propionylation at H3K9 and H3K27 respond to SCFA levels and are enriched at active regulatory regions in colorectal cancer cells. Treatment with individual or combined SCFAs mimicking gut conditions alters gene expression patterns, with butyrate playing a dominant regulatory role. Butyrate's effects on gene expression are claimed to be independent of HDAC inhibition and instead rely on the p300/CBP complex through histone butyrylation. These findings underscore SCFAs as crucial modulators of epigenetic regulation in the human colon and highlight butyrate's dominant role in shaping chromatin and gene regulation beyond its known metabolic functions.

The authors used two human cell lines and an in vivo murine model paired with RNA and ChIP sequencing approaches to identify target genes and chromatin modifications in response to SCFAs. While the findings are interesting and could provide important insights into the epigenetic influence of SCFAs in human cells, the study would benefit from additional experiments to strengthen the conclusions. Comments and suggestions are listed below:

1. Figure 1: The H3K27bu expression in human biopsies highlights the clinical significance of the current study. However, the authors need to provide more information on the human colon samples, e.g., how many total patients were analyzed, and what were the age and/or sex. Only the methods mention the use of benign TMA; this should also be clarified in the figure legends. It would also be helpful to show histone butyrylation levels in normal vs. cancer human tissues.
2. Figure 1: In addition, given that the butyrate level descends towards the base of the colonic crypt (with the highest at the top of the crypt where mature intestinal epithelial cells reside) (Kaiko et al., 2016), it is important to show how the H3K27bu signature is distributed along the crypt. This data would further emphasize the clinical relevance of this study, given that most colorectal cancers (CRCs) arise from stem and progenitor cells.
3. Throughout the manuscript: The rationale for selecting the two CRC cell lines (HCT 116 and Caco2) should be explained. While commonly used, providing background on their genetic differences (e.g., driver mutations) is important, as this could greatly influence the PTM landscape.
4. The study lacks additional controls, such as a normal colon epithelial cell line and a non-colonic cell type. Including these would help determine whether the observed butyrate effects are tissue- or disease-specific. This data would also help assess whether SCFA effects, and specifically butyrate's effects, on histone acylation and gene expression are systemic or local.
5. Figure 2: The authors show ChIP-seq results in the HCT 116 cell line. To exclude the possibility that the demonstrated chromatin signatures are cell line-specific, results from Caco2 should also be shown. In addition, the 2D environment and multiple passaging alter gene expression in cell lines; using human colonic organoids would provide a more clinically and physiologically relevant model.
6. Figure 4 is very confusing. Entinostat itself, as an HDAC inhibitor (iHDAC), increases butyrylation. The data shown are insufficient to draw conclusions. First, the authors should use additional iHDACs, and second, they should illustrate the overlap in gene expression changes between all treatments using a Venn diagram to clarify which genes/signatures are specific to each treatment.
7. Figure 4: The authors use an HDAC inhibitor to rule out butyrate's effect on gene expression via HDAC inhibition. However, butyrate can also modulate gene expression through activation of GPR109a. Using GPR109a antagonists is necessary to address this possibility. These data are essential to validate the specific role of histone butyrylation in gene regulation.
8. Supplementary Figure 4 and manuscript: There is no in vivo methods section describing the tributyrin-gavaged mice. The authors should clarify how the experiment was performed, how cells were isolated, whether sorting was performed, and which markers were used.
9. Supplementary Figure 4: The GO analysis results show that lipid catabolism is among the top differentially enriched pathways. Butyrate is a known PPARγ agonist (Litvak et al., 2018), and activation of PPARγ is known to drive expression of genes involved in lipid metabolism. The authors need to rule out this function of butyrate before attributing this signature solely to histone butyrylation.
10. It would be helpful to include a table of differentially abundant genes as a supplement to the heatmaps and GO analysis.

Significance

This study explores how microbiota-derived SCFAs, particularly butyrate, influence histone acylation and gene regulation. While the topic is relevant, the work lacks important controls (e.g., normal epithelial and non-colonic cells) and omits mechanistic validation (e.g., GPR109a signaling, PPARγ involvement). The rationale for cell line selection is unclear, and in vivo methods are insufficiently described.

Audience:

The study will mainly interest specialists in microbiota-chromatin interaction. Broader impact is limited by the narrow model scope and underdeveloped mechanistic insight.

My Expertise:

Cancer biology, in vivo models, microbiota-host interactions.

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Reply to the reviewers

The authors do not wish to provide a response at this time.

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Referee #3

Evidence, reproducibility and clarity

In this report, Segal and coworkers describe the identification of the CD99 receptor as a marker whose expression discriminates betweeen two populations of a EWS tumor cell model, with distinct morphologies, behavior and xenograft tumor progression. As a top differentially expressed gene, they identify caveolin-1, a pervasive but highly contextual modulator of tumor cell behavior, as a potential driver of Pi3K/AKT-mediated thriving and survival.

Major conceptual comments:

The study uses state-of-the-art technology and their observations are potentially relevant to the field. However, the description of the mechanistic link between CAV1 and CD99 is not clear. The system they developed to stably manipulate CAV1 levels would be ideal to test the relevance of their claims in vivo. Certain additional experiments might clarify the dependency on caveolae or CAV1 (cholesterol/metabolic intervention). I am also intrigued by the proceedings they used to "evolve" CD99hi and CD99lo populations: mechanical stimuli can modulate caveolae assembly, and this should be addressed at least in one independent cell model, if not assessing whether primary tumors exhibit these diverging populations.

Major technical comments:

• the completeness of the "mechanical passaging" should be somehow demonstrated. Does this procedure progressively affect CD99 and CAV1 expression?

• To my understanding, knockdown assays are performed using only one shRNA sequence. this should be validated with at least one independent shRNA intervention, or a similar approach like CRISPr gene ablation

• The "aspect ratio" morphology score should be better explained and biologically contextualized (and if possible, correlated with Akt reporter signal) in the main figures

• Drug resistance assays should be better detailed, first in vitro and then in vivo

Significance

The study aims to identify contextual drivers of EWS tumor cells, and identify two potential molecules as associated with a proliferative/survival phenotype. As such, the aim of the study is important. However, the differential phenotypes investigated arise from a non-standard form of cell passaging in a single established cell line model, and no exploration on the link of their findings to actual human EWS disease is clearly explored. The proposed model of interdependence among the potential drivers found is neither clear at mechanistic level, limiting the potential of these findings to identify specific biomarkers and/or interventions. For publication, to the very least

(1) The mechanistic ties among the different drivers explored should be better characterized (also at technical level, see above) and

(2) the relevance of CAV1 KD in vivo should be shown. I strongly encourage the exploration of public data on EWS for the relevance of their findings, even if preliminary (i.e. expression levels associated with increased or decreased patient survival, for example).

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Referee #2

Evidence, reproducibility and clarity

Summary:

The submitted article identifies a distinct subpopulation of Ewing Sarcoma (EwS) cells characterized by high CD99 and elevated Caveolin-1 expression; shows that Caveolin-1 in these cells orchestrates PI3K/AKT signaling by specifically modulating the spatial organization of PI3K activity on the plasma membrane; demonstrates that the CD99-High and CD99-Low states are reversible, providing a flexible mechanism for survival-oriented plasticity in response to chemotherapy; and proposes that unlike CD99-Low cells,
 CD99-High cells use a Caveolin-1-driven signaling architecture to survive.

Mayor comments:

• The conclusion are well substantiated by the data and no additional experiments are needed to support the claims of the paper. Data and methods are presented in such a way that they can be reproduced. Experiments replicates and statistical analysis appear adequate.

Minor comments:

While the bibliography is appropriate, the manuscript should clarify its novelty from the outset. Specifically, the Introduction must acknowledge that the role of increased Akt activity in Cav-1-mediated cell survival is already established (Li et al., 2003). This study, currently listed as reference 42 in the Discussion, should be moved to the Introduction and discussed alongside references 31 and 32 to properly frame the study's context.

Regarding the role of caveolin-1 facilitating mechanosensitive Akt signaling, Sedding et al. (doi: 10.1161/01.RES.0000160610.61306.0f.) should be cited.

Likewise, Results: "Knockdown of Cav-1 in TC71 cells drastically reduced phosphorylated Akt levels in CD99Hi cells (Figure 5A), suggesting a dependence on Caveolin-1 for their Akt signaling". Rather than suggesting, these results are consistent with published data (Yang, H et al 2016; reference 32)

The nature of the CD99high state remains ill-defined. While the authors identify CD99 as a standard biomarker for Ewing Sarcoma (EwS) (Ref 38), they simultaneously suggest that this specific CD99high subpopulation may have been previously overlooked due to its sensitivity to conventional enzymatic dissociation. To avoid confusion, the authors should explicitly clarify the distinction between baseline CD99 expression and this highly sensitive, high-expression state.

Figure 4C. In addition to caveolae, CD99Hi, CD99Lo, and CD99Hi+Cav-1KD cells also present conspicuous differences in ER and ribosome content. These should be taken into account and the possibility be considered that the effect of Cav-1 may actually be caveolin-independent.

Significance

This manuscript adds further support to the role of caveolin-1 facilitating mechanosensitive Akt signaling, and establishes a novel link to CD99 expression in Ewing sarcoma.

These findings will be of interest for researchers across the fields of mechanobiology and preclinical oncology, particularly those investigating caveolar scaffolds and PI3K/Akt-driven malignancies.

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Referee #1

Evidence, reproducibility and clarity

This manuscript identified a subpopulation of Ewing sarcoma TC71 cells following mechanical passaging that express high levels of the CD99 marker. This CD99-hi TC71 population was shown by multiple in vitro and in vivo assays to be more aggressive than the CD99-lo population (Figures 1-3). The authors then show that Caveolin-1 is upregulated at the transcriptional level in CD99-hi cells and that these cells have caveolae, show that Cav1 expression in the CD99-hi cells reduced pAkt signaling and they propose that this affects survival of this cell population.

The strength of the paper is the very exhaustive in vitro and in vivo phenotypical analysis of the CD99-hi population (Figures 1-3).

There are however multiple important weaknesses and omissions in this paper:

1. The study is based on a single cell line, TC71, and conclusions are extended to Ewings sarcoma in general. Attributing conclusions generally to Ewings sarcoma must necessarily be based on analysis of multiple Ewings sarcoma cell lines and preferably supported by patient tumor data.

2. The statement that caveolin-1 is a molecular signature of the CD99-hi state is not supported by the Western blot in Supp fig 4E, that shows that CD99-hi cells have lower Cav1 levels than CD99-lo cells, even though the CD99-hi have caveolae. This must be explained mechanistically and functionally and it cannot be argued that caveolin-1 is a "molecular signature of the CD99-hi state" if caveolin-1 expression levels are reduced in the CD99-hi population.

3. The mechanistic role of caveolin-1 selectively in the CD99-hi population needs to be better established. Data supporting a role for Cav1 in survival is weak (Fig 4D) and not supported by the data presented in Supp fig 4G where Cav1 KD shows no effect on survival. A selective role for caveolin-1 in the CD99-hi cells must be demonstrated by parallel analysis of CD99-lo cells. Similarly ,the effects of caveolin-1 knockdown on AKT signaling are restricted to CD99-hi cells (Fig 5AB) and must be also shown for CD99-lo cells.

4. There is no data linking AKT signaling to the CD99-hi phenotype elaborately detailed in Figs 1-3. If as the authors claim " the CD99High state establishes a Caveolin-1-driven signaling architecture that supports tumor cell survival through mechanisms distinct from those used by CD99Low cells" then: 1. caveolin-1 dependent Akt signaling must be shown to be specific to CD99-hi and not CD99-lo cells; and 2. Akt signaling shown to selectively regulate survival of CD99-hi cells in a caveolin-1 dependent manner, based on the in vivo assays developed in figures 2 and 3.

Significance

The strength of the paper is the very exhaustive in vitro and in vivo phenotypical analysis of the CD99-hi population. There are however multiple important weaknesses and omissions in this paper which when addressed, could considerably improve the significance of the manuscripts findings for the community.

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Reply to the reviewers

We thank the Reviewers for their comments on our manuscript “Structural insights into mitotic-centrosome assembly”. As described below, we have substantially revised the manuscript in response to their comments and are hoping you would consider the revised manuscript “Phosphorylation relieves autoinhibition to drive Cnn centrosome scaffold assembly” at The EMBO Journal. Our specific responses (black text) to the Reviewer’s comments (blue text) are detailed below

Reviewer #1

Main Points:

1) From previous studies, it seems to me that for the residues potentially relevant for the hairpin regulation there is direct evidence of phosphorylation only for S567 (mass spec, phospho-antibody). Have the authors tested single site mutants (S567A and E)? Also, have they tested D mutations? If so, this should be commented on and shown. If not, it should be tested, in particular since the 2E phospho-mimetic is not functioning properly in vivo. If S571 is indeed crucial, it should be demonstrated that it is also phosphorylated. Otherwise it is possible that the mutation of this residue simply impairs important interactions (e.g. PReM-CM2, others), independent of phosphorylation.

As requested, we have now tested individual S567A and S571A mutations and found that they both perturb Cnn scaffold assembly, but to a lesser extent than the 2A double mutant (New Fig.S3A). We also now confirm by MS that recombinant Polo can phosphorylate both S567 and S571 in vitro, and we have examined the behaviour of a 2D mutant and find that it behaves very similarly to the 2E mutant (New Fig.S3B).

2) It is unclear why in vitro only A mutations have been tested and not phospho-mimetics. This should be tested for the interaction between PReM and CM2. This would allow to probe the model that phosphorylation opens the hairpin to allow interaction. Currently, such proof is missing in the study. Alternatively, the authors could phosphorylate the recombinant protein in vitro. The in vivo data is harder to interpret due to the complexity of the model and the authors should take advantage of the in vitro system.

As requested, we now show in New Fig.S5 that whereas in vitro WT Cnn490-608 and Cnn-2A490-608 behave as dimers, Cnn-2E490-608 elutes in two major fractions—a tetramer species and a much larger species that elutes in the void volume (meaning that 2E can form very large species even in the absence of CM2) (Figure S5A). In the presence of CM2, Cnn-2E490-608 forms a tetramer (that eluted slightly later than the Cnn-2E490-608 tetramer) and larger complexes that contained CM2 and eluted in the void volume with a profile similar to Cnn-2E490-608 on its own (Figure S5B). These results are consistent with the possibility that the 2E substitutions open the helical hairpin to allow self-interactions that drive homo-tetramer and larger complex assembly in vitro.

3) Regarding the worm PReM and CM2 domains, the authors mention that they have tested in vitro phosphorylation by PLK-1, but I could not find any data showing this. They should demonstrate successful phosphorylation or test candidate site by phospho-mimetic mutation. It is possible that the worm proteins depend more strongly on phosphorylation to relieve autoinhibition compared to the fly proteins.

This is a good point, and we apologise for this omission. We now state that we confirmed by MS analysis that the recombinant worm PLK-1 we used in these in vitro experiments phosphorylates the putative SPD-5 PReM domain on the three sites (S627, S653 and S658) known to be important for promoting SPD-5 scaffold assembly in vivo (Figure Legend, Figure 6). Thus, the lack of detectable binding between these proteins is not due to the lack of phosphorylation.

Minor Point:

4). Fig. 6C, D: the labeling of the chimeric constructs using "+" symbols is confusing, since it suggests that separate proteins were expressed. If I understand this correctly, with the current labeling, deltaCM2+DmCM2 means WT? The authors should write the full name of the wildtype or chimeric construct in each case and use a more standard/less confusing nomenclature. Also, I suggest to start the panels and graphs with the WT sample.

We thank the Reviewer for this suggestion and have re-labelled this Figure to clarify this point. We understand the point about putting the WT panels first in Figure 6C,D (now Figure 5C,D) but think that this is not the correct comparison to emphasise. We are testing the ability of the various CM2 domains to “rescue” the lack of a CM2 domain, so we feel Drosophila Cnn lacking CM2 is the correct baseline for this comparison.

Reviewer #2

Main Comments:

1. The title is too vague. Any number of existing papers could be said to provide "structural insights into mitotic centrosome assembly". The authors need to narrow down to a defined conclusion and state this as the title.
2. I think the strongest and most novel aspects of this study relate to the mechanism of Cnn assembly via relief of the auto-inhibited PReM. The effort to elucidate assembly mechanisms of SPD-5 and CDK5RAP2 are comparatively light and there are no accompanying experiments in worms or human cells. Without the in vivo experiments, it's hard to know if the in vitro experiments are valid. It's speculative for the authors to say they found the true PReM for CDK5RAP2; they do not demonstrate that PLK-1 phosphorylation potentiates assembly in Figure 8. Thus, I suggest re-writing the paper to focus on Cnn. Experiments in Figure 6 are still valid if reframed. For example, substituting Cnn's CM2 with the CM2 from CDK5RAP2 vs. the C-term of SPD-5 illustrates that a simple coiled-coil with open ends (H.s.CM2) is sufficient to interact with PReM whereas a coiled-coil with a closed end (SPD-5 C-term, predicted by Figure 6A) cannot. We thank the Reviewer for these helpful comments and have re-written and re-organised the manuscript in accord with these suggestions—most importantly providing a more specific title and re-ordering the data to better focus the paper on the relief of Cnn autoinhibition.

The purpose of Figure 1 is unclear. None of the other figures examine SPD-5 and CNN in the condensate form, which required using 4% PEG in this paper. The other assays look at the network form, which could behave differently and have different dependence on specific domains. I think they should perform the condensate assay for all other figures, otherwise leave it out. Furthermore, CDK5RAP2 is mentioned, yet not examined in Figure 1. It must be noted that CDK5RAP2 will also condense into droplets under crowding conditions or with a synthetic nucleator (Rios et al., 2025 J Cell Sci). Thus, it seems that condensation potential is a universal feature of known PCM scaffold proteins.

The original Figure 1 has been moved to end of the paper (now Figure 8) and we now more thoroughly explain the logic of these experiments. Briefly, given that the PReM and CM2 domains in flies and worms seem to function in different ways in vivo, we sought here to test whether this was also the case in vitro—where the behaviour of full-length SPD-5 and of these domains of Cnn have been extensively studied, but never directly compared. We believe such a direct comparison will be of some interest to the field (the Woodruff et al., 2017 paper describing these in vitro SPD-5 condensates has been cited >700 times). We now also cite the Rios et al., 2025 paper but note that, despite extensive efforts, we were unable to purify enough well-behaved CDK5RAP2 for our experiments and so could not include it in this analysis. We think Rios et al., used an MBP-fusion of CDK5RAP2 in their experiments, which may explain this difference.

The study uses different species without doing the same types of experiments on each. Sometimes human CDK5RAP2 is thrown in, sometimes not. They solve crystal structures of PReM from Cnn but not from the other proteins. This gets confusing, especially since the authors state that they seek to test if fly Cnn and worm SPD-5 assemble through different mechanisms (see last sentence of the intro). Also, if the focus is on worm vs. fly PCM assembly mechanisms, why include the human protein, especially Figure 8?

On re-reading our original manuscript we appreciate this confusion. We hope that in re-writing the manuscript along the lines suggested by the Reviewer the logical flow of our experiments will be clearer.

The conclusion that SPD-5's narrow PReM and "CM2" domains don't interact is consistent with the cross-linking mass spectrometry data from Rios et al. 2024. They showed only one X-link with low occurrence (1 out of 6 samples) between these two regions, even in the phosphorylated state (Fig. 1G). However, Nakajo et al (2022) claimed the opposite, showing that a larger PReM-containing construct (a.a. 272-732) interacts with a C-terminal construct (a.a. 1061-1198) after PLK-1 phosphorylation. Can the authors comment on this? Perhaps there is another site in SPD-5, outside of a.a. 541-677, that acts like the Cnn PReM?

These are good points and we now mention this last possibility in the Discussion. We also now mention the supporting cross-linking Mass Spec data from Rios et al., 2024.

I have serious doubts that the C-terminus of SPD-5 has a CM2 domain. To me, there is no real sequence homology with the traditional CM2's from humans and flies, and the AF3 predictions support this. Ohta et al. (2021) called this region "CM2-like" based on very poor homology, which a is questionable practice. Any coiled-coil region will appear somewhat homologous due to the heptad repeat pattern that defines them (e.g., leucines line up quite nicely). Thus, is it fair to say that SPD-5 doesn't assemble through a PReM-CM2 interaction? There may be a different region in SPD-5 that looks more like the canonical CM2. I think the authors have compelling evidence to give the C-terminal coiled-coil region in SPD-5 its own name rather than calling it CM2.

This is a fair point, although the literature is already quite confusing on the nomenclature for the C-terminal region of SPD-5 (e.g., Ohta et al., JCB, 2021; Nakajo et al., JCS, 2022), so we are reluctant to add another name to the mix. Given that we draw comparisons with the fly and human CM2 domains (that are clearly related by sequence), we think it is easiest for readers if we use the “CM2” nomenclature throughout, although making clear our conclusion that SPD-5 “CM2” does not appear to function in the same way as fly/human CM2.

Figure 3E. Would measuring scaffold mass be more appropriate? The PReM(deltaH1,NTH2) leads to more compact scaffolds, but maybe they assemble just as well as the deltaH1 mutant. As it stands, there is a discrepancy between panel E and F in terms of what is measured (area vs. intensity) and the outcome.

In several previous papers we use fluorescence intensity to measure the “amount” of protein at centrosomes in vivo but, in our original paper (Feng et al., Cell, 2017), we quantified PReM::CM2 scaffold assembly in vitro by measuring the area of scaffold assembly. Thus, we prefer to present the current data in this way for consistency across publications, and we believe either measure is valid. We could measure the area and intensity of the PReM∆H1 and PReM∆H1∆NTH2 scaffolds to compare scaffold density, but we think this would unnecessarily complicate this data. The main point is not how much or how dense each scaffold is, but rather that the PReM∆H1∆NTH2 protein doesn’t really make a scaffold at all—but rather makes smaller “blobs” that tend to bunch together (further characterised in Fig.S2).

Minor Comments:

1. In one version of the PDF there are images missing in Fig 1F, 4C, 4D. I opened another version (source version) and the images were there. Just FYI.
2. Figure 4A. The blue coloration makes it difficult to read the black letters.
3. Figure 4A. Why is part of the protein colored in green? This coloration isn't defined, nor does it show up again in panel B.
4. The layout of Figure 4 is confusing. It took me a few minutes to realize that the big red box inset belonged to panel B and not panel A.
5. Figure 4C,D. The sample size is not mentioned in the legend.
6. The title for Figure 4 seems too speculative. How can the authors say that phosphorylation relieves the autoinhibition without structural data?
7. Figure 5B. The sample size is not mentioned in the legend.
8. Figure 6B,D. The sample size is not mentioned in the legend.
9. The text in Figure 7B is hard to read because it is too small. Please make this bigger.
10. Figure 8C. What is colored in magenta? Is there an additional labeled protein besides mNG-CM2?
11. Figure 8C. What is the sample size? How many images were taken? Also, why are there data points off to the right of the last column?
12. The wording of these sections needs improving. I found them complicated and difficult to understand. We thank the Reviewer for taking the time to make these helpful comments. We have addressed all these points in the revised manuscript. On point 10, the magenta objects were fiduciary beads that were inadvertently included on this panel (and are no longer shown).

Reviewer #3

Major Comments: 1. The title, "Structural Insights into Mitotic-Centrosome Assembly," is overly broad. The study primarily focuses on CM2-PReM intramolecular interactions in D. melanogaster Cnn and does not comprehensively address mitotic centrosome assembly across species. A more specific title reflecting the fly-centric and structural focus would better align with the manuscript's scope and conclusions.

As described at the start of our response to Reviewer #2, the title and focus of the manuscript have been extensively revised along these lines.

The authors analyze condensate formation by Cnn and SPD-5 but overlook condensate formation by CDK5RAP2, which was recently reported by Rios et al. (2025, PMID: 40454523). Including CDK5RAP2 would enable a more balanced and informative comparison across fly, worm, and human homologs.

As described in point 3 of our response to Reviewer #2, we now cite Rios et al., 2025 but note that, despite extensive efforts, we were unable to purify enough well-behaved CDK5RAP2 for our experiments and so could not include it in this analysis. We believe Rios et al., used a full-length MBP-fusion of CDK5RAP2 in their experiments, which may explain this difference as MBP is very good at keeping proteins soluble (but would not be appropriate in our experiments where we compare full-length untagged proteins).

In Figure 3, reconstitution of Cnn scaffolds using purified CM2 and PReM fragments yields "macromolecular scaffolds," but their physical properties are not defined. It remains unclear whether these assemblies are ordered or amorphous, and whether they exhibit solid- or gel-like behavior. Moreover, the heterogeneous, scattering particles observed by negative-stain EM (Figure S3B), likely corresponding to the Cnn490-608-CM2 complex, raise the possibility of nonspecific aggregation rather than organized scaffold formation. Appropriate controls lacking CM2 are needed to exclude spontaneous aggregation of PReM fragments. In addition, testing shorter truncations of the PReM H2 helix could help define the minimal requirements for scaffold assembly. Finally, the rationale for including the CnnΔExPReM construct only in vivo (Figure 3F), but not in the in vitro assays (Figure 3A-E), should be clarified.

We apologise, as our presentation of this data has clearly led to some confusion on these points.

First, as we now clarify, the amorphous solid-like physical properties of the PReM::CM2 scaffolds were described in our previous paper where we also showed that these scaffolds are not simply non-specific aggregates—as several single point mutations that disrupt the LZ::CM2 tetramer also prevent PReM::CM2 scaffold assembly in vitro as well as Cnn scaffold assembly in vivo (see Fig.5, Feng et al., Cell, 2017). Also, in all in vitro scaffolding experiments we always perform a negative control (-CM2) to confirm that none of the scaffolds are aggregates of the PReM domain being tested. We don’t usually show this control now as there would be lots of empty black boxes on the Figures. We do, however, show this control for the human putative PReM domain (Figure 7C), as we are testing this here for the first time.

Second, the request to test shorter truncations of the PReM H2 helix to define the minimal requirements for scaffold assembly is unnecessary as PReM∆H1∆NTH2 already cuts H2 at the start of the LZ, and we previously showed the LZ is required for PReM::CM2 scaffold assembly in vitro (Feng et al., Cell, 2017). Thus, any further truncation of H2 will start to remove the LZ, which we already know is essential. We have now made this point more clearly.

Finally, the Cnn∆ExPReM construct the Reviewer mentions was tested in both the in vitro (now Figure 2B) and in vivo (now Figure 2F) assays, but the labelling was confusing so this was not clear. We have now clarified this point.

The coarse-grained (CG) simulation methodology is insufficiently described. Given that CG approaches sacrifice atomic detail and may oversimplify interactions, readers require more information to evaluate the model's reliability and limitations. A comparison with the framework used by Ramirez et al. (2024, PMID: 38356260) would be informative. It is also unclear why available crystal structures of WT and 2A Cnn (Figure 2C; Figure S4) were not used as simulation inputs, or why the structure of Cnn490-579 2E was not determined to complete the structural comparison.Furthermore, mutation of Ser567 and Ser571 to alanine markedly stabilizes the PReM domain (Figure 5C, D), implying that these residues maintain domain flexibility. Back-mapping CG models to atomic resolution could reveal the interactions altered by these mutations. The exclusive focus on double mutants (2A and 2E) is also limiting; analysis of single-point mutants at S567 or S571 would clarify whether both residues contribute equally or play distinct roles.

We performed coarse-grained simulations because although they simplify atomic interactions and capture overall conformational dynamics, which is what we are trying to assess here (Fig.4C,D). We now clarify this point and provide more detail of our simulation methodology in the main text and Materials and Methods. We used the full helical hairpin (i.e., H2+H3+H4) prediction in these simulations—rather than the crystal structure of the partial helical hairpin (i.e., H2+most of H3)—as we reasoned that the presence of the full H3 and H4 might influence breathing, and the full helical hairpin (see Video S1) seems likely to be the relevant biological fold. As we now show (new Figure S5), and as discussed above, the 2E mutants do not behave well in vitro so we were unable to solve their structure. We agree that we could perform atomic resolution simulations to better understand how the 2A/E and single A/E mutations might suppress/enhance breathing, but we believe such an analysis is beyond the scope of the current manuscript and would distract from our main conclusions.

The discussion lacks sufficient integration with prior studies and often presents conclusions without adequate citation. For example, the claim that flies and humans rely on related PReM-CM2 interactions whereas worms use distinct phosphorylation-regulated mechanisms is not supported by appropriate references. In addition, limited cross-referencing to the manuscript's own data weakens the connection between results and conclusions. Expanding and better grounding the discussion in existing literature would significantly enhance its depth and clarity. We thank the Reviewer for this general point and have tried to better integrate our results with prior studies—particularly in the Discussion section.

Minor Comments: 1. In Figure 1B, the molecular weight units for the protein marker are missing and should be included. Fixed.

In Figures 1E and 1F, readability would be improved by including x-axis labels on all graphs, rather than only on the bottom panels.Fixed. The protein structures shown in Figures 2C and 2D sh7w b b∫ybb ould be explicitly labeled as dimers to avoid confusion. Fixed. In Figures 3A-D, using fluorescently labeled CM2 would help validate both the interaction with the PReM domain and its localization within the scaffold.We have previously tried fluorescently tagging the CM2 domain, but scaffold formation is much less robust. We do not think this invalidates this assay, as the evidence supporting the PReM::CM2 interaction is very strong—including assessing the physiological influence of multiple point mutations in both domains in residues at the heart of the interaction interface identified by crystallography (e.g., see Fig.4, Feng et al., Cell, 2017).

In Figure 3E, no statistical comparisons are presented between the original PReM construct and other samples. In addition, information regarding sample size and the number of experimental replicates is missing from the figure legend. Fixed. In Figure 3F, the absence of a pixel intensity scale bar makes the data difficult to interpret, as color values corresponding to high and low signal intensities are unclear. Moreover, no additional centrosome marker is included, nor is there evidence that PReM fragment expression levels are comparable across samples. These concerns also apply to Figures 4C and 4D.We now include pixel intensity scales in all relevant Figures. We think we do not need to show additional centrosome markers in our images as centrosomes exhibit a very reproducible behaviour in these embryos so we can be very confident that the objects we show here are genuine centrosomes. Considering expression levels, the images in Fig.4C,D (now 3C,D) are derived from stable transgenic lines so we can measure protein expression levels and show that the 2A and 2E mutants are expressed at similar levels to WT (new Figure S6). The images in 2F are from mRNA injections, so cannot be quantified in this way. However, we have vast experience with this assay (used in >15 publications since 2014) and can tell when, very occasionally, an injected mRNA is not expressed well (as this leads to a lack of general fluorescence in the cytoplasm). In addition, we know that deletions in Cnn do not generally destabilise the protein as we have analysed many such transgenic lines (see, for example, Reviewer Figure 1). Thus, the differences in centrosomal levels observed and quantified in 2F are almost certainly not caused by differences in the stability of the proteins being generated from the injected mRNAs.

In Figure 4A, the interacting residues of PReM and CM2 shown in the red inset would be clearer if residue annotations for each domain were displayed in distinct colors. Additionally, the legends for Figures 4C and 4D do not specify the scale bar length.Fixed. The authors state that interactions between CM2 and PReM-2A462-608 could not be detected in vitro based on SEC chromatograms (Figure 5A), yet the figure does not clearly show this result. The accompanying SDS-PAGE images are too small and lack lane labels, making interpretation difficult (a similar issue applies to Figure 7B). Furthermore, the SEC chromatogram x-axis lacks volume annotations, hindering correlation between chromatographic peaks and SDS-PAGE results (in contrast to Figure 7B, which provides an appropriate example).We thank the reviewer for these points, all of which have now been fixed/adjusted.

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Referee #3

Evidence, reproducibility and clarity

This study by Mohamad et al. builds on prior work by Conduit et al. (2014, PMID: 24656740) and Feng et al. (2017, PMID: 28575671), which established the essential role of intramolecular interactions between the phospho-regulated multimerization (PReM) domain and centrosomin motif 2 (CM2) of Drosophila Cnn in pericentriolar matrix (PCM) expansion during mitosis. Extending these studies, the authors investigate the structural properties of Cnn's PReM and CM2 domains and compare them with homologous proteins in C. elegans (SPD-5) and humans (CDK5RAP2). Their analyses suggest a phosphorylation-dependent mechanism that relieves Cnn autoinhibition, with particular emphasis on Ser567 and Ser571 within the PReM domain. The authors further propose that, whereas Cnn and CDK5RAP2 share conserved CM2-PReM interactions, SPD-5 has diverged to employ distinct mechanisms for PCM scaffold assembly.

Although these conclusions rely heavily on AlphaFold3-predicted models (Abramson et al., 2024, PMID: 38718835), they are supported by a combination of in vitro and in vivo experiments, including live-cell imaging and molecular dynamics simulations. However, inconsistencies between in vitro and in vivo observations weaken some interpretations and warrant more careful discussion. Addressing the concerns below would substantially strengthen the manuscript.

Major Comments

1. The title, "Structural Insights into Mitotic-Centrosome Assembly," is overly broad. The study primarily focuses on CM2-PReM intramolecular interactions in D. melanogaster Cnn and does not comprehensively address mitotic centrosome assembly across species. A more specific title reflecting the fly-centric and structural focus would better align with the manuscript's scope and conclusions.
2. The authors analyze condensate formation by Cnn and SPD-5 but overlook condensate formation by CDK5RAP2, which was recently reported by Rios et al. (2025, PMID: 40454523). Including CDK5RAP2 would enable a more balanced and informative comparison across fly, worm, and human homologs.
3. In Figure 3, reconstitution of Cnn scaffolds using purified CM2 and PReM fragments yields "macromolecular scaffolds," but their physical properties are not defined. It remains unclear whether these assemblies are ordered or amorphous, and whether they exhibit solid- or gel-like behavior. Moreover, the heterogeneous, scattering particles observed by negative-stain EM (Figure S3B), likely corresponding to the Cnn490-608-CM2 complex, raise the possibility of nonspecific aggregation rather than organized scaffold formation. Appropriate controls lacking CM2 are needed to exclude spontaneous aggregation of PReM fragments. In addition, testing shorter truncations of the PReM H2 helix could help define the minimal requirements for scaffold assembly. Finally, the rationale for including the CnnΔExPReM construct only in vivo (Figure 3F), but not in the in vitro assays (Figure 3A-E), should be clarified.
4. The coarse-grained (CG) simulation methodology is insufficiently described. Given that CG approaches sacrifice atomic detail and may oversimplify interactions, readers require more information to evaluate the model's reliability and limitations. A comparison with the framework used by Ramirez et al. (2024, PMID: 38356260) would be informative. It is also unclear why available crystal structures of WT and 2A Cnn (Figure 2C; Figure S4) were not used as simulation inputs, or why the structure of Cnn490-579 2E was not determined to complete the structural comparison.

Furthermore, mutation of Ser567 and Ser571 to alanine markedly stabilizes the PReM domain (Figure 5C, D), implying that these residues maintain domain flexibility. Back-mapping CG models to atomic resolution could reveal the interactions altered by these mutations. The exclusive focus on double mutants (2A and 2E) is also limiting; analysis of single-point mutants at S567 or S571 would clarify whether both residues contribute equally or play distinct roles. 5. The discussion lacks sufficient integration with prior studies and often presents conclusions without adequate citation. For example, the claim that flies and humans rely on related PReM-CM2 interactions whereas worms use distinct phosphorylation-regulated mechanisms is not supported by appropriate references. In addition, limited cross-referencing to the manuscript's own data weakens the connection between results and conclusions. Expanding and better grounding the discussion in existing literature would significantly enhance its depth and clarity.

Minor Comments

1. In Figure 1B, the molecular weight units for the protein marker are missing and should be included.
2. In Figures 1E and 1F, readability would be improved by including x-axis labels on all graphs, rather than only on the bottom panels.
3. The protein structures shown in Figures 2C and 2D should be explicitly labeled as dimers to avoid confusion.
4. In Figures 3A-D, using fluorescently labeled CM2 would help validate both the interaction with the PReM domain and its localization within the scaffold.
5. In Figure 3E, no statistical comparisons are presented between the original PReM construct and other samples. In addition, information regarding sample size and the number of experimental replicates is missing from the figure legend.
6. In Figure 3F, the absence of a pixel intensity scale bar makes the data difficult to interpret, as color values corresponding to high and low signal intensities are unclear. Moreover, no additional centrosome marker is included, nor is there evidence that PReM fragment expression levels are comparable across samples. These concerns also apply to Figures 4C and 4D.
7. In Figure 4A, the interacting residues of PReM and CM2 shown in the red inset would be clearer if residue annotations for each domain were displayed in distinct colors. Additionally, the legends for Figures 4C and 4D do not specify the scale bar length.
8. The authors state that interactions between CM2 and PReM-2A462-608 could not be detected in vitro based on SEC chromatograms (Figure 5A), yet the figure does not clearly show this result. The accompanying SDS-PAGE images are too small and lack lane labels, making interpretation difficult (a similar issue applies to Figure 7B). Furthermore, the SEC chromatogram x-axis lacks volume annotations, hindering correlation between chromatographic peaks and SDS-PAGE results (in contrast to Figure 7B, which provides an appropriate example).

Significance

This work will be of interest not only to cell biologists studying centrosomes, but also to molecular biologists investigating how protein modifications regulate protein behavior.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Mohamed et al. set out to compare the assembly mechanisms of pericentriolar material (PCM) in flies and nematodes. They reveal that the main PCM scaffold protein in each species (Cnn in flies, SPD-5 in nematodes) are sufficient to form supramolecular droplets (with a crowding agent) or networks (without a crowding agent). However, they diverge in one key aspect: Cnn scaffold assembly relies on the interaction between a C-terminal CM2 domain and a central phospho-regulated domain (PReM), whereas SPD-5 does not. The authors solve the crystal structure of a region within Cnn's PReM. With the help of modeling, they speculate that this region is auto-inhibited through backfolding of alpha helices, thus preventing its interaction with the CM2 domain. This auto-inhibition would be relieved by phosphorylation, which modeling suggests would increase "breathing" of the backfolded structure. The author end by presenting evidence to suggest that the human PCM scaffold protein CDK5RAP2 may assemble through a PReM-CM2 interaction.

Major Comments:

1. The title is too vague. Any number of existing papers could be said to provide "structural insights into mitotic centrosome assembly". The authors need to narrow down to a defined conclusion and state this as the title.
2. I think the strongest and most novel aspects of this study relate to the mechanism of Cnn assembly via relief of the auto-inhibited PReM. The effort to elucidate assembly mechanisms of SPD-5 and CDK5RAP2 are comparatively light and there are no accompanying experiments in worms or human cells. Without the in vivo experiments, it's hard to know if the in vitro experiments are valid. It's speculative for the authors to say they found the true PReM for CDK5RAP2; they do not demonstrate that PLK-1 phosphorylation potentiates assembly in Figure 8. Thus, I suggest re-writing the paper to focus on Cnn. Experiments in Figure 6 are still valid if reframed. For example, substituting Cnn's CM2 with the CM2 from CDK5RAP2 vs. the C-term of SPD-5 illustrates that a simple coiled-coil with open ends (H.s.CM2) is sufficient to interact with PReM whereas a coiled-coil with a closed end (SPD-5 C-term, predicted by Figure 6A) cannot.
3. The purpose of Figure 1 is unclear. None of the other figures examine SPD-5 and CNN in the condensate form, which required using 4% PEG in this paper. The other assays look at the network form, which could behave differently and have different dependence on specific domains. I think they should perform the condensate assay for all other figures, otherwise leave it out. Furthermore, CDK5RAP2 is mentioned, yet not examined in Figure 1. It must be noted that CDK5RAP2 will also condense into droplets under crowding conditions or with a synthetic nucleator (Rios et al., 2025 J Cell Sci). Thus, it seems that condensation potential is a universal feature of known PCM scaffold proteins.
4. The study uses different species without doing the same types of experiments on each. Sometimes human CDK5RAP2 is thrown in, sometimes not. They solve crystal structures of PReM from Cnn but not from the other proteins. This gets confusing, especially since the authors state that they seek to test if fly Cnn and worm SPD-5 assemble through different mechanisms (see last sentence of the intro). Also, if the focus is on worm vs. fly PCM assembly mechanisms, why include the human protein, especially Figure 8?
5. The conclusion that SPD-5's narrow PReM and "CM2" domains don't interact is consistent with the cross-linking mass spectrometry data from Rios et al. 2024. They showed only one X-link with low occurrence (1 out of 6 samples) between these two regions, even in the phosphorylated state (Fig. 1G). However, Nakajo et al (2022) claimed the opposite, showing that a larger PReM-containing construct (a.a. 272-732) interacts with a C-terminal construct (a.a. 1061-1198) after PLK-1 phosphorylation. Can the authors comment on this? Perhaps there is another site in SPD-5, outside of a.a. 541-677, that acts like the Cnn PReM?
6. I have serious doubts that the C-terminus of SPD-5 has a CM2 domain. To me, there is no real sequence homology with the traditional CM2's from humans and flies, and the AF3 predictions support this. Ohta et al. (2021) called this region "CM2-like" based on very poor homology, which a is questionable practice. Any coiled-coil region will appear somewhat homologous due to the heptad repeat pattern that defines them (e.g., leucines line up quite nicely). Thus, is it fair to say that SPD-5 doesn't assemble through a PReM-CM2 interaction? There may be a different region in SPD-5 that looks more like the canonical CM2. I think the authors have compelling evidence to give the C-terminal coiled-coil region in SPD-5 its own name rather than calling it CM2.
7. Figure 3E. Would measuring scaffold mass be more appropriate? The PReM(deltaH1,NTH2) leads to more compact scaffolds, but maybe they assemble just as well as the deltaH1 mutant. As it stands, there is a discrepancy between panel E and F in terms of what is measured (area vs. intensity) and the outcome.

Minor Comments

1. In one version of the PDF there are images missing in Fig 1F, 4C, 4D. I opened another version (source version) and the images were there. Just FYI.
2. Figure 4A. The blue coloration makes it difficult to read the black letters.
3. Figure 4A. Why is part of the protein colored in green? This coloration isn't defined, nor does it show up again in panel B.
4. The layout of Figure 4 is confusing. It took me a few minutes to realize that the big red box inset belonged to panel B and not panel A.
5. Figure 4C,D. The sample size is not mentioned in the legend.
6. The title for Figure 4 seems too speculative. How can the authors say that phosphorylation relieves the autoinhibition without structural data?
7. Figure 5B. The sample size is not mentioned in the legend.
8. Figure 6B,D. The sample size is not mentioned in the legend.
9. The text in Figure 7B is hard to read because it is too small. Please make this bigger.
10. Figure 8C. What is colored in magenta? Is there an additional labeled protein besides mNG-CM2?
11. Figure 8C. What is the sample size? How many images were taken? Also, why are there data points off to the right of the last column?
12. The wording of these sections needs improving. I found them complicated and difficult to understand.

"Fly and worm Spd-2/SPD-2 and Polo/PLK-1 are clear homologues, but Cnn and SPD-5 share little sequence homology-although they are both predicted to be large coiled-coil-rich proteins. Thus, it remains unclear whether these two, largely unrelated, molecules form mitotic-PCM scaffolds that assemble and function in a similar manner"

"We first focused on Drosophila Cnn as, although the full structure of the original PReM domain (Cnn403-608) is unknown, this domain contains an internal leucine-zipper (LZ) dimer (Cnn490-544) whose crystal structure, in a tetrameric complex with a CM2 dimer, had been solved (Figure 2A) (Feng et al., 2017)."

"When the full PReM and CM2 domains are mixed in vitro, they form large micron-scale assemblies and point mutations that perturb the LZ::CM2 tetramer perturb PReM::CM2 scaffold assembly in vitro and Cnn scaffold assembly in vivo."

Significance

Overall Assessment:

While I find the premise of this study to be interesting, its execution and presentation are not fully convincing. The study is a collection of experiments connected by a thread that can be difficult to follow. One concern is the lack of focus and a clearly stated conclusion, which is ultimately embodied by the vague title. For example, the research question at the beginning doesn't match with the outcome in the end. At the end of the introduction, the authors state they wish to compare assembly mechanisms of Cnn and SPD-5. However, at the end of the results, they present data on CDK5RAP2 and speculate on its assembly. Why introduce the human protein here? Another concern is the lack of symmetry in the experiments. There is much more in vitro characterization of Cnn than SPD-5 or CDK5RAP2, and all in vivo work is performed in flies. Finally, this study does not address if the best-established model for SPD-5 assembly-multimerization via specific, multivalent coiled-coil interactions-applies to fly Cnn. Thus, to me, this is study is a deeper dive into the mechanism of Cnn assembly, not necessarily a fair cross-species comparison. I do not have major issues with the results, but I recommend that this paper undergo significant re-writing before being re-reviewed. There are also issues with data display and reporting of experimental details (e.g., sample sizes) that should be easily fixed.

Advance: this study provides new insight into how two specific domains interact within PCM scaffold proteins to promote scaffold assembly. It provides some new structural insight into the mechanism of Cnn auto-inhibition. However, there is limited conceptual advance, as the bigger ideas (e.g., auto-inhibition as a regulatory control, PCM scaffold assembly through condensation of coiled-coil proteins) were already established.

Audience: this study will be of interest to cell biologists studying centrosome assembly, mitosis, and evolution.

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Referee #1

Evidence, reproducibility and clarity

The study by Mohamad et al. investigates the structural basis and regulatory role of phosphorylation in the assembly of the mitotic pericentriolar material (PCM) scaffold, which nucleates microtubules and organizes the poles of the mitotic spindle. They use structure determination, biochemical reconstitution and in vivo experiment in flies to address how fly, worm, and human homologs of a key scaffold protein (Cnn, SPD-5, and CDK5RAP2, respectively) are relieved from auto-inhibition in a phosphorylation-dependent manner to form extended scaffolds through interactions between PReM and CM2 domains. An important discovery is a helical hairpin structure in the PReM domain that is the basis of autoinhibition and is regulated by phosphorylation. The work addresses the fundamental question how the centrosome matures in preparation for mitosis, by increasing the size and activity of the PCM scaffold that surrounds the centrioles. It also addresses how conserved the underlying molecular mechanism are among flies, worms, and humans. The study is overall of high quality, building on previous works by the authors and other groups, and adding new structural and biochemical insight. Most of the conclusions are supported by the data. I have a few concerns though that should be addressed. An important issue is the analysis of phosphorylation sites, which appears incomplete. For example, it lacks demonstration that both of the two studied phosphorylation sites are indeed phosphorylated. Kinase motif identification and mutation is not sufficient, considering that phosphorylation is integral to the proposed model of how autoinhibitory intra-molecule interactions are relieved, and considering that phospho-mimetics have not been tested in vitro and function poorly in vivo.

Main:

1) From previous studies, it seems to me that for the residues potentially relevant for the hairpin regulation there is direct evidence of phosphorylation only for S567 (mass spec, phospho-antibody). Have the authors tested single site mutants (S567A and E)? Also, have they tested D mutations? If so, this should be commented on and shown. If not, it should be tested, in particular since the 2E phospho-mimetic is not functioning properly in vivo. If S571 is indeed crucial, it should be demonstrated that it is also phosphorylated. Otherwise it is possible that the mutation of this residue simply impairs important interactions (e.g. PReM-CM2, others), independent of phosphorylation.

2) It is unclear why in vitro only A mutations have been tested and not phospho-mimetics. This should be tested for the interaction between PReM and CM2. This would allow to probe the model that phosphorylation opens the hairpin to allow interaction. Currently, such proof is missing in the study. Alternatively, the authors could phosphorylate the recombinant protein in vitro. The in vivo data is harder to interpret due to the complexity of the model and the authors should take advantage of the in vitro system.

3) Regarding the worm PReM and CM2 domains, the authors mention that they have tested in vitro phosphorylation by PLK-1, but I could not find any data showing this. They should demonstrate successful phosphorylation or test candidate site by phospho-mimetic mutation. It is possible that the worm proteins depend more strongly on phosphorylation to relieve autoinhibition compared to the fly proteins.

Minor:

4). Fig. 6C, D: the labeling of the chimeric constructs using "+" symbols is confusing, since it suggests that separate proteins were expressed. If I understand this correctly, with the current labeling, deltaCM2+DmCM2 means WT? The authors should write the full name of the wildtype or chimeric construct in each case and use a more standard/less confusing nomenclature. Also, I suggest to start the panels and graphs with the WT sample.

Significance

The study's strength is the use of a combination of structural and biochemical approaches with in vivo model testing. Its main limitation is that the analyses of the role of phosphorylation lacks depth and is not fully conclusive, despite its importance for centrosomal scaffold assembly. The study advances our understanding of centrosomal scaffold assembly and maturation at a molecular level, and how specific molecular aspects of these processes are conserved or differ among different organisms. The findings are of interest to cell biologists. My expertise is in centrosome and microtubule biology.

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Reply to the reviewers

_Overall, we were encouraged by the comments of the reviewers, who mostly agreed that the study advance our understanding of two component system signaling mechanisms. The most substantive critique raised was the lack of mechanistic insight into the specific binding sites of Cu and NO on the PdtaS protein and the lack of examination of additional ligands such as cyclic di-GMP and zinc. We agree with this critique and cannot, and did not, make specific statements about the location of ligand binding. However, w_e draw a clear distinction in the manuscript between the functional effects of a chemical entity (ligand) on kinase activity and knowledge of the precise binding site of that ligand on the protein. As acknowledged, we did not determine the binding site. However, we do demonstrate the functional effect of the ligands, and these effects cannot occur without physical interaction between the ligand and the protein, so we believe the statement that the ligands are having this effect through binding is accurate, without knowledge of the precise location of that binding. ____

Reviewer 1:

• The primary concern pertains to ligand recognition by PdtaS. While PdtaS constitutive autophosphorylation is shown to be dependent on dimerization, there is no direct evidence of ligand binding. How Cu and NO inhibits PdtaS activity remains uncharacterized. Is it unclear if there are specific binding pockets inducing PdtaS conformational switch, if both substrates compete for a single binding pocket, or if Cu and NO inhibit dimerization by binding to the dimer interface. Similarly, it is unclear if NO does not covalently modify the key cysteine residues by S-nitrosylation, nor if Cu induces a distinct and reversible thiol-switch by site-specific oxidation that regulates PdtaS dimerization and activity.

• __Response: Our discussion already contained this sentence: "Although we identify mutations with both positive and negative effects on dimer affinity which have effects of ligand inhibition of the kinase, this data does not identify specific molecular details on how dimerization is inhibited and whether Cu and NO both interact with the same regions of the dimer interface." We have added a sentence acknowledging that we do not determine whether NO is covalently modifying a thiol (line 343). __

• Given the focus on ligand effects on PdtaS dimerization and activity, zinc and c-di-GMP should also be considered, as prior studies have suggested they may be sensed by PdtaS. Similarly, given the claim of multiligand sensing, it would be valuable to examine the combined effects of NO and Cu. Do they act additively, synergistically, or interfere with each other?

• Response: We have added data to the manuscript examining the effect of c-di-GMP on kinase activity in combination with Cu. We do not observe a substantial synergistic effect. This new data is now Figure S3.

• PdtaS variants and mutants are neither introduced nor adequately described. For example, in lines 144-150, PdtaS-H303Q and G443 are mentioned without citation, and their construction is not described in the Materials and Methods section. As a result, it is difficult to determine which experiments and constructs are specific to this manuscript. Please provide a detailed Materials and Methods section, and include as supplementary material a complete list of all strains, primers, and constructs used in this study, along with their origins.

• __Response: We have added a section to the methods detailing the construction of the PdtaS mutant protein expression plasmids. __

• References: Xing J et al 2023 is duplicated. Please correct in the text and in the references list.

• Response: We have deleted the duplicate reference

• Please provide molecular weights on gels (fig. 1C, D, E, 2A, 5C, D, 7A). Please provide incubation time for kinase reactions in figure legends (e.g. Fig 1C, D, E, ...).

• __Response: All of these incubation times are included in the materials and methods. We ____will add to the figure legends depending on journal style. We have added selected MW numbers to the MW markers in 1D,E, 5D,7A.

__

• Please indicate whether representative experiments are shown, and specify the number of replicates performed for each assay (e.g. Fig 1C, D, E, ...). This information is essential for assessing the reproducibility and robustness of the findings.

• __Response: We are somewhat confused by this comment. For each claim made about quantitative effects, we include a quantitation panel that contains experimental replicates (1F, 2D, 4D, 5C, 7B). For MST graphs, we state the number of replicates for each time point. __

• Please clarify the discrepancy in Figure 2A regarding the calcium concentration used. The results section (line 163) refers to 10 µM, whereas the figure legend (line 393) states 1 mM.

• __Response: We have corrected the figure legend to 10____m __

• Figure 2A should include zinc, as previous work by the authors has shown that zinc directly inhibits the kinase activity of PdtaS. It would also be informative to test c-di-GMP in Fig. 2, given that c-di-GMP has been described to binds PdtaS (PMID: 33772870), and that c-di-GMP binding at dimer interfaces has been demonstrated in transcription factors (e.g., PMID: 25171413).

• __Response: We did not test zinc because in our prior studies the effects of Zn and Cu were identical. We have tested c-di-GMP as noted above (see new Fig S3). __

• The interpretation in lines 206-207 is not convincing. PdtaS homologs may differ in ligand specificity, precluding the presence of a conserved ligand-binding cavity but not of a specific ligand binding cavity in the GAF/PAS domains. Functional divergence of the binding site can occur, and this possibility should be acknowledged.

• Response: We are somewhat confused by this comment. This is the sentence in question: "____This analysis suggests that the PdtaS kinase family has evolved to conserve the dimerization interface, shown above to be important for autokinase activity, but that the putative ligand binding domains do not have a conserved ligand cavity, arguing against a specific ligand that binds in the GAF or PAS pocket in this family of histidine kinases." The sentence does not argue that there is no ligand binding in the GAF PAS cavity, only that the cavity is not conserved, and this argues against a single ligand. To clarify this point, we will insert the word "single" before "specific ligand"

Reviewer 2:

• The dimer model is consistent with trans phosphorylation, but I did not see model quality described, especially in the H303-ATP binding interface. Can the authors provide AlphaFold PAE and pLDDT scores?

• __Response: We have added a SI figure (Figure S4) with this data. __

• Although the effect of Cu and NO on the two mutant PdtaS is clear, why the WT activity in Fig. 2A is not also inhibited is not obvious to me, especially since WT dimerization is affected by Cu and NO (Fig. 2B, C). Is there also cis-autophosphorylation that masks reductions in trans phosphorylation? Is the WT signal saturated on this autorad?

• __Response: This assay, as noted in the figure legend, was done with 10_m_M Cu. This dose is only mildly inhibitory to the wild type kinase, as demonstrated in Figure 5D-E, which clearly demonstrates Cu inhibition. We don't have an explanation for why the trans phosphorylation mutant pair is inhibited by lower doses of Cu. It is possible this reflects some cis-autophosphorylation, but the strong inhibition of trans autophosphorylation is consistent with our model. __

• The two Cys residues in PdtaS were previously found to affect kinase activity. Here, the authors show they also modestly affect dimerization. Since ~1/3 of mycobacteriales have both Cys, a double mutant would have been interesting for the in vitro characterization (it is used in live bacteria in Fig. 7A) and might show a more pronounced effect (not critical).

• __Response: Although we agree, we attempted to purify the double cysteine mutant from * coli* but unable to due to insolubility, so we were unable to test the protein. __

• Although competition data and structural model clearly indicate trans phosphorylation, some cis-phosphorylation can probably not be ruled out, especially since the dimer mutant H67A shows some activity. Although that mutation does not seem to fully disrupt the dimer, the H67A activity could be indicative of some cis-phosphorylation.

• __Response: The H67A mutant is a dimerization mutant that weakens, but does not completely disrupt the dimer. This mutant cannot be used to distinguish cis vs trans phosphorylation and therefore we cannot rule out a mixture of cis vs trans autophosphorylation. The data in figure 1 argues for trans phosphorylation being the dominant mechanism. __

• The Cys residues destabilize the dimer, and mutating the Cys stabilizes it, even canceling out the effect of the chemical destabilizers Cu and NO. In Fig. 4A, it looks like all Cys are too far apart to form disulfides, but Cu2+ can cause formation of disulfides. Can the authors comment on the distance of the Cys and the likelihood that disulfides have a role in this mechanism? If this were plausible, thiol-to-disulfide ratios with and without Cu could be directly measured. Although a bit more of a stretch, NO could also contribute to disulfide formation through ROS, and disulfides could be a way by which these two disparate ligands have the shared effect on activation shown here.

• __Response: As stated above, we are not able to comment about whether direct modification of these cysteines is occurring. We do not believe the proximity of the cysteines would allow disulfide formation. __

• The interdomain mutation Arg261Ala is quite nice and shows a specific effect on activity, but not dimerization, indicating that this interdomain ion bond somehow transfers the dimerization signal from the GAF to the PAS domain. Were there any other interdomain bonds? For completeness, was the basal autophosphorylating or phosphotransfer activity to PdtaR affected by the 261 mutation?

• __Response: We did not detect any other bonds in our modeling. The basal level of autophosphorylation of the R261A protein compared to WT is visible at the lower end of the Cu inhibition curve in 6E and is comparable. We did not observe a difference in autophosphorylation at 0 Cu in the gels supporting this curve. __

• First sentence in the Discussion, wording: The study investigates kinase activation, not signal sensing in a strict sense.

• __Response: We have edited this sentence. __

• Although this is primarily a biochemical, mechanistic study, one or two sentences on the biological significance of PdtaS/R in M. tuberculosis in the Introduction would be nice

• __Response: We believe these sentences in the introduction already satisfies this request: "PdtaS and PdtaR were implicated in the Rip1 pathway of * tuberculosis signal transduction by a genetic suppressor screen in which inactivation of either PdtaS or PdtaR reverted the copper and nitric oxide sensitivity of M. tuberculosis lacking rip1. Copper and NO directly inhibit the kinase activity of PdtaS, an inhibition that requires the N terminal GAF and PAS domains _[39]_, indicating that the GAF-PAS are necessary to transmit the inhibitory signal to the kinase domain." We would also note that although much of the data is biochemical, we test the in vivo relevance of our model using M. tuberculosis* strains carrying PdtaS mutations

__

Reviewer 3

• Limited characterization and validation of dimerization measurements: (a) while MST is an established technique, the central thesis relies heavily on dimerization measurements using this single method. Given the importance of this finding, at least one additional orthogonal approach would strengthen the conclusions significantly. Analytic size exclusion chromatography (SEC) could be a very simple, accessible and reliable approach to address this core mechanistic question. By choosing the right size resolution separation matrix, the authors should be able to separate complete monomers, from partial complexes (e.g. dimers only held through the kinase domain) and full dimers (the species the authors expect for the constitutively active wt protein). Ready advantage of having the wt protein can be taken, as well as several dimerization mutants (C53A, C57A, H67A), and presence/absence of cognate ligands (NO, Cu). For necessary reference standards, a dilution series should be able to reveal the elution position for wt monomers (and if this approach reveals to be difficult, mild chaotropic conditions can always be attempted, often times also pH shifts can do the job). Other techniques can point in the same direction as SEC, such as SAXS (best coupled to a SEC, or SEC-SAXS), native polyacrylamide gel electrophoresis, and/or dynamic light scattering.
• __Response: We appreciate the reviewers' careful suggestions for additional experimental approaches. Although logical, we are unable to undertake them at this time and further exploration will hopefully be stimulated by our study. __

(b) More importantly, additional techniques should be chosen such that a clear distinction can be made between two different scenarios, namely: that only the sensory domains (PAS/GAF) undergo ligand-triggered dissociation; or, instead, that the entire protein dissociates into separate monomers (i.e. including the kinase domains). This seems like an extremely important distinction, so that the proposed kinase-regulation mechanism is well understood/described. The first scenario would be less "disruptive" wrt previous paradigms (sensory domain dissociation could well be linked to a conformational rearrangement that allosterically inhibits kinase auto-phosphorylation).

• __Response: We agree that this is an important distinction. We would note here that our prior data (Buglino et al eLife 2021) demonstrated that the isolated kinase domain of PdtaS is not inhibited by copper or NO, indicating that the effect of these ligands both requires the GAF-PAS and that the kinase dimer itself is not sensitive to ligand induced inhibition. This result does not directly address the reviewer's question, which is whether there is localized inhibition of dimerization in the GAF-PAS dimer, which, via an allosteric mechanism, inhibits phosphorylation by the kinase domain, which we have shown is in trans, without actual dissociation. We are not aware of a technique that could distinguish what would presumably be a type of allosteric localized dimer disruption from full dissociation. Our data clearly indicates that the kinase inhibition effect is mediated by the dimer dissociation effect on the GAF/PAS and full characterization of the effects of that on the kinase domain will await further studies outside of this paper. __
• R261A mechanistic inconsistency: The manuscript shows that the R261A mutant has attenuated copper inhibition in vitro, albeit remaining functional in vivo (Figure 7B). While the authors acknowledge this suggests their "interdomain coupling model is incomplete or compensated by other mechanism in vivo," this significant discrepancy undermines confidence in the proposed mechanism and deserves more thorough investigation and/or discussion.
• __Response: We thank the reviewer for this comment, which relates to the R261A mutant. We disagree that this result "undermines confidence in the proposed mechanism". We rigorously interrogated our in vitro findings by genetic complementation in M. tuberculosis cells using epitope tagged proteins and these results largely confirmed the model in that C53A, C53A/C57A, and H67A all inactivated signaling, as predicted from our model. R261 is the exception and, as we discuss, it indicates that we do not completely understand the in vivo determinants of coupling between the GAF-PAS dimer and the kinase domain, which is dependent on R261A in vitro. __

Insufficient evidence about signal integration: While the authors argue this mechanism enables "integration of multiple inputs into the kinase without the constraints of specific ligand recognition" (lines 342-344), this appears conceptually flawed to me. The ligands (Cu and NO) must still be specifically sensed and bound somewhere on the protein to trigger dimerization disruption - the mechanism simply uses dimerization modulation as the output rather than the more typical allosteric conformational changes. The conservation pattern (interface > binding sites) may reflect selective pressure to maintain dimerization capability across the family, while individual species evolved different ligand specificities. The authors should clarify that their mechanism represents a novel output mode for ligand sensing rather than an alternative to specific ligand recognition, and discuss how this distinction affects their evolutionary interpretation.

• Response: We thank the reviewer for this comment. The issue raised is the difference between ligand "recognition" and "sensing" with the former implying a specific binding site (which we acknowledge above and in the paper that we do not identify) and the functional output modified by ligands. Our data supports that dimerization is an important mechanism of sensing, but we do not claim that the dimer interface is the binding site for the ligands. We would note that the following sentences were in the reviewed version of the paper and we believe clearly make the exact distinction that the reviewer requests: __ Abstract: "These results indicate that a single bacterial kinase can __sense chemically diverse inputs through inhibition of dimerization dependent phosphorylation"

Line 110: "Ligand binding pockets of GAF and PAS domains can bind a wide variety of ligands[38], but it remains to be determined whether multi-ligand sensing by PdtaS represents a manifestation of specific chemical recognition by the GAF-PAS domains or some other mechanism."

Line 119: "Mutations in the GAF dimer interface that alter dimerization also impair multi-ligand sensing __of Cu and NO in vitro and in M. tuberculosis cells. Our findings establish a mechanism of __multi ligand sensing through alteration of sensor oligomeric state."

Line 330: "Taken together, these data are consistent with a model in which modulation of dimer affinity is the sensing mechanism of the mycobacterial clade of PdtaS kinases, rather than specific recognition of Cu or NO by the ligand binding pockets of the GAF or PAS domains."

__We have edited one instance (line 337) in the discussion where the use of "recognition" might have been misconstrued. __

Minor Comments 1. The manuscript could better explain why PdtaS is described as "constitutively active" - the distinction between showing autophosphorylation activity in vitro versus true constitutive activity could be clearer. Can the authors show or refer to evidence of live constitutive PdtaR phosphorylation by PdtaS? (e.g. PhosTag electrophoresis gels of whole protein extracts and Western blotting revealed by anti-PdtaR; the use of NO and Cu can easily be used as inhibitors in such experimental setup).

• Response: We thank the reviewer for this question. Our basis for claiming that the kinase is constitutively active, both for autophosphorylation and phosphotransfer to PdtaR, is the following:
• __In the work of others and our prior work, PdtaS autophosphorylates without added ligand, which is contrary to most histidine kinases which are ligand activated. __
• __PtdaS phosphorylates PdtaR without added ligand in vitro (see Figure 5C of this paper) __

• __In terms of in vivo demonstration of PdtaR phosphorylation, this is very challenging in all response regulators given the unstable nature of the aspartate phosphorylation. We have been unsuccessful in visualizing PdtaR phosphorylation in vivo using phostag or western blotting. However, we note that our prior work demonstrated that mutation of the phosphoacceptor residue in PdtaR (D65A) phenocopied loss of both PdtaS and PdtaR (Buglino et al eLife 2021). __

• Figure 5D shows some gel quality issues and also limited detail in the legend to know what exactly each panel represents and labels' definitions (e.g. "Ca" on the first lane, etc). The difference between wt and mutant is not clearcut to me, difficult from these data alone to derive a reliable Ki. Furthermore, the control gel on the bottom for the wt (I believe this is a cold control gel to see loaded quantities of protein on each lane?), seems to have less protein in the higher Cu concentrations.

• __Response: The calcium lane is the divalent ion control as in the other figures. The legend of this figure refers to figure 1, which is more detailed and the identical assay. As noted in the methods, the phosphorylation signal is normalized to the total protein in the lower gel, so the lower amount of protein in these lanes in incorporated into the quantitation, which itself is derived from triplicate experiments, as noted in the legend. __

Enough experimental detail should be included on figure legends so that the experiments are self-explanatory.

• __Response: This is a journal style question that will be addressed depending on the identity of the eventual journal. __

Lines 184-185 : they only refer to the fact that c-di-GMP binds to the GAF domain of PdtaS, yet the paper by Hariharan et al 2021 also shows that it activates PdtaS's autokinase activity. This should be double-checked and taken into account for the discussion of cognate ligands' effects.

• Response: As noted above, we have added a supplemental figure (S3) that examines the effect of c-di-GMP on autokinase activity. Hariharan reported activation of PdtaS by c-di-GMP (Figure 6A of that publication). We do not see similar activation and do not observe an effect of cDG with Cu. Line 233: "Dimerization separation of function mutations" title is unclear

• Response: Edited The structural model source (AlphaFold3) should be mentioned in the main text, not just figure legends. AF3-predicted models should be illustrated according per-residue pLDDT reliability indices (typically with a color ramp).

• __Response: The paper contains this sentence:_ "_We performed bioinformatic analyses of the conservation of PdtaS across the Actinomycetota phyla and mapped this conservation onto the predicted full length PdtaS dimer structure predicted using AlphaFold". We have added the specific AlphaFold model (3) to this sentence. __

• __We have also added an SI figure containing the pLDDT data (Figure S4). __

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Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript by Sankhe and collaborators, investigates the mechanism by which the Mycobacterium tuberculosis two-component system PdtaS/PdtaR senses copper and nitric oxide. The authors demonstrate that PdtaS is a constitutively active histidine kinase that autophosphorylates in trans, and that ligand-triggered inhibition occurs through disruption of dimerization rather than typical allosteric conformational changes of the dimeric species. Through phylogenetic analysis, mutagenesis, and biochemical assays, they show that conservation occurs primarily at the dimer interface rather than putative ligand binding sites, supporting a novel mechanism of multi-ligand sensing through modulation of oligomeric state. The experimental design is generally sound, with appropriate controls and multiple lines of evidence supporting the main conclusions. The trans-autophosphorylation experiments are particularly elegant and convincing. While there are some mechanistic concerns that should be addressed (particularly around R261A, and the actual dimerization extent/effect), the core findings are significant, and the work represents an important contribution to understanding bacterial signal transduction.

Major Comments:

1. Limited characterization and validation of dimerization measurements: (a) while MST is an established technique, the central thesis relies heavily on dimerization measurements using this single method. Given the importance of this finding, at least one additional orthogonal approach would strengthen the conclusions significantly. (b) More importantly, additional techniques should be chosen such that a clear distinction can be made between two different scenarios, namely: that only the sensory domains (PAS/GAF) undergo ligand-triggered dissociation; or, instead, that the entire protein dissociates into separate monomers (i.e. including the kinase domains). This seems like an extremely important distinction, so that the proposed kinase-regulation mechanism is well understood/described. The first scenario would be less "disruptive" wrt previous paradigms (sensory domain dissociation could well be linked to a conformational rearrangement that allosterically inhibits kinase auto-phosphorylation). Analytic size exclusion chromatography (SEC) could be a very simple, accessible and reliable approach to address this core mechanistic question. By choosing the right size resolution separation matrix, the authors should be able to separate complete monomers, from partial complexes (e.g. dimers only held through the kinase domain) and full dimers (the species the authors expect for the constitutively active wt protein). Ready advantage of having the wt protein can be taken, as well as several dimerization mutants (C53A, C57A, H67A), and presence/absence of cognate ligands (NO, Cu). For necessary reference standards, a dilution series should be able to reveal the elution position for wt monomers (and if this approach reveals to be difficult, mild chaotropic conditions can always be attempted, often times also pH shifts can do the job). Other techniques can point in the same direction as SEC, such as SAXS (best coupled to a SEC, or SEC-SAXS), native polyacrylamide gel electrophoresis, and/or dynamic light scattering.
2. R261A mechanistic inconsistency: The manuscript shows that the R261A mutant has attenuated copper inhibition in vitro, albeit remaining functional in vivo (Figure 7B). While the authors acknowledge this suggests their "interdomain coupling model is incomplete or compensated by other mechanism in vivo," this significant discrepancy undermines confidence in the proposed mechanism and deserves more thorough investigation and/or discussion.
3. Insufficient evidence about signal integration: While the authors argue this mechanism enables "integration of multiple inputs into the kinase without the constraints of specific ligand recognition" (lines 342-344), this appears conceptually flawed to me. The ligands (Cu and NO) must still be specifically sensed and bound somewhere on the protein to trigger dimerization disruption - the mechanism simply uses dimerization modulation as the output rather than the more typical allosteric conformational changes. The conservation pattern (interface > binding sites) may reflect selective pressure to maintain dimerization capability across the family, while individual species evolved different ligand specificities. The authors should clarify that their mechanism represents a novel output mode for ligand sensing rather than an alternative to specific ligand recognition, and discuss how this distinction affects their evolutionary interpretation.

Minor Comments

1. The manuscript could better explain why PdtaS is described as "constitutively active" - the distinction between showing autophosphorylation activity in vitro versus true constitutive activity could be clearer. Can the authors show or refer to evidence of live constitutive PdtaR phosphorylation by PdtaS? (e.g. PhosTag electrophoresis gels of whole protein extracts and Western blotting revealed by anti-PdtaR; the use of NO and Cu can easily be used as inhibitors in such experimental setup).
2. Figure 5D shows some gel quality issues and also limited detail in the legend to know what exactly each panel represents and labels' definitions (e.g. "Ca" on the first lane, etc). The difference between wt and mutant is not clearcut to me, difficult from these data alone to derive a reliable Ki. Furthermore, the control gel on the bottom for the wt (I believe this is a cold control gel to see loaded quantities of protein on each lane?), seems to have less protein in the higher Cu concentrations.
3. Enough experimental detail should be included on figure legends so that the experiments are self-explanatory.
4. Lines 184-185 : they only refer to the fact that c-di-GMP binds to the GAF domain of PdtaS, yet the paper by Hariharan et al 2021 also shows that it activates PdtaS's autokinase activity. This should be doube-checked and taken into account for the discussion of cogante ligands' effects.
5. Line 233: "Dimerization separation of function mutations" title is unclear
6. The structural model source (AlphaFold3) should be mentioned in the main text, not just figure legends. AF3-predicted models should be illustrated according per-residue pLDDT reliability indices (typically with a color ramp).
7. Ensure consistent reporting of replicate numbers across all experiments.

Significance

General assessment:

The study provides elegant trans-autophosphorylation experiments and strong phylogenetic support for dimerization interface conservation. However, it relies heavily on MST as the sole method for measuring dimerization -the main finding in terms of novelty- and shows mechanistic inconsistencies (R261A functional in vivo despite attenuated inhibition in vitro).

Scientific Advance:

While the authors overstate novelty by claiming to bypass "specific ligand recognition" (ligands must still bind specifically to trigger dimerization disruption), the identification of dimerization modulation as the inhibitory output mechanism represents a meaningful advance. The work establishes an important framework for understanding how M. tuberculosis senses multiple host-derived stresses and may inform studies of other inhibitory sensor kinases.

Target Audience:

I believe this work will be of great interest to bacterial signaling researchers and M. tuberculosis pathogenesis specialists, with broader appeal to the microbiology community studying two-component systems and host-pathogen interactions. The dimerization-based mechanism may also attract structural biologists studying multi-domain sensor architectures.

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Referee #2

Evidence, reproducibility and clarity

Summary

This study explores the activation mechanism of a two-component system in M. tuberculosis, PdtaS/R. PdtaS/R is known to sense Cu and NO. Here, the authors show that PdtaS autophosphorylates in trans upon dimerization. PdtaS is constitutively active, and Cu and NO binding inactivate the kinase by preventing dimerization. The dimerization interface, but not the ligand binding domain, is conserved in PdtaS orthologs, and disruption of the dimer interface also disrupts ligand sensing in vitro and in live M. tuberculosis.

Major comments

This is an interesting and thorough analysis of the (in)activation mechanism of a TCS. Although much work has been done on such systems, this TCS is quite interesting as it is a rarer cytosolic, soluble system, because it has been shown to sense two chemically very different ligands- Cu and NO (and apparently also cdi-GMP)- and because it is constitutively active and inactivated by ligands, which is more unusual. A main strength of the paper is the identification of a range of mutants with specific effects on dimerization, activity, auto and substrate phosphorylation and GAF-PAS interactions to probe and parse the contribution of different aspects of the mechanism. The flow of the experiments is logical, and the data are generally clear, even though TCS phosphorylation is short-lived and can be tricky to capture. The heterodimer mixing experiments using WT, phosphoreceptor His-, and ATP binding mutants are clear and conclusively show trans phosphorylation. The control ruling out dimerization defects of the mutants is useful, and bioinformatic analysis of the GAF and PAS domains shows surprisingly clearly the conservation of the dimer interface, not the ligand binding site. The experiments showing the effects of dimerization on the activity of PdtaS are conclusive, with mutations showing stronger (Cys) or weaker (His67, already shown in a previous paper) dimerization and the expected effects on PdtaS activity. Testing some key mutants in live bacteria is another nice feature of the study that shows that in vitro findings (mostly) carry over to live bacteria, which is not always the case, and often just not tested. In sum, this is a solid, straightforward study on the activation mechanism of a more unusual M. tuberculosis TCS.

Minor comments

The dimer model is consistent with trans phosphorylation, but I did not see model quality described, especially in the H303-ATP binding interface. Can the authors provide AlphaFold PAE and pLDDT scores?

Although the effect of Cu and NO on the two mutant PdtaS is clear, why the WT activity in Fig. 2A is not also inhibited is not obvious to me, especially since WT dimerization is affected by Cu and NO (Fig. 2B, C). Is there also cis-autophosphorylation that masks reductions in trans phosphorylation? Is the WT signal saturated on this autorad?

Related: Although competition data and structural model clearly indicate trans phosphorylation, some cis-phosphorylation can probably not be ruled out, especially since the dimer mutant H67A shows some activity. Although that mutation does not seem to fully disrupt the dimer, the H67A activity could be indicative of some cis-phosphorylation.

Some kinetic experiments would have been useful to gauge the timescale of these mechanisms (but not critical).

The two Cys residues in PdtaS were previously found to affect kinase activity. Here, the authors show they also modestly affect dimerization. Since ~1/3 of mycobacteriales have both Cys, a double mutant would have been interesting for the in vitro characterization (it is used in live bacteria in Fig. 7A) and might show a more pronounced effect (not critical).

The Cys residues destabilize the dimer, and mutating the Cys stabilizes it, even canceling out the effect of the chemical destabilizers Cu and NO. In Fig. 4A, it looks like all Cys are too far apart to form disulfides, but Cu2+ can cause formation of disulfides. Can the authors comment on the distance of the Cys and the likelihood that disulfides have a role in this mechanism? If this were plausible, thiol-to-disulfide ratios with and without Cu could be directly measured. Although a bit more of a stretch, NO could also contribute to disulfide formation through ROS, and disulfides could be a way by which these two disparate ligands have the shared effect on activation shown here.

The interdomain mutation Arg261Ala is quite nice and shows a specific effect on activity, but not dimerization, indicating that this interdomain ion bond somehow transfers the dimerization signal from the GAF to the PAS domain. Were there any other interdomain bonds? For completeness, was the basal autophosphorylating or phosphotransfer activity to PdtaR affected by the 261 mutation?

First sentence in the Discussion, wording: The study investigates kinase activation, not signal sensing in a strict sense.

Although this is primarily a biochemical, mechanistic study, one or two sentences on the biological significance of PdtaS/R in M. tuberculosis in the Introduction would be nice

Christoph Grundner

Significance

This is a mechanistic study on the (in)activation mechanism of an M. tuberculosis TCS with some unusual features: The kinase, PdtaS, is constitutively active and ligand binding inactivates it. It is a soluble system that binds multiple ligands, fewer of which have been described to date. While trans-phosphorylation and regulation by dimerization are not conceptually new, they were also not a given in this more unusual TCS. The authors identified relevant mutants at several steps of the activation mechanism to specifically probe the effect of dimerization, interdomain communication etc., and test their relevance in live bacteria, which goes beyond what comparable biochemical studies typically do. The authors have previously published some aspects of the PdtaS/R activation mechanism (inhibition by Cu and NO, Cys mutants). The conserved dimer interface suggests that many of the PdtaS orthologs are similarly regulated, and that different ligands can converge on this dimerization-dependent activation. Thus, the study could be relevant for the whole family and the range of ligands they likely sense. The study summarizes the findings in the idea that PdtaS activity relies on dimerization to react to divergent ligands rather than specific ligand binding to the GAF and PAS domains. This statement is perhaps too strong and that rather than either/or, it is likely both. Overall, this is a thorough biochemical study that reveals aspects of a more non-typical TCS activation mechanism that are of high interest to the Mtb and bacterial signaling field.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript the authors aim to characterize the mechanism regulating PdtaS activity, a histidine kinase of Mycobacterium tuberculosis responding to nitric oxide (NO) and copper ions (Cu). The PdtaS/PdtaR two-component system is atypical, with PdtaS being cytoplasmic and phosphorylating PdtaR in the absence of signal(s). Here, the authors characterize key residues involved in PdtaS dimerization necessary for PdtaS activity on PdtaR, in vitro and in M. tuberculosis. They show that both NO and Cu inhibit dimerization and thus PdtaS autokinase activity. They propose a model where changes in dimer affinity serve as the sensing mechanism allowing to integrate multiple signals without relying on specific ligand binding.

Major comments:

• The primary concern pertains to ligand recognition by PdtaS. While PdtaS constitutive autophosphorylation is shown to be dependent on dimerization, there is no direct evidence of ligand binding. How Cu and NO inhibits PdtaS activity remains uncharacterized. Is it unclear if there are specific binding pockets inducing PdtaS conformational switch, if both substrates compete for a single binding pocket, or if Cu and NO inhibit dimerization by binding to the dimer interface. Similarly, it is unclear if NO does not covalently modify the key cysteine residues by S-nitrosylation, nor if Cu induces a distinct and reversible thiol-switch by site-specific oxidation that regulates PdtaS dimerization and activity.
• Since there is currently no direct evidence of ligand binding or residue modification, the conclusions drawn-particularly in the title and discussion-should be presented more cautiously, unless further structural, biochemical, or genetic data substantiate ligand binding.
• Given the focus on ligand effects on PdtaS dimerization and activity, zinc and c-di-GMP should also be considered, as prior studies have suggested they may be sensed by PdtaS. Similarly, given the claim of multiligand sensing, it would be valuable to examine the combined effects of NO and Cu. Do they act additively, synergistically, or interfere with each other?
• OPTIONAL. A significant limitation is the exclusive consideration of a single PdtaS conformation-the autophosphorylation-competent state. Histidine kinases typically cycle through at least three distinct enzymatic activities: phosphatase, autokinase, and phosphotransfer. Each of these functions relies on specific conformational states, which are often modulated by ligand binding. It is therefore important to investigate whether PdtaS also possesses phosphatase activity. Do ligands such as NO and Cu influence this activity-increasing phosphatase function, or simply inhibiting autophosphorylation and/or phosphotransfer? Moreover, does the monomeric or dimeric form of PdtaS exhibit phosphatase activity? In addition, the stability of phosphorylated PdtaR should be addressed, as it is crucial for understanding the overall dynamics and output of the signaling cascade.

Minor comments:

• PdtaS variants and mutants are neither introduced nor adequately described. For example, in lines 144-150, PdtaS-H303Q and G443 are mentioned without citation, and their construction is not described in the Materials and Methods section. As a result, it is difficult to determine which experiments and constructs are specific to this manuscript. Please provide a detailed Materials and Methods section, and include as supplementary material a complete list of all strains, primers, and constructs used in this study, along with their origins.
• References: Xing J et al 2023 is duplicated. Please correct in the text and in the references list.
• Please provide molecular weights on gels (fig. 1C, D, E, 2A, 5C, D, 7A).
• Please provide incubation time for kinase reactions in figure legends (e.g. Fig 1C, D, E, ...).
• Please indicate whether representative experiments are shown, and specify the number of replicates performed for each assay (e.g. Fig 1C, D, E, ...). This information is essential for assessing the reproducibility and robustness of the findings.
• Please clarify the discrepancy in Figure 2A regarding the calcium concentration used. The results section (line 163) refers to 10 µM, whereas the figure legend (line 393) states 1 mM.
• Figure 2A should include zinc, as previous work by the authors has shown that zinc directly inhibits the kinase activity of PdtaS. It would also be informative to test c-di-GMP in Fig. 2, given that c-di-GMP has been described to binds PdtaS (PMID: 33772870), and that c-di-GMP binding at dimer interfaces has been demonstrated in transcription factors (e.g., PMID: 25171413).
• I am not convinced by the interpretation line 206-207. PdtaS homologs can have different ligand specificity, impling the conservation of a ligand cavity in the GAF/PAS domains.
• The interpretation in lines 206-207 is not convincing. PdtaS homologs may differ in ligand specificity, precluding the presence of a conserved ligand-binding cavity but not of a specific ligand binding cavity in the GAF/PAS domains. Functional divergence of the binding site can occur, and this possibility should be acknowledged.

Significance

The manuscript demonstrates that PdtaS autokinase activity occurs in trans and that homodimerization is critical for its constitutive activity. While these findings extend previous work by the authors (PMID: 34003742)-which had already identified several key residues in PdtaS, including cysteines essential for NO and Cu sensing-they represent incremental advances. The mechanistic model proposed remains speculative without substantial additional experimental validation. The conclusions rely heavily on structural predictions from AlphaFold, representing only a single conformation corresponding to the autokinase-competent state. Crucially, the manuscript does not provide direct evidence for the mechanism of NO and Cu sensing. It also excludes the possibility of direct ligand binding-including untested candidates such as zinc and c-di-GMP-to a specific pocket, without experimentally addressing the hypothesis. These gaps significantly limit the mechanistic insight and overall impact of the study.

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Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

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Referee #3

Evidence, reproducibility and clarity

Velázquez et al. investigate the transcriptomic and epigenetic consequences of exogenous expression of the Ewing sarcoma fusion oncogene EWSR1∷FLI1 (EF1) in yeast. The study provides compelling evidence that EF1 can bind ETS transcription factor motifs, as well as a single 4xGGAA repeat within the S. cerevisiae genome, despite the absence of several canonical cofactors often implicated in EF1 biology, including CBP/p300 and Polycomb group (PcG) proteins. The authors further show that EF1 expression redistributes RNA Polymerase II toward EF1-bound ETS sites, yet. Strikingly, this relocalization is accompanied by only modest global transcriptional effects relative to those reported in human or insect systems. In addition, EF1 expression reverses repeat-associated epigenetic silencing of synthetic GGAA microsatellites in engineered reporter strains. Taken together, the data support the conclusion that GGAA microsatellite-mediated transcriptional rewiring is a comparatively conserved EF1 property, whereas broader transcriptomic changes arising from individual EF1-bound ETS sites appear to be more context-dependent. Overall, the manuscript is clearly written and logically organized, and the methodological descriptions and data-analysis details appear sufficient to enable reproducibility.

Major comments

None.

Minor comments

1. Additional citations in the Introduction. A small number of additional references would further support specific statements.
   • End of paragraph 3: consider adding Boulay et al. (2017).
   • Paragraph 4, after "proximal and distal genes": consider adding Tomasou et al. (2015) and Orth et al. (2022).
2. Potential antibody cross-reactivity in the CoIP experiment. Is there an EWSR1 homolog in S. cerevisiae? To rule out unintended interactions, it would be helpful to exclude binding of endogenous yeast proteins by the anti-EWS antibody used for co-immunoprecipitation, for example via a homology search and/or appropriate specificity controls.
3. Clarification of EF1-associated toxicity. The authors suggest that part of the observed transcriptional signal may reflect EF1 toxicity. It would strengthen the interpretation to characterize this phenotype more explicitly (e.g., growth rate over time, viability/cell death, or longer-term fitness effects). In addition, it would be informative to test whether toxicity depends on EF1 DNA-binding activity and whether truncation mitigates toxicity, as reported in Drosophila (Mahnoor et al., 2024).
4. RNA Polymerase II relocalization versus limited transcriptional output. The apparent recruitment/repositioning of RNA Pol II in the absence of substantial transcriptional change is particularly interesting. This point could be strengthened by assessing RNA Pol II "states," for example using phosphorylation-state specific antibodies to distinguish stalled/paused from actively elongating polymerase.
5. Promoter choice in the GGAA microsatellite reporter. The use of a modified constitutive promoter to monitor GGAA microsatellite-dependent activation is somewhat unconventional. Many studies (e.g., Gangwal et al., Hölting et al.) use minimal promoters to demonstrate EF1-dependent upregulation rather than reversal of heterochromatin-associated silencing. A brief rationale for the chosen design or discussion of how it relates to prior reporter paradigms would help readers contextualize the approach.
6. Reconstituting minimal cofactor requirements for ETS-site activity. The finding that EF1 binding at single ETS sites does not translate into strong transcriptomic remodeling in yeast is an intriguing aspect of the work. The manuscript could be further enriched by systematic attempts to reconstitute candidate cofactors in this minimal system to define the minimal requirements for ETS-site-dependent gene activation.

Significance

This study will be of broad interest because it convincingly separates EF1-driven GGAA microsatellite-dependent activation from the canonical regulatory functions of FLI1, reinforcing the concept that fusion transcription factors can acquire genuinely neomorphic activities-activities that may ultimately be therapeutically actionable. Beyond the biological insight, the successful establishment of exogenous EF1 expression in yeast is itself a notable technical achievement, given the longstanding challenges associated with EF1 expression in heterologous settings. As presented here, yeast offers a valuable platform to interrogate EF1 function in a simplified and more controlled context.

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Referee #2

Evidence, reproducibility and clarity

In this article, Velázquez et al. use the S. cerevisiae model to study the interactome of the fusion protein EWSR1::FLI1, characteristic of Ewing sarcoma. They employ this system to determine to what extent the neomorphic features of EWSR1::FLI1 depend on specific cofactors. The use of yeast as a simplified system allows the exploration of EWSR1::FLI1's dependence on key cofactors (ETS-TFs, Polycomb, CBP/p300, BAF) that are absent in this organism. Since these proteins are poorly conserved in yeast (e.g., BAF) or do not exist at all (ETS-TFs, Polycomb, CBP/p300), the aim is to determine whether their presence is necessary for EWSR1::FLI1 function. According to the authors, the interactome of EWSR1::FLI1 is much more limited in yeast than in humans, sharing only the core transcriptional machinery (RNA Pol II, FACT), failing to recruit BAF complexes, and showing enrichment in the SAGA chromatin remodeling complex, which is not part of the human interactome. In yeast, EWSR1::FLI1 binds to ETS consensus sites and CA repeats. Moreover, EWSR1::FLI1 induces only minor changes in the yeast expression profile, in contrast to what is observed in humans or Drosophila. Finally, EWSR1::FLI1 can bind to artificially introduced GGAA repeat regions in yeast, which naturally lacks such repeats, the sequences that EWSR1::FLI1 targets in humans to activate transcription. The study is methodologically sound and could potentially shed light on the requirements of EWSR1::FLI1.

Velázquez and colleagues provide a conceptually interesting model. However, the interpretation of the results requires caution. As a final conclusion, although the work is methodologically correct, the high toxicity of the model prevents more definitive insights. Based on the results presented, it cannot be stated that yeast is a suitable model to study EWSR1::FLI1 mechanisms. Put differently, the presence of specific cofactors is required to recapitulate, at least partially, the intrinsic effects of EWSR1::FLI1.

Major comments

As shown in Supplementary Figure 1, the expression of EWSR1::FLI1 in yeast is highly toxic. Indeed, as the authors acknowledge in the discussion (page 11, end of the last paragraph), many of the observed expression changes may be a consequence of this toxicity, reflected in the high proportion of deregulated genes related to stress. This makes it difficult to draw clear conclusions. Since the model is inducible, it would be worth considering whether expression levels of EWSR1::FLI1 could be controlled. Achieving a balance with tolerable expression levels might help clarify the situation.

Only the interactome of EWSR1::FLI1 has been studied. Given that the interactome largely depends on DNA-binding capacity, it would be informative to analyze the interactome of the RRLL mutant. It would also be valuable to determine the interactomes of wild-type EWSR1 and FLI1, or better, of the domains involved in the fusion, to identify which proteins interact with each domain.

A fundamental feature of EWSR1::FLI1 is its ability to form condensates on GGAA repeats. These condensates are essential for cofactor recruitment and transcriptional activation at GGAA microsatellites. Since yeast lacks GGAA microsatellites, condensate formation is unlikely, but it would be important to determine whether it occurs. For example, the methodology used by Selig EE et al. (Phase separation of the oncogenic fusion protein EWS::FLI1 is modulated by its DNA-binding domain. Proc Natl Acad Sci U S A. 2025;122(20):e2221823122) could be applied to assess condensate formation, which may explain many of the results described.

One striking aspect is the discrepancy between binding regions and regulated genes. The authors report 834 binding regions but only 86 regulated genes (73 up, 13 down). This suggests no clear association between DNA binding and transcriptional activation in yeast, possibly due to the absence of cofactors or the inability to form aggregates on GGAA microsatellites. The lack of correlation points to indirect mechanisms, such as RNA Pol II redistribution, as the authors suggest.

In Ewing sarcoma cells, EWSR1::FLI1 binding to ETS consensus sites is associated with repression through displacement of ETS transcription factors. In yeast, most binding sites appear to be putative ETS consensus sites, but no repressive effect is observed, likely because there are no ETS factors to displace. This should be discussed.

The claim that EWSR1::FLI1 "deregulates the yeast transcriptome" seems exaggerated, given the small number of affected genes compared to humans. Moreover, many correspond to stress responses, suggesting nonspecific effects of overexpression. This conclusion should be tempered.

In Figure 5A, EWSR1::FLI1 restores GFP expression but to levels still lower than those observed in control cells. In humans, combining the GGAA promoter with EWSR1::FLI1 leads to higher expression than baseline. The absence of this effect in yeast indicates that EWSR1::FLI1 is not sufficiently active, even when a GGAA repeat locus is introduced, likely due to missing cofactors. This possible explanation should be included in the discussion.

Minor comments

• Raw data from proteomics, RNA-seq, and ChIP-seq studies should be deposited in public repositories.
• Supplementary material should include a table with interactome results, listing proteins, relative expression levels (e.g., log2), p-values, adjusted p-values, and whether the protein has been described in the human interactome (with references).
• Supplementary material should also include a table with RNA-seq results, showing means, fold changes, adjusted p-values, and whether the genes are EWSR1::FLI1 targets in humans (see Orth MF et al., Cell Reports, 2022;41(10):111761).
• The number of experiments performed in proteomics, RNA-seq, and ChIP-seq should be specified both in the methods section and in figure legends.
• In Figures 4D and 5A, the meaning of the letters used to indicate statistical significance should be clarified, or preferably replaced with asterisks, which are the standard convention.
• A GSEA analysis should be performed to test whether the expression pattern regulated in yeast corresponds to the transcriptional program of EWSR1::FLI1 in Ewing sarcoma cells.

Significance

Strengths

1. Originality of the experimental model The use of yeast as a simplified system eliminates the influence of endogenous cofactors (ETS-TFs, Polycomb, CBP/p300, BAF), allowing the study of intrinsic functions of EWSR1::FLI1 in a "minimal" context.
2. Relevant findings on the interactome The study shows that the interactome in yeast is reduced and centered on the core transcriptional machinery (RNA Pol II, FACT, SAGA), providing information on essential and specific interactions, although already known.
3. Validation of binding to ETS motifs and GGAA repeats The study confirms that EWSR1::FLI1 retains its ability to bind ETS motifs and GGAA repeats in yeast (when artificially introduced), reproducing a key feature of its biology in human cells.

Weaknesses

1. Limited scope of transcriptome deregulation Only 86 genes (73 up and 13 down) were regulated, a very small percentage compared to humans. Moreover, many appear to correspond to stress responses, which challenges the claim that EWSR1::FLI1 "deregulates the yeast transcriptome."
2. Methodological and data presentation shortcomings The number of replicates in the interactome studies is not specified, and the raw proteomic and transcriptomic data are not deposited in public repositories.
3. Limitations of the model compared to humans The yeast model does not recapitulate the most relevant and characteristic aspects of EWSR1::FLI1 in human cells, but it is useful to confirm the need for cofactors to carry out its function.

Advance

The study does not provide major conceptual advances in the biology of EWSR1::FLI1, although it indirectly confirms what is already known about the requirement for cofactors and DNA domains necessary for its function. In other words, the inability to reproduce what is observed in the more complex human system precisely confirms that those elements present in humans and absent in yeast are essential for its activity.

Audience

The article is undoubtedly of interest to a specialized audience in the field of Ewing sarcoma, although in my opinion of limited interest to other fields. It is also relevant from a basic research perspective, as it highlights why not every model is suitable for studying the biology of a given protein, and that exploring this is important to understand when a particular model may not be the most appropriate-an insight that is itself valuable.

Expertise My field of expertise is the study of Ewing sarcoma, which I have pursued for 25 years. I cannot assess in detail the methodological description of the proteomic studies, but I do consider myself qualified to interpret the results derived from them

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Referee #1

Evidence, reproducibility and clarity

Summary: This study addressed the effect of EWS:FLI1 expression in heterologous budding yeast, using three sets of experiments: 1) EWS::FLI1 interactome in yeast, 2) EWS::FLI1 genomic binding sites and transcriptome changes induced by EWS::FLI1 in yeast, and 3) whether EWS:FLI1 can activate transcription through GGAA tandem repeats in yeast. The yeast EWS::FLI1 interactome showed enrichment for the SAGA chromatin remodeling complex and lacked the BAF and spliceosome complexes while sharing RNA polymerase II and FACT with the human counterpart. EWS::FLI1 bound to hundreds of ETS sites in the yeast genome, but caused minimal transcriptional changes. EWS::FLI1 activated a GGAA tandem repeat-driven reporter in yeast.

Major comments:

While the manuscript title states EWS::FLI1 functions as a pioneer factor in Saccharomyces cerevisiae, the authors merely demonstrated that EWS:FLI1 can activate a GGAA repeat-driven reporter in yeast, without any evidence for GGAA-repeats having compact closed chromatin configuration, which is opened by EWS::FLI1, recruiting chromatin modifiers and allowing access by other transcription factors (these are the definition of a 'pioneer factor'). The claim that EWS::FLI1 functions as a pioneer factor in yeast is not supported by the small amount of data from a heterologous reporter experiment.

OPTIONAL: The toxicity of wild-type EWS::FLI1 in Saccharomyces cerevisiae, as seen in most human cell types, is intriguing and clarifying the nature of this toxicity could provide a useful insight.

The data and the methods are presented in such a way that they can be reproduced.

The replicates and statistical analyses are generally adequate.

Minor comments:

Prior studies are referenced appropriately.

The figures are generally clear and accurate. Some of the text is wordy and can be simplified to improve the readability.

Significance

The study addressed the consequence of EWS::FLI1 expression in heterologous budding yeast system. Overall, the study is largely descriptive with little mechanistic insights, and the findings from the heterologous system do not seem to have much impact on the Ewing sarcoma field though they might suffice the curiosity of those in the field. The audience would be 'specialized,' limited to those working on the basic science of Ewing sarcoma.

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Referee #3

Evidence, reproducibility and clarity

Perez-Rico et al use dCAS9 to activate and repress L1 expression levels in the subfamily level for younger mouse L1s to address their cisregulatory potential

They choose to transcriptionally perturb full-length L1s subfamily.

An important topic, and I liked the approach of using CRISPR to perturb an entire subfamily of transposable elements. However, this study has yet to add any new findings or conclusions. This study can be improved by further analysis or experimentation. The regulatory role of L1s in cis-regulatory function has been previously demonstrated in mouse and human stem cell systems using multiple approaches, including CRISPR-mediated perturbations, CRISPR-based deletions, and 3D chromatin structure analysis. My main concern is the analysis is very superficial and lacks integration of other datatypes such as HiC to further support the role of L1s in enhancer activity and further validation on candidate loci. One of the major limitations of CRISPR-based perturbations is that it can be difficult to conclude the cis-regulatory role of these targeted elements (L1) as synthetic tethering of VPR or KRAB domain can indirectly spread their effect in cis, which otherwise may not have a specific cis-regulatory role to regulates genes in cis. Some of the major comments that needs to be addressed to strengthen the manuscript conclusions

1. One of the important controls could be targeting different or older L1s to show how it can affect gene expression. can authors perturb older families?
2. Although meta-analysis of L1s show up/downregulation of L1MdTf, ChIPseq for dCAS9 is needed to demonstrate which L1s are directly targeted in the experiment and analyse the data separately for dCAS9 bound L1s vs rest of the L1s in the subfamily.
3. L1s' transcriptional activation could be independent of their cis-regulatory activity. So, it is important to analyse the enhancer chromatin feature of TEs: Do they make 3D contact with the nearby genes?
4. how many replicates of RNA seq is done?
5. Are genes that respond to CRISPR activation in the same TAD? Do they loop with LINE1?
6. Figures 4 A &B show clear perturbation of host genes upon CRISPRi. However, they need to show L1s outside the genes (not in the introns) as CRISPR dCAS9 perturbation of Intronic L1s is expected to affect the expression of genes.
7. One of the key experiment missing is to genetically delete candidate L1s that are intergenic that are predicted to have a cis-regulatory function in the RNAseq data.
8. Authors should present the RNAseq data for genes 10 to 100 kb away from dCAS9-KRAB and dCAS9-VPR targeted L1s. It will be interesting to compare KRAB v VPR effect with distance.
9. The suggested role of L1s in neuronal gene expression is not strongly supported by their experiments or anlaysis. The authors end the results section with "Most of these genes are not expressed or have low expression levels in ESCs compared to other upregulated genes that are not part of these processes and pathways (Fig.S9E)". This result suggests that dCAS9-VPR targeting to multiple (How many are targeted is missing) L1s leads to the activation of many genes that are not normally expressed in mESCs due to the spreading of transcriptional activators or mESCs getting spontaneously differentiated to the neuronal lineage. Authors need to address these points.

Minor comments

Fig 2E) which housekeeping gene

Figures 4 A &B, show if these L1s make looping interactions or are in the same TAD as target genes.

Referee Cross-commenting

I agree with the other two reviewers points.

Significance

This study can be improved by further analysis or experimentation. In its current version, the conceptual advance offered by the current results and approach of the manuscript seem limited.

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Referee #2

Evidence, reproducibility and clarity

In this study Pérez-Rico et al. set out to study the cis-regulatory effects of evolutionary young L1 elements (specifically L1MdTf) in mouse embryonic stem cells. Using state of the art systems, they manage to silence/activate these elements expression and study the following gene expression cascade.

Major comments:

1. A general assessment or profiling of the L1MdTf expression in WT mESC is missing. It is very challenging to set their results in perspective (especially those of the repression system) without a general overview of the baseline L1-expression in mESC. How many elements does the WT mESC express? How is the genomic distribution of these elements? And how does it relate to nearby gene expression?
2. Off-target effects are very poorly documented and limited to in silico analysis. Documentation of changes in H3K4me3 and H3K9me3 upon activation/silencing would be beneficial to interpret the results. As it is now it is very difficult to understand why the activation-system is so much stronger that the silencing system.
3. It would be beneficial to explain why different experimental strategies were used for silencing/activation?
4. The study would benefit of a more detailed characterization of their systems' effect. E.g. It is not clear from Figure 3D-E how many of these repeats are part of the L1MdTf subfamily or other closely related subfamilies. This is relevant to assess the specificity of the systems.
5. The RNA-seq analysis relies on reads that are too short to uniquely map most L1s in the mouse genome. This should be mentioned and discussed.
6. A key issue that remains unresolved is the functional of L1-silencing/activation in mESC. Does this change cell morphology, pluripotency, or differentiation potential? This is essential information.
7. Fig 3B: Is this n=2? Hence why there is no statistical analyses? Same for Fig 5A-B: here a p-value is presented but it would be good to highlight the statistically significant results somehow.
8. Are only L1MdTf elements plotted in Fig 3D and 3E? As the authors claim that the system is quite specific, it would be good to have a clear view of the repeats that are differentially expressed and are evolutionarily close to the L1MdTf family. The figure might also benefit of some further characterization on a family level (multi-mapping) rather than single elements (unique mapping or multi mapping with reads that map to a single location, like here)
9. The authors provide some evidence for the existence of a bidirectional promoter on L1MdTf elements. In what elements was this observed? Does it result in chimeric transcripts? And if so, are these genes in line with the enrichment found?

Minor comments:

1. The introduction would benefit from a more detailed description of the L1-content in the mouse genome including the presence of polymorphic elements.
2. There is no characterization of the edited mESC. Stainings? Markers from bulk RNA seq analysis? Morphology assessment?

Significance

The manuscript is timely and in line to some similar and very recent studies suggesting a link between evolutionary young L1s and neuronal-related genes in mice (e.g. Toda et al.). However, the manuscript is quite preliminary in the current form. The investigation of potential off-target effects of their system requires more in-depth investigations. In addition, the manuscript could be improved with further exploration into the functional consequences of L1-silencing/activation.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors utilize engineered transcriptional effectors (CRISPRa or KRAB-Zinc Finger proteins) to activate or inhibit the expression of retrotransposons in mouse embryonic stem cells. They focus on a young L1 family in mouse, L1MdTf, which is particularly active. This study reveals extensive alterations in gene expression for surrounding genes, and it suggests that the dysregulated genes are enriched in repressive chromatin and preferentially associated with neuronal functions.

Major comments

The experiments are well-executed and controlled overall. However, to fully support the conclusions, a few aspects of the work could be strengthened:

1. Engineered Effector Binding: The binding sites for the engineered effectors (CRISPRa or KRAB-Zinc Finger proteins) were predicted computationally, but not validated experimentally using techniques like ChIP-seq. Although mapping reads within L1MdTf might be challenging, ChIP-seq could still be informative. It would help define the ratio of on-target vs. off-target binding and elucidate potential off-target effects (binding outside L1MdTf repeats).
2. Mechanism of action: The study somehow assumes that the effectors influence L1MdTf transcription, which then impacts the host transcriptome. However, it is also possible that the engineered effectors directly modulate nearby cis-regulatory elements (promoters or enhancers) due to their proximity to L1MdTf sequences. Further investigation is needed to differentiate between these possibilities.
3. Statistics: The study lacks robust statistical testing in several figures (e.g., Fig. 1B,D; 2C,E; S2; S5C,D). Additionally, the null hypotheses and statistical models used are not explicitly defined. To strengthen the analysis, the authors could quantify the percentage of differentially expressed (DE) or allele-specifically expressed genes associated with targeted L1s compared to non-targeted L1s or other relevant control groups. Furthermore, neuronal genes are known to be longer than average, which can bias enrichment analyses like those performed using DAVID. This increased length makes them more likely to harbor L1 insertions and potentially be affected by the engineered effectors targeting these elements. It would be informative to see how the conclusions change if the null models account for gene size or only consider genes with full-length L1MdTf elements.
4. Allele-specific expression: The analysis of allele-specific expression could be further strengthened by incorporating L1 heterozygosity data. Since the whole genome sequence of these cells is available, calling genotypes for L1 insertions using established pipelines like MELT or others would be a straightforward approach. This would allow the authors to ensure that allele-specific expression patterns are indeed associated with L1 insertional polymorphisms.

Minor comments

1. Western blot analysis could benefit from a more quantitative approach. Analyzing the intensity profiles of the ORF1p bands might help differentiate between potential ORF1p isoforms and pinpoint the specific changes (reduction or increase) in the top band. Additionally, an earlier explanation for the observed doublet band as a consequence of coexisting L1 families would be helpful for readers unfamiliar with mouse L1s.
2. The chromHMM enrichment analysis reports fold enrichments (ratios of observed vs. expected associations with chromatin states). However, the magnitude of these enrichments seems to be modest in most cases. It would be informative to see the actual number of sequences falling into each category for a better understanding of the enrichment patterns.

Significance

Strengths

• This study contributes to a limited body of research exploring the consequences of the global activation or repression of entire transposable element families.
• Notably, the authors achieve this manipulation in a relevant cell type (embryonic stem cells) where retrotransposition is known to occur, utilizing a retrotransposition-competent L1 family (L1MdTf).

Limitations

• While the study offers a relatively novel approach, the biological question addressed could be further refined. This would allow for more specific conclusions regarding the role/consequences of L1MdTf dysregulation.
• Artificially targeting L1 sequences is conceptually similar with randomly targeting the genome for transcriptional effects, since many, possibly most, L1 elements may not be naturally expressed under any biological conditions.

While the manuscript confirms the known potential of L1 sequences to act as cis-regulatory elements, it does not provide significant new insights into the mechanisms underlying their regulatory potential. Notably, a recent study by Tong et al. IJMS (2024) demonstrated the activation of young human L1 elements using CRISPRa. This work similarly confirmed the ability of young human L1 elements to form chimeric transcripts and influence gene expression, likely through promoter or enhancer activity. However, key limitations of both studies are that the strength of the engineered effector might influence the observed transcriptional effects, and that the targeted L1 elements might not be naturally expressed, potentially leading to an overestimation of the regulatory impact of L1 activation.

The study focuses on the impact of L1MdTf on gene expression, but exploring the phenotypic consequences of manipulating its expression could significantly broaden its significance. This would provide valuable insights into the functional impact of L1 activity in a broader context, potentially attracting a wider audience. In this context, L1MdTf silencing in mESC cells which naturally express these elements could be more insightful than artificially over-activating them. Phenotypic analyses could encompass cell cycle progression, commitment to the primed pluripotent state, totipotency, differentiation potential, DNA damage response, or X chromosome inactivation. Identifying whether observed phenotypes arise from cis-effects (on neighboring genes) or trans-effects (mediated by L1 RNA or proteins) would be crucial for understanding the underlying mechanisms.

My field of expertise lies in molecular and cellular biology and genomics, with a particular focus on transposable elements.

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Reply to the reviewers

We sincerely thank all the reviewers for their thoughtful and constructive comments.

In our revision, we have addressed the reviewer's specific criticisms with additional experiments and text edits as described below. We believe the constructive feedback from peer reviews helped us to significantly extend our mechanistic findings and strengthen the manuscript through revision.

Point-by-point description of the revisions

Reviewer #1:

Summary:

The study by Zatulovskiy et al. examined how cell size influences cell susceptibility to ferroptosis. The authors found a size dependence specifically for ferroptosis-inducing drug Era2, but not for other drugs. Using various human cell lines (HMEC, HT 1080, RPE 1), the authors generated populations of small and large G1 cells by FACS, CDK4/6 inhibition (palbociclib), or inducible cyclin D1 knockdown, and measured cell susceptibility to ferroptosis. Larger cells were more resistant than smaller cells. Mechanistically, larger cells showed reduced plasma membrane lipid peroxidation, higher glutathione concentrations, and changes in relevant cellular proteins levels, as analyzed using previously published data. Deleting ACSL4, which is involved in ferroptosis, partly eliminated the size dependence of ferroptosis. The work concludes that cell size is a key determinant of ferroptosis susceptibility.

My major concerns about this work focus on whether many of the results reflect cell size or cell cycle effects, and whether the FACS-based size-scaling analyses have some misleading features to their design & presentation. If these concerns can be addressed with new experiments, then the conclusions of this paper are justified. If these concerns cannot be addressed, then the authors should more directly acknowledge the alternative hypothesis that cell cycle effects may explain many of their results.

The experiments seem to be replicated sufficiently, and most conclusions rely on data from multiple cell lines. My minor comments focus on needs to provide statistics and method details, and on suggestions on how to improve text clarity, but these edits are easily done and don't require new experiments. Overall, this is an interesting study, and it should be published once the concerns below are addressed.

Major comments:

• In experiments reported in Fig 1 and 2A, the authors sort small and large cells in G1, plate them, and later start the drug treatments & cell monitoring. Are these cells actively cycling (progressing in the cell cycle), and how fast? The large cells are likely to enter S phase earlier than the small cells, so by the time that the authors start their drug treatments, they may be comparing cells in different cell cycle stages, which could influence drug sensitivity more than cell size (as the authors also suggest later in Fig 2). This needs to be controlled for. Furthermore, even if the cells remain in G1 after sorting until the drug treatments are started, the authors should address the fact that the drugs are present for a long time, thus targeting the cells in various cell cycle stages.

We agree with the reviewer that the cell cycle stage could affect ferroptosis susceptibility and could be a confounding effect in asynchronous cells. One of us (Dixon) reported the cell cycle effects on ferroptosis previously, and we observe them in this manuscript too (Fig. 2B,C,E). We now state this more clearly both in the Results and in the Discussion sections, where we write:

Line 159: "We note that non-arrested cells had a lower susceptibility to Era2-induced ferroptosis compared to cells that were arrested in G1 for 2-3 days, despite being smaller in size. This is likely due to the difference in the fraction of cells in different cell cycle phases between arrested and non-arrested conditions since cells in S/G2/M phases are known to be more resistant to ferroptosis than cells in G0/G1 phases (Rodencal et al, 2024; Kuganesan et al, 2023)"

Line 533: "Cells in G1 phase of the cell cycle were reported to be more susceptible to ferroptosis (Rodencal et al, 2024; Kuganesan et al, 2023), which suggested that ferroptosis inducers could be used in combination with cancer drugs, like the CDK4/6 inhibitor palbociclib, that arrest cells in G1 phase of the cell cycle (Herrera-Abreu et al, 2024). However, while CDK4/6 inhibitors arrest cells in G1, they do not inhibit cell growth, such that the longer they are arrested, the larger the cells grow (Lanz et al, 2022; Crozier et al, 2023; Manohar et al, 2023). This results in a complex, non-monotonic ferroptotic response dynamics in cells treated with CDK4/6 inhibitors (Fig. 2B,E). Just following CDK4/6 inhibitor treatment, as more and more cells are arrested in G1 phase, cells become more sensitive to both RSL3- and erastin-induced ferroptosis (Kuganesan et al, 2023; Rodencal et al, 2024). However, the longer the cells are arrested, the larger they become, which further promotes their susceptibility to RSL3 (Fig. S1B) but reduces their susceptibility to Era2-induced ferroptosis (Fig. 2B). The fact that the cell cycle arrest and cell size increase have opposing effects on Era2-induced ferroptosis susceptibility could explain why different studies reported seemingly contradictory results, where sometimes an increased and sometimes a decreased or unchanged sensitivity to system xc- inhibitors was observed depending on the cell type, duration and type of cell cycle arrest (Lee et al, 2024; Kuganesan et al, 2023; Rodencal et al, 2024). Such complex interplay between the cell cycle and cell size effects on ferroptosis suggests that combination therapies utilizing CDK4/6 inhibitors and ferroptosis inducers would have to carefully choose a dosage schedule.""

Given the potentially confounding effects of the cell cycle in cycling cells sorted by size, we performed an additional experiment, in which RPE-1 cells were pre-treated with the CDK4/6 inhibitor palbociclib to synchronize them in G1 phase prior to treatment. These cells were then continuously exposed to palbociclib during the Era2 treatment (Fig. 2C-E). RPE-1 cells pre-treated with palbociclib for 2 and 4 days had the same cell cycle distribution with 94% of cells being arrested in G1, but with different sizes. Cells treated with palbociclib for 4 days were significantly larger and more resistant to Era2 as can be seen in the Figure 2C-E.

Additionally, in the experiment shown in Fig. 5E,F, where we FACS-sorted WT and ACSL4 KO HMEC cells by cell size, and then measured Era2 susceptibility, we pre-treated the cells with palbociclib for 24 h to synchronize them in G1 prior to the sorting. We then cultured the cells in the presence of palbociclib during the Era2 treatment to avoid the cell cycle effects observed in Fig. 2. In this case, we still observe that larger cells are more resistant to Era2, consistent with our conclusion that cell size protects against Era2-induced ferroptosis.

Reviewer #1: "Can the G1 arrest-driven changes in drug susceptibility (Fig 2 C-D) be attributed to cell size? Can the authors rescue the palbociclib treatment with rapamycin or other growth inhibitors that allow size to remain small during G1 arrest?"

We have attempted to perform these experiments, but when we co-treated the cells with palbociclib and mTORC inhibitors, but observed variable results, which are likely due to the fact that prolonged mTORC inhibition itself rewires cellular metabolism and reduces cell susceptibility to ferroptosis, as one of us (Dixon) found previously (Armenta et al. (2022), Ferroptosis inhibition by lysosome-dependent catabolism of extracellular protein. Cell Chemical Biology 29: 1588-1600.e7). Our results were consistent with this previous report and is now included in a new supporting figure panel (Fig. S3C).

Thus, upon palbociclib+rapamycin co-treatment there seems to be a competition between cell-size-mediated and metabolism-mediated effects of mTORC inhibition on ferroptosis, which leads to variable outcomes.

Reviewer #1: "In Fig 2E-F, is the cell cycle distribution of the samples influenced by CCND1 shRNA induction? Are the drug sensitivity effects due to cell size or cell cycle changes?"

The CCND1 manipulation model is extensively characterized in our recent work cited in this manuscript (You et al. (2025), Cell size-dependent mRNA transcription drives proteome remodeling. 2025.10.30.685141 doi:10.1101/2025.10.30.685141). Indeed, CCND1 shRNA cells have a slightly elongated G1 phase due to a ~30% reduction in Cyclin D1 concentration: the G1 fraction changes from ~70% in wild-type to ~80% in CCND1 shRNA cells, which could potentially affect the ferroptosis susceptibility, but the additional results obtained on synchronized RPE-1 cells, described above (Fig. 2C-E), support the conclusion that the primary effect on Era2 sensitivity is due to cell size.

Reviewer #1: "Can the authors address the meaningfulness of the FACS-based size-scaling results in cases where cell-to-cell variability is very large? For example, in Fig 4D&G, the results are so variable even in identically sized cells that the importance of the size-scaling pattern seems questionable."

We do observe variability in fluorescent probe-based measurements of GSH and lipid oxidation, which could be due to biological (natural cell heterogeneity) and/or technical (low sensitivity of the probes) reasons. However, when we look at binned data and compare the mean values {plus minus} s.e.m. for each bin, we observe a robust and reproducible trend (black line with dark-grey shaded area), even though the SD is quite broad (lighter shaded area). We believe such trends are meaningful when describing cell death in probabilistic terms as we do. I.e., the GSH measurement might not be precise enough to predict cell death for a given individual cell, but the statistical trend is clear and these measurements help predict cell death probabilities for cells of different sizes.

Reviewer #1: "In Figs 4B-D, the cell size axis seems to have over 4-fold size variability, but when the authors show the analysis of this data (Figs 4E-G) the variability is only 2-fold. What was excluded and on what basis?"

To address this point, we have now clarified in the Methods section how the data were processed and what data points we excluded from this analysis:

Line 671: "For all binned flow cytometry data plots, the cells below the 2nd and above the 98th cell size percentiles were excluded to remove the extreme outliers. Then, the remaining data were binned by size and plotted as background-corrected average fluorescence intensity for each bin against the bin's average cell size. Bins with fewer than 200 cells were excluded from the analysis to reduce noise."

Typically, such pre-processing reduces the size range, mostly from the large-cell end, because of the long right tail of the size distribution containing a few very large cells.

Reviewer #1: "Based on the methods section & figure legends of Fig 4B-I, the RPE cells were not pre-sorted to include only G1 cells, nor did the assay account for cell cycle differences. How can these data be used to explain results from earlier figures, where analyses were exclusively focused on size differences in G1?"

This is a valid point: Cells in the GSH measurement experiment were not gated by Hoechst signal for G1 phase because the channel normally used for Hoechst staining was in this case occupied by the MCB probe. However, given the data in Fig. 4A,B showing that the GSH production machinery is superscaling when measured specifically in G1-phase cells, we believe the flow cytometry data in Fig. 4C-J showing GSH concentration increasing with cell size across the whole cell cycle is very likely true for G1 cells as well.

Reviewer #1: "Minor comments:

I recommend clarifying in the early introduction that all size changes discussed are in the absence of DNA content increase."

We have now clarified this in the introduction (Line 41 and Line 81).

Reviewer #1: "The introduction seems to cite primary research and review paper in the same sentences, which is a bit misleading as the reviews don't seem to add new evidence."

We have removed review citations where they did not provide additional context.

Reviewer #1: "*OPTIONAL* In the second introduction paragraph, consider the classification/description of the three different mechanisms. Currently, it seems that these mechanisms are not independent of each other, and the details provided about each mechanism are inconsistent."

We have now modified this paragraph to make the description more consistent.

Reviewer #1: "Please provide statistics for the IC50 values reported based on Fig 1C. Were small and large cells statistically different? Are the IC50 values reported as +/- standard deviation or some other metric?"

This has now been clarified in the text as follows:

"For example, at the 72 h time point, the Era2 IC50 was 28 {plus minus} 11 µM (mean {plus minus} SD) for large cells versus 2.0 {plus minus} 1.4 µM for small cells (Student's t-test: p = 0.039) (Fig. 1C)."

Reviewer #1: "*OPTIONAL* Providing more insight into why Era2 and RSL3 treatments yield more opposite responses would be of great interest to the field."

We agree this is an important point that should be discussed in more detail. In the field of ferroptosis, context-dependent (i.e., cell type-specific) effects are common and multiple groups including our own (Dixon) have published extensively on genes and mechanisms that can lead to differences between erastin2 and RSL3 sensitivity. For example, there are studies showing that the mTOR pathway or the p53 pathway can either prevent or promote ferroptosis, depending on the cell type and/or other currently unknown variables. To address more specifically the differences between Era2 and RSL3 in the context our observed cell-size-dependent response, we have now added more data and discussion. In the Results section we added panel 4B and the following text:

Line 359: "While the upregulation of GSH biosynthesis may promote the resistance of larger cells to ferroptosis, such an upregulation alone cannot explain why larger cells become more resistant to ferroptosis induced by the cystine import inhibitor Era2, but not, for example, by the GPX4 inhibitor RSL3 (Chan et al, 2025) (Figs. 2B, S1B). We found previously that upon mTORC1 inhibition cells can evade cystine deprivation-induced ferroptosis by uptake and catabolism of cysteine-rich extracellular proteins, mostly albumin (Armenta et al, 2022) (Fig. S3C). This process involves albumin degradation in lysosomes, predominantly by cathepsin B (CatB), and subsequent export of cystine from lysosomes to fuel the synthesis of glutathione. Large cells undergo proteome rearrangements similar to those occurring upon mTORC1 inhibition (Zatulovskiy et al, 2022). This suggests that large cells may upregulate CatB expression to bypass the Era2-induced cystine import inhibition via system xc-. To test this hypothesis, we used flow cytometry to measure how the expression of cathepsin B and the system xc- cystine/glutamate transporter SLC7A11 (xCT) scales with cell size (Fig. 4B). We found that SLC7A11 concentration modestly decreases, while CatB concentration significantly increases with cell size (Fig. 4B). This shift in the ratio between SLC7A11 and CatB supports the hypothesis that larger cells may rely less on cystine import via system xc- and thus become more resistant to system xc- inhibition by Era2."

Additionally, in the Discussion we added the following:

Line 578: "We show that large cells may become resistant specifically to Era2 but not RSL3 through the upregulation of lysosomal function, particularly cathepsin B expression, which enables the uptake and catabolism of cysteine-rich extracellular proteins. A size-dependent shift in the ratio between SLC7A11 and cathepsin B makes large cells less dependent on cystine import via system xc-, and thus, more resistant to Era2. In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

Reviewer #1: "Is the BODIPY-C11 labeling specific to plasma membrane, as suggested by the writing of the authors, or do the results shown integrate signals over all cell membranes?"

We thank the reviewer for pointing this out. BODIPY-C11 581/591 stains many membranes in the cell, not just the plasma membrane. We have changed the wording in the manuscript to reflect this.

Reviewer #1: "How exactly is gating done for the flow cytometry samples? Especially when analyzing size-scaling, the results are likely to be sensitive to outliers, such as those seen in Fig 4C (a subpopulation of very low CFSE stained cells). Can the authors clarify their methods and/or display supplementary figures with gating examples?"

We have now specified our gating strategy in the Methods section (Line 663) and added a corresponding Supplementary Figure S5:

"Single cells were gated based on FSC-A vs SSC-A, then FSC-A vs FSC-H, then SSC-A vs SSC-W plots. From this population of single cells, G1 cells were selected using Hoechst-A vs FSC-A plot for subsequent scaling analysis"

Reviewer #1: "In Fig 4, total protein staining was used as a control, whereas Fig 5B b-actin was used as a control. Why did the authors rely on different controls approaches for essentially the same measurements? Are these controls comparable?"

In our flow cytometry experiments, we consistently use live-cell total protein stain (CFSE) for live cells, and anti-Tubulin immunofluorescent staining for fixed cells, both of which scale in proportion to cell volume and act as a read-out for total cellular protein content (Lanz and Zatulovskiy et al., Mol Cell 2022; Berenson et al. MBoC 2019), which we use to calculate concentrations of other cellular components (analogous to loading controls). In Fig. 5B, beta-Actin is used as a reference - a protein whose concentration does not change with cell size, as opposed to ACSL4 whose concentration decreases with cell size. In this plot, both ACSL4 and beta-Actin amounts were normalized to alpha-Tubulin, which is analogous to a concentration calculation using loading control. This is now explained in more detail in the Figure legend.

Reviewer #2:

"Zatulovskiy et al. demonstrate that cell size modulates susceptibility to ferroptosis, a form of iron-dependent cell death driven by lipid peroxidation. Using human cell lines (HMEC, HT-1080, RPE-1), the authors examined cell size through FACS sorting, CDK4/6 inhibition and inducible cyclin D1 knockdown. They found that larger cells are more resistant to ferroptosis induced by system xc⁻ inhibition (erastin2), but more sensitive to GPX4 inhibition (RSL3), highlighting pathway-specific size dependencies.

Mechanistically, larger cells exhibited:

• Higher glutathione levels, supporting lipid peroxide detoxification
• Increased ferritin expression, promoting iron sequestration
• Lower ACSL4 levels, reducing incorporation of peroxidation-prone lipids These findings were supported by high-throughput microscopy, flow cytometry (BODIPY-C11 lipid peroxidation assays), and proteomic analyses. The study concludes that cell size influences proteome composition and metabolic capacity, thereby shaping cell death decisions, an insight with implications for aging, cancer, and ferroptosis-based therapies.

Major Comments

1. Direct evaluation of SLC7A11 abundance and function is needed The opposite size-dependent effects of erastin2 and RSL3 strongly suggest a role for SLC7A11/system xc⁻ activity in size-dependent ferroptosis resistance. However, SLC7A11 levels were not quantified due to insufficient peptide detection in the proteomic data.

o Direct measurement of SLC7A11 protein levels (immunoblotting or flow cytometry) in small vs large cells would test whether its expression scales with size.

o Functional perturbation (siRNA/CRISPR knockdown) followed by erastin2 treatment would provide mechanistic validation.

o Use of additional SLC7A11 inhibitors (e.g., sulfasalazine, sorafenib) could further test whether the size resistance phenotype is xc⁻-specific."

We agree that the difference in size-dependent responses to RSL3 and Era2 is an important point that needs further investigation and discussion, as other reviewers also pointed out. To address more specifically the differences between Era2 and RSL3 in the context of cell-size-dependent response, we have now added more data and discussion. In the Results section we added panel 4B measuring SLC7A11 and Cathepsin B scaling with cell size and the following text:

Line 359: "While the upregulation of GSH biosynthesis may promote the resistance of larger cells to ferroptosis, such an upregulation alone cannot explain why larger cells become more resistant to ferroptosis induced by the cystine import inhibitor Era2, but not, for example, by the GPX4 inhibitor RSL3 (Chan et al, 2025) (Figs. 2B, S1B). We found previously that upon mTORC1 inhibition cells can evade cystine deprivation-induced ferroptosis by uptake and catabolism of cysteine-rich extracellular proteins, mostly albumin (Armenta et al, 2022) (Fig. S3C). This process involves albumin degradation in lysosomes, predominantly by cathepsin B (CatB), and subsequent export of cystine from lysosomes to fuel the synthesis of glutathione. Large cells undergo proteome rearrangements similar to those occurring upon mTORC1 inhibition (Zatulovskiy et al, 2022). This suggests that large cells may upregulate CatB expression to bypass the Era2-induced cystine import inhibition via system xc-. To test this hypothesis, we used flow cytometry to measure how the expression of cathepsin B and the system xc- cystine/glutamate transporter SLC7A11 (xCT) scales with cell size (Fig. 4B). We found that SLC7A11 concentration modestly decreases, while CatB concentration significantly increases with cell size (Fig. 4B). This shift in the ratio between SLC7A11 and CatB supports the hypothesis that larger cells may rely less on cystine import via system xc- and thus become more resistant to system xc- inhibition by Era2."

Additionally, in the Discussion we added the following:

Line 578: "We show that large cells may become resistant specifically to Era2 but not RSL3 through the upregulation of lysosomal function, particularly cathepsin B expression, which enables the uptake and catabolism of cysteine-rich extracellular proteins. A size-dependent shift in the ratio between SLC7A11 and cathepsin B makes large cells less dependent on cystine import via system xc-, and thus, more resistant to Era2. In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

Reviewer #2: "2. Functional tests of ferritin contribution to resistance are needed

Although elevated ferritin (FTH1/FTL) levels in larger cells represent a strong correlational signal, definitive experimental evidence establishing causality is currently lacking.

o Measuring the labile iron pool directly in size-stratified populations would strengthen the link.

o Knockdown of FTH1 or FTL could reveal whether ferritin upregulation is necessary for the resistance of large cells to ferroptosis."

We thank the reviewer for raising this point. We have now completed additional experiments, as suggested by the reviewer, and found that iron chelation is unlikely to mediate the size-dependent response to Era2. We have modified the manuscript accordingly and added the following data and discussion to address this point:

Line 296: "The observed increase in ferritin concentration with cell size could therefore lead to additional Fe2+ ion chelation, which in turn would protect large cells from iron-dependent lipid peroxidation and ferroptosis. However, when we measured the concentration of labile intracellular Fe2+ using a fluorescent probe FerroOrange (Hirayama et al, 2020), we did not observe any size-dependent decrease in labile iron concentration (Fig. S2A). Previous work suggests a link between increased sequestration of ferrous iron in lysosomes and resistance to ferroptosis. It was reported that senescent cells, which are also large (Fig. S3A,B), gain resistance to ferroptosis through lysosomal alkalinization and sequestration of ferrous iron in lysosomes (Loo et al, 2025). We therefore tested whether the superscaling of lysosomes observed in large cells (Lanz et al, 2022; You et al, 2025) promotes Era2 resistance through lysosomal iron sequestration. To do this, we stained the cells with the lysosomal iron detection probe Lyso-FerroRed (Saimoto et al, 2025) and measured its scaling using flow cytometry (Fig. S2B). We observed that the amount of Lyso-FerroRed, and therefore, the amount of lysosomal iron, scaled in direct proportion to cell size, just like the total cellular protein content (Fig. S2B). These results indicate that iron chelation by ferritin and its sequestration in lysosomes are unlikely to play a crucial role in size-dependent decrease in Era2 sensitivity."

Reviewer #2: "3. Relevance to senescence should be addressed experimentally or explicitly discussed

Given that senescent cells are enlarged and accumulate in aged and tumour tissues, testing senescent models for erastin2 resistance would greatly strengthen the physiological significance."

We agree that an increase in cell size contributing to the resistance of senescent cells to ferroptosis is intriguing. We have now added a Supplementary Figure S3 and discussion of this point in the manuscript as follows:

Discussion line 552: "our data suggest that previously reported resistance of senescent cells to ferroptosis can at least partially be due to the increased cell size, a well-established hallmark of senescence."

Reviewer #2: "Minor Comments

1. Mechanistic nuance regarding RSL3 should be included RSL3 has been reported to induce ferroptosis independently of GPX4 (PMID: 37087975, PMID: 40392234) and may target other selenoproteins such as TXNRD1. This nuance would help explain the observed divergence between RSL3 and erastin2 sensitivity across sizes."

We have now added this in the Discussion as suggested by the reviewer (line 583):

"In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

Reviewer #2: "2. Dynamic range of BODIPY-C11 assays needs commentary

Despite high erastin2 doses, the oxidized BODIPY signal remains close to DMSO levels. The authors should comment on whether this reflects high GSH buffering capacity, probe limitations, or other factors."

We believe there are both technical (narrow dynamic range of the probe) and biological reasons for the relatively small (2-3 fold) difference in Oxidized-to-Non-oxidized BODIPY-C11 ratios between DMSO and Era2-treated cells. The biological reason is that the cells continue producing GSH until they fully deplete the cystine pool, which happens ~20-24 h after Era2 addition. Once the cystine pool is depleted, the cells very rapidly deplete GSH and initiate cell death. Therefore, there is only a short time window where cells are strongly depleted of GSH before dying. We see this small fraction of cells with a high Oxidized BODIPY-C11 signal in our flow cytometry experiments and in previous microscopy analysis of BODIPY-C11 (Murray et al., Protocol for detection of ferroptosis in cultured cells. STAR Protoc. 2023), but at our chosen time point (20h Era2) most cells are not as bright because we aimed to analyze the population before the onset of widespread cell death.

Reviewer #2: "3. Western blot for shCycD1 depletion should be included

CycD1 depletion usually causes cells to stop proliferating, which is not the case here. Therefore, depletion must be partial. The level of depletion should be shown by immunblotting."

The CCND1 manipulation model is extensively characterized in our recent work cited in this manuscript (You et al. (2025), Cell size-dependent mRNA transcription drives proteome remodeling. 2025.10.30.685141 doi:10.1101/2025.10.30.685141). CCND1 shRNA cells do not fully arrest in G0/G1 because the concentration of Cyclin D1 protein in this system is only partially decreased, as the reviewer noted. As a result, the cells have a slightly elongated G1 phase due to a ~30% reduction in Cyclin D1 concentration, but continue to proliferate. The G1 fraction changes from ~70% in wild-type to ~80% in CCND1 shRNA cells.

Reviewer #3:

"In this manuscript, Zatulovskiy and colleagues elaborate on their previous work describing cell size-dependent changes in the proteome by investigating whether these changes can be correlated in differences in cell physiology. Using a cleverly-designed high throughput screen, they searched for compounds that differently-sized cells display differential sensitivity towards. Their primary hit, Era2, is involved in the ferroptosis pathway and serves as the starting point for a detailed study of how excess cell size protects cells from ferroptosis-induced cell death via: 1) lower concentrations of ACSL4 (which produces peroxidation-prone PUFAs), 2) increased ferritin concentrations, and 3) increased GSH concentrations.

Overall, the experiments in this manuscript are well-designed and interpreted. It is an extremely well-written manuscript with a clear trajectory of logic. I have only a few major concerns that should be addressed before publication:"

We thank Reviewer #3 for their careful reading of the manuscript and for the clear summary of our study and its central findings. We appreciate their positive assessment of the experimental design, interpretation, and overall clarity of the writing and logical flow. We are also grateful for their constructive feedback and take their major concerns seriously; we have addressed each point in detail below.

Reviewer #3: "Major concerns:

1) In Figure 3E, the authors gate their flow cytometry data using SYTOX so that they are only analyzing live cells. Based on their gating scheme, it seems like there are really a lot of dead cells. Presumably the cells that died were the most sensitive to Era2, so it seems an oversight to discard these cells. Of course, it is not appropriate to analyze dead cells, but this could potentially be solved by using a shorter treatment duration than 24 hours wherein fewer cells die."

This is a good point. To address it, we have now replaced this panel with a time point where most cells are still alive (20 h, 0.2 µM Era2), as suggested by the reviewer (Fig. 3E,F). This did not change the conclusion that BODIPY-C11 oxidation decreases with cell size.

Reviewer #3: "2) In Figure 5, are the small, medium, and large bins for ACSL4 KO cells the same as for WT cells? If the ACSL4 KO cells are just bigger to begin with, this could explain why the "small" bin has greater cell survival than the WT small bin. Moreover, is the overlap between the three bins the same in the WT and KO cells?"

This is an important point that we now address with data shown in Fig. S4B. We have now added a Supplementary Figure S4B to show the relative size of small, medium, and large WT and ACSL4 KO HMEC cells. As seen from this graph, the ACSL4 KO cells are not bigger than WT cells. Importantly, the fold-range between the small and large FACS-sorted cells is similar (~1.9 to 2-fold).

Reviewer #3: "3) Loo, et al. Nat Comms 2025 similarly found that senescent cells (which are enlarged) are resistant to ferroptosis using the same inhibitor as the authors. In contrast to the authors, they show that this is due to lysosomal alkalinization and sequestration of ferrous iron in lysosomes. Given that Lanz et al. 2022 found that lysosomal components super-scale with cell size, it seems like this would be an important hypothesis to address. Free lysosomal iron can be easily measured with the LysoRhoNox stain. Loo et al. was able to restore ferroptosis sensitivity in senescent cells using the V-ATPase activator EN6, so it would be important for the authors to address whether this (or similar) treatment would have the same effect in enlarged cells."

This is an excellent point. We have now performed this experiment and added it to the manuscript, as suggested by the reviewer. Based on the Lyso-FerroRed staining (another brand name for the LysoRhoNox probe), we do not see an increase in lysosomal iron sequestration in large cells (Fig. S2B) - see the graph and the corresponding discussion below:

Line 301: "Previous work suggests a link between increased sequestration of ferrous iron in lysosomes and resistance to ferroptosis. It was reported that senescent cells, which are also large (Fig. S3A,B), gain resistance to ferroptosis through lysosomal alkalinization and sequestration of ferrous iron in lysosomes (Loo et al, 2025). We therefore tested whether the superscaling of lysosomes observed in large cells (Lanz et al, 2022; You et al, 2025) promotes Era2 resistance through lysosomal iron sequestration. To do this, we stained the cells with the lysosomal iron detection probe Lyso-FerroRed (Saimoto et al, 2025) and measured its scaling using flow cytometry (Fig. S2B). We observed that the amount of Lyso-FerroRed, and therefore, the amount of lysosomal iron, scaled in direct proportion to cell size, just like the total cellular protein content (Fig. S2B). These results indicate that iron chelation by ferritin and its sequestration in lysosomes are unlikely to play a crucial role in size-dependent decrease in Era2 sensitivity."

Reviewer #3: "Minor concerns:

1) It would be helpful if this manuscript were re-submitted with line numbers to more easily reference the text."

We have added line numbers for convenience.

Reviewer #3: "2) In Figure 5A and other figures that reproduce data from Lanz et al. 2022, it would be helpful to have a summary curve for the overall abundance of each protein rather than only the individual peptide curves. These plots (particularly Figure 5A) are difficult to interpret since some peptides were presumably more abundant / measured with higher confidence than others."

We have added the average ACSL4 protein slope line to Fig. 5A.

Reviewer #3: "3) In Figure 5, the authors show the validation of the ACSL4 KO HT-1080 cell line but not HMEC, even though both are used in this figure. It would be useful to show both. Additionally, the authors switch back and forth between the two cell lines for this figure, and it is not clear why."

We have added the HMEC ACSL4 KO validation Western blot in Fig. S4A (see below).

For the BODIPY oxidation experiment (Fig. 5D), we used HT-1080 instead of HMEC because HT1080 cells are sensitive to lower concentrations of Era2, and therefore, we could better optimize the Era2 concentrations and treatment durations to measure BODIPY oxidation at the time point when most cells are still alive but demonstrate a pronounced oxidized BODIPY signal.

Reviewer #3: "4) In Figure 5B, the authors use antibody-based staining of ACSL4 and flow cytometry to correlate a loss of ACSL4 expression with increased cell size, validating the proteomics data in Figure 5A. This does not seem like a good way to do this. Firstly, fixing cells with formaldehyde alters their size (is this proportional across differently sized cells? It's impossible to know), which makes it inappropriate to use SSC as a proxy for size in this particular situation. Secondly, the normalization scheme here doesn't make sense. If actin was used as a reference protein, why was tubulin used to normalize ACSL4 abundance? Overall, this seems like a very round-about experiment that could have just been addressed by doing a simple western blot with the four size bins sorted from live cells (as it was in the proteomics). If the issue is that ACSL4 is not detectable by western in the HMEC cells, another solution would be plating the live, sorted bins on coverslips and measuring by IF (or using the HT-1080 cells)."

We prefer IF flow cytometry to Western blotting for protein scaling analysis because it is more quantitative and provides cell size and protein content information for each individual cell. While in principle, different-sized cells might change their size differently during fixation, the cells that were larger or smaller prior to the fixation remain larger or smaller after fixation as well. Therefore, the SSC measurement after fixation still provides reliable information on size ranking, even if SSC does not perfectly linearly scale with cell volume. We do not use the SSC information to calculate protein concentrations here. Instead, we divide the amount of our protein of interest in the cell by the amount of constitutively-expressed Tubulin, which acts as an analogue of a loading control in this experiment. In Fig. 5B, both ACSL4 and Actin were normalized to Tubulin to estimate their concentrations. Actin is used just as a reference protein to show how the concentration of a perfectly scaling protein remains constant across cell size, as opposed to the sub-scaling ACSL4. Tubulin in this case was used as a proxy for total cellular protein content, which scales linearly in proportion to cell volume. This approach for determining the scaling behaviors of different proteins was previously validated in Lanz et al., Mol Cell 2022.

Reviewer #3: "5) In Figure 5E/5F, the authors pre-arrest the cells in G1 with palbociclib before size-sorting them. The pre-arrest is not done in other experiments using this cell line for size-sorting, so it would be important for the authors to comment on why this was done for this experiment but not others."

As we found in Fig. 2B-E, the cell cycle has confounding effects on size-dependent ferroptosis susceptibility measurements (as discussed in detail in our response to the first major point of Reviewer #1 above). Briefly, to avoid these confounding effects and isolate the effects of cell size from the effects of the cell cycle, we pre-synchronized the cells with 24 h treatment with palbociclib in Fig. 5E,F. This is now better clarified in the text, as follows:

Line 456: "In this experiment, we synchronized cells in G1 phase using palbociclib prior to cell sorting and also incubated the sorted cells in the presence of palbociclib during Era2 treatment to isolate cell size effects from the previously observed confounding effects of the cell cycle on ferroptosis (Fig. 2B,E)."

Reviewer #3: "6) Conceptually, it is difficult for me to understand why large cell size sensitizes cells to GPX4 inhibition but confers resistance to Era2 treatment. Particularly given the pathway described in Figure 3A, I am having trouble understanding why these would convey such opposing phenotypes. Shouldn't the extra ferritin in the bigger cells also help them cope with GPX4 inhibition if, as the authors state in the discussion, the increased sensitivity to the GPX4 inhibitor is reported to be mediated by (among other things) iron accumulation? A deeper discussion of this seeming-incongruity would be helpful for contextualizing the broader role of cell size in determining ferroptosis sensitivity."

We agree this is an important point, which was also raised by the other reviewers. As such, we note that context-dependent (i.e., cell type-specific) effects are common in the ferroptosis field, and multiple groups including our own (Dixon) have published extensively on genes and mechanisms that can lead to differences between erastin2 and RSL3. For example, there are studies showing that the mTOR pathway or the p53 pathway can both prevent and promote ferroptosis, depending on the cell type or some other hidden variable.

To better address the differences between Era2 and RSL3 in the context of the cell-size-dependent response, we have now added more data and discussion. In the Results section we added panel 4B and the following text:

Line 359: "While the upregulation of GSH biosynthesis may promote the resistance of larger cells to ferroptosis, such an upregulation alone cannot explain why larger cells become more resistant to ferroptosis induced by the cystine import inhibitor Era2, but not, for example, by the GPX4 inhibitor RSL3 (Chan et al, 2025) (Figs. 2B, S1B). We found previously that upon mTORC1 inhibition cells can evade cystine deprivation-induced ferroptosis by uptake and catabolism of cysteine-rich extracellular proteins, mostly albumin (Armenta et al, 2022) (Fig. S3C). This process involves albumin degradation in lysosomes, predominantly by cathepsin B (CatB), and subsequent export of cystine from lysosomes to fuel the synthesis of glutathione. Large cells undergo proteome rearrangements similar to those occurring upon mTORC1 inhibition (Zatulovskiy et al, 2022). This suggests that large cells may upregulate CatB expression to bypass the Era2-induced cystine import inhibition via system xc-. To test this hypothesis, we used flow cytometry to measure how the expression of cathepsin B and the system xc- cystine/glutamate transporter SLC7A11 (xCT) scales with cell size (Fig. 4B). We found that SLC7A11 concentration modestly decreases, while CatB concentration significantly increases with cell size (Fig. 4B). This shift in the ratio between SLC7A11 and CatB supports the hypothesis that larger cells may rely less on cystine import via system xc- and thus become more resistant to system xc- inhibition by Era2."

Figure 4. (B) Flow-cytometry-based measurement of cystine/glutamate transporter SLC7A11 (xCT) and cathepsin B (CatB) concentrations in G1-phase RPE-1 cells demonstrates a modest decrease in SLC7A11 and a significant increase in Cathepsin B concentrations with cell size. To calculate the concentrations of SLC7A11 and CatB, their amounts were measured with flow cytometry using immunofluorescence and normalized to the amounts of α-Tubulin. The data were binned by cell size, and mean values for each bin were plotted against normalized cell size (solid blue line for SLC7A11 and red line for CatB). Shaded areas denote the s.e.m. for each bin.

Additionally, in the Discussion we added the following:

Line 578: "We show that large cells may become resistant specifically to Era2 but not RSL3 through the upregulation of lysosomal function, particularly cathepsin B expression, which enables the uptake and catabolism of cysteine-rich extracellular proteins. A size-dependent shift in the ratio between SLC7A11 and cathepsin B makes large cells less dependent on cystine import via system xc-, and thus, more resistant to Era2. In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Zatulovskiy and colleagues elaborate on their previous work describing cell size-dependent changes in the proteome by investigating whether these changes can be correlated in differences in cell physiology. Using a cleverly-designed high throughput screen, they searched for compounds that differently-sized cells display differential sensitivity towards. Their primary hit, Era2, is involved in the ferroptosis pathway and serves as the starting point for a detailed study of how excess cell size protects cells from ferroptosis-induced cell death via: 1) lower concentrations of ACSL4 (which produces peroxidation-prone PUFAs), 2) increased ferritin concentrations, and 3) increased GSH concentrations.

Overall, the experiments in this manuscript are well-designed and interpreted. It is an extremely well-written manuscript with a clear trajectory of logic. I have only a few major concerns that should be addressed before publication:

Major concerns:

1) In Figure 3E, the authors gate their flow cytometry data using SYTOX so that they are only analyzing live cells. Based on their gating scheme, it seems like there are really a lot of dead cells. Presumably the cells that died were the most sensitive to Era2, so it seems an oversight to discard these cells. Of course, it is not appropriate to analyze dead cells, but this could potentially be solved by using a shorter treatment duration than 24 hours wherein fewer cells die.

2) In Figure 5, are the small, medium, and large bins for ACSL4 KO cells the same as for WT cells? If the ACSL4 KO cells are just bigger to begin with, this could explain why the "small" bin has greater cell survival than the WT small bin. Moreover, is the overlap between the three bins the same in the WT and KO cells?

3) Loo, et al. Nat Comms 2025 similarly found that senescent cells (which are enlarged) are resistant to ferroptosis using the same inhibitor as the authors. In contrast to the authors, they show that this is due to lysosomal alkalinization and sequestration of ferrous iron in lysosomes. Given that Lanz et al. 2022 found that lysosomal components super-scale with cell size, it seems like this would be an important hypothesis to address. Free lysosomal iron can be easily measured with the LysoRhoNox stain. Loo et al. was able to restore ferroptosis sensitivity in senescent cells using the V-ATPase activator EN6, so it would be important for the authors to address whether this (or similar) treatment would have the same effect in enlarged cells.

Minor concerns:

1) It would be helpful if this manuscript were re-submitted with line numbers to more easily reference the text.

2) In Figure 5A and other figures that reproduce data from Lanz et al. 2022, it would be helpful to have a summary curve for the overall abundance of each protein rather than only the individual peptide curves. These plots (particularly Figure 5A) are difficult to interpret since some peptides were presumably more abundant / measured with higher confidence than others.

3) In Figure 5, the authors show the validation of the ACSL4 KO HT-1080 cell line but not HMEC, even though both are used in this figure. It would be useful to show both. Additionally, the authors switch back and forth between the two cell lines for this figure, and it is not clear why.

4) In Figure 5B, the authors use antibody-based staining of ACSL4 and flow cytometry to correlate a loss of ACSL4 expression with increased cell size, validating the proteomics data in Figure 5A. This does not seem like a good way to do this. Firstly, fixing cells with formaldehyde alters their size (is this proportional across differently sized cells? It's impossible to know), which makes it inappropriate to use SSC as a proxy for size in this particular situation. Secondly, the normalization scheme here doesn't make sense. If actin was used as a reference protein, why was tubulin used to normalize ACSL4 abundance? Overall, this seems like a very round-about experiment that could have just been addressed by doing a simple western blot with the four size bins sorted from live cells (as it was in the proteomics). If the issue is that ACSL4 is not detectable by western in the HMEC cells, another solution would be plating the live, sorted bins on coverslips and measuring by IF (or using the HT-1080 cells).

5) In Figure 5E/5F, the authors pre-arrest the cells in G1 with palbociclib before size-sorting them. The pre-arrest is not done in other experiments using this cell line for size-sorting, so it would be important for the authors to comment on why this was done for this experiment but not others.

6) Conceptually, it is difficult for me to understand why large cell size sensitizes cells to GPX4 inhibition but confers resistance to Era2 treatment. Particularly given the pathway described in Figure 3A, I am having trouble understanding why these would convey such opposing phenotypes. Shouldn't the extra ferritin in the bigger cells also help them cope with GPX4 inhibition if, as the authors state in the discussion, the increased sensitivity to the GPX4 inhibitor is reported to be mediated by (among other things) iron accumulation? A deeper discussion of this seeming-incongruity would be helpful for contextualizing the broader role of cell size in determining ferroptosis sensitivity.

Significance

Strengths: well-designed study, clear results that are broadly in line with other recent studies on the same topic.

Limitations: opposing results between Era2 and GPX4i (which should in theory cause similar phenotypes) call into question how broadly cell size impacts ferroptosis susceptibility / indicate that this may occur in a limited context

Advances: first study to show that enlarged cells might have higher antioxidant capacity

Audiences: cell size researchers, ferroptosis/cell death researchers

My expertise: cell cycle checkpoints, cell size control, proteomics

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Referee #2

Evidence, reproducibility and clarity

Zatulovskiy et al. demonstrate that cell size modulates susceptibility to ferroptosis, a form of iron-dependent cell death driven by lipid peroxidation. Using human cell lines (HMEC, HT-1080, RPE-1), the authors examined cell size through FACS sorting, CDK4/6 inhibition and inducible cyclin D1 knockdown. They found that larger cells are more resistant to ferroptosis induced by system xc⁻ inhibition (erastin2), but more sensitive to GPX4 inhibition (RSL3), highlighting pathway-specific size dependencies. Mechanistically, larger cells exhibited:

• Higher glutathione levels, supporting lipid peroxide detoxification
• Increased ferritin expression, promoting iron sequestration
• Lower ACSL4 levels, reducing incorporation of peroxidation-prone lipids

These findings were supported by high-throughput microscopy, flow cytometry (BODIPY-C11 lipid peroxidation assays), and proteomic analyses. The study concludes that cell size influences proteome composition and metabolic capacity, thereby shaping cell death decisions, an insight with implications for aging, cancer, and ferroptosis-based therapies.

Major Comments

1. Direct evaluation of SLC7A11 abundance and function is needed The opposite size-dependent effects of erastin2 and RSL3 strongly suggest a role for SLC7A11/system xc⁻ activity in size-dependent ferroptosis resistance. However, SLC7A11 levels were not quantified due to insufficient peptide detection in the proteomic data.
   • Direct measurement of SLC7A11 protein levels (immunoblotting or flow cytometry) in small vs large cells would test whether its expression scales with size.
   • Functional perturbation (siRNA/CRISPR knockdown) followed by erastin2 treatment would provide mechanistic validation.
   • Use of additional SLC7A11 inhibitors (e.g., sulfasalazine, sorafenib) could further test whether the size resistance phenotype is xc⁻-specific.
2. Functional tests of ferritin contribution to resistance are needed Although elevated ferritin (FTH1/FTL) levels in larger cells represent a strong correlational signal, definitive experimental evidence establishing causality is currently lacking.
   • Measuring the labile iron pool directly in size-stratified populations would strengthen the link.
   • Knockdown of FTH1 or FTL could reveal whether ferritin upregulation is necessary for the resistance of large cells to ferroptosis.
3. Relevance to senescence should be addressed experimentally or explicitly discussed Given that senescent cells are enlarged and accumulate in aged and tumour tissues, testing senescent models for erastin2 resistance would greatly strengthen the physiological significance.

Minor Comments

1. Mechanistic nuance regarding RSL3 should be included RSL3 has been reported to induce ferroptosis independently of GPX4 (PMID: 37087975, PMID: 40392234) and may target other selenoproteins such as TXNRD1. This nuance would help explain the observed divergence between RSL3 and erastin2 sensitivity across sizes.
2. Dynamic range of BODIPY-C11 assays needs commentary Despite high erastin2 doses, the oxidized BODIPY signal remains close to DMSO levels. The authors should comment on whether this reflects high GSH buffering capacity, probe limitations, or other factors.
3. Western blot for shCycD1 depletion should be included CycD1 depletion usually causes cells to stop proliferating, which is not the case here. Therefore, depletion must be partial. The level of depletion should be shown by immunblotting.

Are the suggested experiments realistic in terms of time and resources? Yes, measuring SLC7A11 expression (£400, 2 days) and knocking down SLC7A11 and FTL/FTH1 (£1000, 1-2 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? Number of replicates are adequate. The different statistical analyses performed should be mentioned.

Referee cross-commenting

It seems that all reviewers are largely in agreement. Key things to focus on in a revised version are:

• Clarifying the pathway to better explain why different ferroptosis inducers show opposite phenotypes.
• Dependency of effects on cell cycle phase.
• Checking the lysosomal iron in cells of different size.
• Describing and showing all statistical tests.

Significance

General Assessment: This study presents a mechanistic link between cell size and ferroptosis susceptibility. Using high-throughput microscopy, proteomics, and genetic perturbations across multiple human cell lines, the authors demonstrate that larger cells are more resistant to ferroptosis induced by system xc⁻ inhibition (erastin2). This resistance is attributed to elevated glutathione production, increased ferritin-mediated iron sequestration, and reduced ACSL4-dependent lipid peroxidation. The experimental design is rigorous and multifaceted, with consistent results across cell types and size manipulation methods. While the study is limited to in vitro systems, its conceptual and mechanistic insights lay the groundwork for future in vivo and translational investigations.

Advance: This work is the first to systematically show that cell size directly influences ferroptosis susceptibility via proteome scaling. It reconciles previous findings that large cells are sensitized to GPX4 inhibition (RSL3) by demonstrating that the ferroptosis pathway targeted system xc⁻ vs GPX4 determines the direction of size-dependent vulnerability. The study provides a conceptual advance by positioning cell size as a regulatory axis in cell death decisions, and a mechanistic advance by identifying size-dependent changes in glutathione metabolism, ferritin levels, and ACSL4 expression. Audience: This research will be of interest to specialists in cell death, ferroptosis, redox biology, and cancer biology. It also holds relevance for aging researchers and translational scientists exploring ferroptosis-based therapies. The findings may influence how cell size heterogeneity is considered in therapeutic design, particularly in oncology and senescence-targeting strategies.

Field of Expertise: Translational cancer biology, cell cycle regulation, proteomics, therapy resistance, molecular mechanisms of cell death.

Limitations of Evaluation: I do not have sufficient expertise to evaluate the glutathione kinetics, though the biological interpretation is clear and well-supported.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The study by Zatulovskiy et al. examined how cell size influences cell susceptibility to ferroptosis. The authors found a size dependence specifically for ferroptosis-inducing drug Era2, but not for other drugs. Using various human cell lines (HMEC, HT 1080, RPE 1), the authors generated populations of small and large G1 cells by FACS, CDK4/6 inhibition (palbociclib), or inducible cyclin D1 knockdown, and measured cell susceptibility to ferroptosis. Larger cells were more resistant than smaller cells. Mechanistically, larger cells showed reduced plasma membrane lipid peroxidation, higher glutathione concentrations, and changes in relevant cellular proteins levels, as analyzed using previously published data. Deleting ACSL4, which is involved in ferroptosis, partly eliminated the size dependence of ferroptosis. The work concludes that cell size is a key determinant of ferroptosis susceptibility.

My major concerns about this work focus on whether many of the results reflect cell size or cell cycle effects, and whether the FACS-based size-scaling analyses have some misleading features to their design & presentation. If these concerns can be addressed with new experiments, then the conclusions of this paper are justified. If these concerns cannot be addressed, then the authors should more directly acknowledge the alternative hypothesis that cell cycle effects may explain many of their results.

The experiments seem to be replicated sufficiently, and most conclusions rely on data from multiple cell lines. My minor comments focus on needs to provide statistics and method details, and on suggestions on how to improve text clarity, but these edits are easily done and don't require new experiments. Overall, this is an interesting study, and it should be published once the concerns below are addressed.

Major comments:

• In experiments reported in Fig 1 and 2A, the authors sort small and large cells in G1, plate them, and later start the drug treatments & cell monitoring. Are these cells actively cycling (progressing in the cell cycle), and how fast? The large cells are likely to enter S phase earlier than the small cells, so by the time that the authors start their drug treatments, they may be comparing cells in different cell cycle stages, which could influence drug sensitivity more than cell size (as the authors also suggest later in Fig 2). This needs to be controlled for. Furthermore, even if the cells remain in G1 after sorting until the drug treatments are started, the authors should address the fact that the drugs are present for a long time, thus targeting the cells in various cell cycle stages.
• Can the G1 arrest-driven changes in drug susceptibility (Fig 2 C-D) be attributed to cell size? Can the authors rescue the palbociclib treatment with rapamycin or other growth inhibitors that allow size to remain small during G1 arrest?
• In Fig 2E-F, is the cell cycle distribution of the samples influenced by CCND1 shRNA induction? Are the drug sensitivity effects due to cell size or cell cycle changes?
• Can the authors address the meaningfulness of the FACS-based size-scaling results in cases where cell-to-cell variability is very large? For example, in Fig 4D&G, the results are so variable even in identically sized cells that the importance of the size-scaling pattern seems questionable.
• In Figs 4B-D, the cell size axis seems to have over 4-fold size variability, but when the authors show the analysis of this data (Figs 4E-G) the variability is only 2-fold. What was excluded and on what basis?
• Based on the methods section & figure legends of Fig 4B-I, the RPE cells were not pre-sorted to include only G1 cells, nor did the assay account for cell cycle differences. How can these data be used to explain results from earlier figures, where analyses were exclusively focused on size differences in G1?

Minor comments:

• I recommend clarifying in the early introduction that all size changes discussed are in the absence of DNA content increase.
• The introduction seems to cite primary research and review paper in the same sentences, which is a bit misleading as the reviews don't seem to add new evidence.
• OPTIONAL In the second introduction paragraph, consider the classification/description of the three different mechanisms. Currently, it seems that these mechanisms are not independent of each other, and the details provided about each mechanism are inconsistent.
• Please provide statistics for the IC50 values reported based on Fig 1C. Were small and large cells statistically different? Are the IC50 values reported as +/- standard deviation or some other metric?
• OPTIONAL Providing more insight into why Era2 and RSL3 treatments yield more opposite responses would be of great interest to the field.
• Is the BODIPY-C11 labeling specific to plasma membrane, as suggested by the writing of the authors, or do the results shown integrate signals over all cell membranes?
• How exactly is gating done for the flow cytometry samples? Especially when analyzing size-scaling, the results are likely to be sensitive to outliers, such as those seen in Fig 4C (a subpopulation of very low CFSE stained cells). Can the authors clarify their methods and/or display supplementary figures with gating examples?
• In Fig 4, total protein staining was used as a control, whereas Fig 5B b-actin was used as a control. Why did the authors rely on different controls approaches for essentially the same measurements? Are these controls comparable?

Significance

I work in the cell size research field, and I am familiar with other related works in this field. My evaluation reflects a specialist's view of this study. Overall, this study will be of a large interest to a small group of specialists, and specific aspects of the work will also gain some interest from broader basic research audiences studying mechanisms of drug responses and ferroptosis in general. However, I do not see this work gaining very broad interest across larger audiences, simply because the field of cell size research is not of broad interest, and this is not a landmark study for the field.

The field of cell size research has long searched for size-dependent functions, as these could help explain why cell size matters. This study is a nice addition to our field, helping establish ferroptosis as a size-dependent function. However, the significance of this work relies on how clearly the authors can establish that their results are cell size rather than cell cycle effects (see major comments above). Should the authors address these concerns, then this study will provide some conceptual and mechanistic insight.

Regarding mechanistic insights, this work is in stark contrast to a recent study about size-dependency of ferroptosis (https://doi.org/10.1016/j.isci.2025.112363), where increased cell size heightened sensitivity to the GPX4 inhibitor RSL3, thus suggesting an opposite conclusion than what the authors observed with the drug Era2. The authors examined this contradiction, and while their results with the drug RSL3 agreed with the recent study, they did not explain why different drug mechanisms yield opposite results. Providing more insights into this discrepancy would increase the impact of this work.

Regardless of the impact of this work, I want to emphasize that I am fully supportive of seeing this work published once the technical concerns have been addressed. Our field will benefit from this work, and this work could catalyze important future research. The general topic studied here has the potential to become very important.

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Reply to the reviewers

Reviewer 1

__#1.1 __In Fig 1 it appears that both PI3P and PI3,5P2 are present on lysosomes (Lamp1-FRB) and that recruitment of MTM1 (via FKBP) depletes both of them. Additionally, In the images and quantifications, it appears that after recruitment of MTM1, there is no vesicular pools of PI3P or PI3,5P2 left at all. This raises several concerns:

__#1.1a __What is happening to the pool of PI3P on Rab5 endosomes? The main pool of PI3P is on Rab5 endosomes and separate from LAMP1 lysosomes. Why does recruitment of MTM1 to lysosomes then lead to almost complete depletion of all PI3P (Fig1 B bottom panel), when the lysosomal pool of this lipid should be minor compared to that on early endosomes?

We plan to add data showing recruitment of FKBP-MTM1 to FRB-Rab5 positive endosomes. This also causes complete depletion of both PI3P and PI(3,5)P₂ probes. We believe this is the result of the over-expression of Rab5 or LAMP1 reporters, the robust activity of FKBP-MTM1 and the somewhat indistinct nature of these compartments (e.g. 10.1016/j.cell.2024.11.028) – in short, there is enough residual LAMP1 present in Rab5 enriched compartments or Rab5 in LAMP1-enriched membranes that robust depletion of lipids occurs in both when over-expressed .

__#1.1b __The main problem comes from disagreement with figure 3. There it is shown that ".PI(3,5)P2 does not significantly overlap with PI3P". If this is true, then why does recruitment of MTM1 to LAMP1 lead to the depletion of both PI3P and PI3,5P2. This would indicate that they are on the same compartment (LAMP1 positive lysosomes)?

We plan to add a complete, quantitative co-localization analysis of PI(3,5)P₂ and PI3P probes, as well as an analysis of both lipid probes with Rab5 and LAMP1. We already showed in such an analysis that PI3P is more closely co-localized with Rab5 than Rab7 (10.1083/jcb.201312072), but this is not absolute: not all late endosomal compartments are alike, and some contain PI3P whereas some do not (e.g. 10.1016/j.cell.2023.09.027). Likewise, we expect to show near exclusion of PI3P and PI(3,5)P₂, with greater co-localization between PI3P and Rab5 vs LAMP1, and the opposite for PI(3,5)P₂ (as shown in 10.1083/jcb.202408158). But nonetheless, there will be some PI3P-positive LAMP1 membranes.

#1.1c A merge and colocalization analysis is at least needed to address how much of SnxA and EEA1-FYVE is localized to LAMP1-FRB. But just by looking at the one cell depicted, the localisation of LAMP1-FRB seems to be rather distinct from EEA1-FYVE and SnxA

We believe our response to #1.1b will also address his point.

#1.2 Minor: Fig2 is all in all way to small and it is difficult to actually see the signal in panel A and C. It should also be noted that in these panels (zoomed in to my best ability) that there is clear localisation of SnxA to the plasma membrane. Is this pool lost after Apilimod treatment, or is this unspecific binding? This PM localisation also appears in Fig1 B and 5C and should be discussed.

We will enlarge the panels in figure 2 to ease visualization of the detail. We will also describe the PM localization of the probe, and how this is insensitive to apilimod treatment (Fig2. 2A). We will add this to the discussion, also citing how a non-PI(3,5)P₂ dependent PM localization of SnxA was also noted in the original study (Vines et al), and note this as a potential draw back of the full-length SnxA.

__#1.3 __It should also be pointed out that dextran will be taken up through macropinocytosis and might follow different endocytic trafficking to conventional receptor.

We will add a description to the results for figure 2 describing how dextran is taken up non-selectively through fluid-phase endocytosis (i.e. both conventional receptor-mediated endocytosis and micropinocytosis).

#1.4 It also seems that the dextran signal decreases after Ap treatment. Is this the case? Has this been quantified? Would that point towards the whole endocytic structure being degraded and not just PI3,5P2?

We believe this reduction is due to simple photobleaching of the dye under time-lapse imaging. We will quantify this as suggested – but crucially, we included the DMSO vehicle control which will perfectly control for photobleaching.

__#1.5 __OPTIONAL: The timeline of PI3,5P2 degradation and vacuolation is a great experiment and very important. However, PI3,5P2 production is critically dependent on prior generation of PI3P. It could be of interest to readers what happens to SnxA localisation when cells are treated with VPS34-IN-1 or Wortmannin. How does loss PI3,5P2 compare between the timing of PIKfyve inhibition and inhibition of PI3K that generate its substrate. The timescales of this might tell us something interesting about the timings of phosphoinositide conversions. Also, treatment with PI3K inhibitors is known to not lead to vacuolisation even though it does also lead to a loss of PI3,5P2, further indicating that there might be more to the vacuolation phenotype than just the loss of PI3,5P2. These experiments would add novelty and detail to the study but do not change the overall findings or conclusions.

This would indeed be an feasible experiment, but we do not believe the novelty would be significant: rapid depletion of PI3P with PI3K inhibitors has already been documented; notably, we demonstrated depletion of PI3P by wortmannin with a similar ~10 min time constant (10.1083/jcb.201312072) to the PI(3,5)P₂ depletion by apilimod reported herein. Since substrate depletion is ultimately an enzyme inhibitor, we would anticipate very similar kinetics for PI(3,5)P₂ depletion by apilimod vs wortmannin. However, if the reviewer and editor believe this experiment is essential, we could add it. We just do not believe it significantly strengthens the paper.

#1.6a: Major: Fig3: The distinct localisation of PI3P and PI3,5P2 looks convincing but does not seem to be in line with data in Fig1.

We believe our response to #1.1 addresses this point also.

__#1.6b __It should be clearly noted and discussed that the structure in Fig3 B is a nascent macropinosomes (the size and proximity to the PM make this clear) and this transition on macropinosomes as been well characterised in Vines et al 2023

We agree with the reviewer that this structure could easily be a macropinosome, though without a marker, we cannot definitively make this claim. Of course, the same logic applies to our erroneous declaration that this is an endosome (though HEK293A cells do possess some similarly very large, Rab5+ve sorting endosomes)! We will therefore amend the text to classify this as “an initially PI3P positive compartment”.

#1.7 Major minor: Figure 5 is a very powerful approach to produce a completely independent pool of PI3,5P2. As control, the PIKfyve-CCR-Kina construct should be recruited to mitochondria in the absence of the MavQ construct. This should lead to the generation of PI5P (the other known product of PIKfyve) without generating PI3,5P2. This would be a useful control to test that SnxA does not bind to PI5P. (As a side note, this method would be great to use to try and find a bone fide PI5P effector. Maybe by isolating mitos and sending them to Mass Spec after altering their PIP composition? But this is obviously a completely different story)

The is an excellent suggestion. We plan to add these experiments as a control for Fig. 5, though there will be nuanced interpretation – because we have no way of verifying PI5P generation by PIKfyve in the absence of a verified PI5PP biosensor. Furthermore, direct synthesis of PI5P by PIKfyve remains controversial (e.g. 10.1073/pnas.1203106109). Incidentally, we have attempted to co-recruit a PIP4K to convert any PI5P to PI(4,5)P₂, but this did not work.

#1.8 Major: Figure 6 is great work, but it must be discussed that SnxA is a constitutive dimer while the 2xPx is a monomer. Therefore, the SnxA dimer will also contain two fluorescent proteins and will therefore also appear brighter than the 2xPx. Therefore, the increased baseline of SnxA might just be due to its nature as dimer and not because it has a higher affinity to PI3,5P2 compared to the 2xPx. OPTIONAL: One way to clear this up would be to make a 2xPx construct that also contains 2 fluorescent proteins. Also, the increase in fluorescence should also be shown as normalized to the initial intensity. From the graphs in 6a it seems that both have an ~1.3 and ~1.5 fold increase?

We will add a discussion of the constitutive dimer nature of full-length SnxA. However, we disagree with the assertion that the dual GFP of the GFP-SnxA dimers accounts for the increased baseline labeling – since our quantification is based on the ratio of fluorescence at the membrane to elsewhere. Since there is a heavily diffuse signal of unbound probe, this diffuse pool is also dually labelled by the dimeric GFP-SnxA – in effect, the increased signal on membranes by dimeric GFPs is cancelled by the cytosolic dimers. We will clarify this point in the discussion.

#1.9 OPTIONAL (but important): It would be great to compare the recently described G13V mutant of SnxA that is reported to have a higher affinity to PI3,5P2 (Preprint, Nishimura et al 2025). These experiments would add novelty and detail to the study but do not change the overall findings or conclusions. But as the study sets out to find the best PI3,5P2 probe, this might be very important

This is indeed an important study. That said, the existence of this mutant does not change the overall importance of our demonstration here that PI(3,5)P₂ is both necessary and sufficient to recruit SnxA to membranes. We also feel that it is beyond the scope of our manuscript to perform detailed controls on the findings of another manuscript that itself has not passed peer review. However, we will add a point to the discussion about the likely impact of the G13V mutant.

#1.10 Minor: In the discussion it is stated that "Vines et al. showed SnxA to have higher affinity for PI(3,5)P2 in vitro compared to 2xPx-SnxA" The Kd (to model membranes with 5% PI3,5P2 in POPC background!) for SnxA there is 187+-13nM and for 2xPx 217+-7 nM. Taking the top and bottom ranges of the uncertainty intervals to 200nM and 210nM respectively. While this is still a slightly higher Kd for SnxA, I am unsure how physiologically relevant this difference is.

This is an excellent point, and we will amend the discussion to point out that the subtle differences in affinity likely don’t explain the enhanced performance of SnxA, as indeed the dual GFPs don’t as covered in #1.8.

__#1.11 __Minor: In the discussion it is stated that "But, we could observe a short temporal overlap between the two lipids within a single endosome, lasting only a few minutes". If this statement refers to Figure 3B, then it must be clearly stated that this a macropinosome and not be conflated with canonical endosomes

We will less precisely define these membranes as we did in response to #1.6b

__#2.1 __While the data are by enlarge backed up by the presented data, there are two instances in which controls do not show the desired properties in some figures (but do in others). Specifically, the kinase dead control construct experiments in Figures 4D and 5D suffer from a lack of localization of the FKBP-PIKfyve-CCR-Kinase-Dead construct to the Rab5 endosomes or mitochondria respectively. Without robust localization of the control kinase, the dependency on PI(3,5)P2 synthesis (as opposed to physical kinase mediated recruitment) cannot be excluded. The construct shows robust relocalization in Figure 6 when the 2xPx-SnxA is being evaluated. With the combined evidence shown in the paper, this does not create significant doubt about the overall conclusions, but this issue needs to be addressed.

We believe the poor apparent recruitment in figures 4D and 5D stems from two reasons; firstly, the signal to noise of the tagBFP-kinase construct is low (especially since the photodamaging 405 nm excitation laser must be used at low intensity of these time-lapse experiments). Therefore, one solution is to simply select example images to demonstrate recruitment where expression of TagBFP2 had better signal-to-noise. As can be seen from the quantification of data in figures 5 and 6, recruitment of FKBP-PIKfyve-CCR-Kinase and FKBP-PIKfyve-CCR-Kinase-Dead were very similar, but this was not so for figure 4; in this case, we will re-analyze the data to analyze only FKBP-PIKfyve-CCR-Kinase cells with similar recruitment to the dead for a direct comparison; if there is insufficient data, we will repeat the experiments to obtain balanced recruitment of both.

__#3.1 __In Figure 1B, the authors show a rapid depletion of PI3P upon recruitment of MTM1 to LAMP1-positive membranes. The apparent minimal overlap between EEA1-FYVE and LAMP1 signals in the images is intriguing. It would be helpful if the authors could comment on whether this reflects rapid membrane trafficking dynamics or nonspecific membrane targeting of MTM1. In addition, the lysosomal SnxA signal appears to decrease with somewhat slower kinetics compared to PI3P. A short clarification as to whether MTM1 is expected to directly dephosphorylate PI(3,5)P₂, or whether the observed reduction in PI(3,5)P₂ is secondary to depletion of its precursor PI3P, resulting in gradual turnover of the PI(3,5)P₂ pool. Clarification of this point would further refine the mechanistic interpretation, although this point does not detract from the overall conclusions.

The first part of this comment will be addressed by our response to #1.1. We will also add a discussion detailing how MTM1 itself has a somewhat controversial substrate selectivity, with the first report stating it was PI3P selective and did not hydrolyze PI(3,5)P₂ (10.1073/pnas.160255697), whereas a subsequent study found that it has robust activity against PI(3,5)P₂ (10.1016/s0960-9822(03)00132-5). Therefore, direct activity on PI(3,5)P₂ cannot be ruled out. Secondly, we will describe how our data and Pemberton et al showed that PIKfyve recruitment depletes PI3P, demonstrating that PIKfyve activity can outstrip VPS34 that makes PI3P. Therefore, in PI(3,5)P₂-positive, PI3P-negative membranes, it is possible that VPS34 is still active, but PI3P never accumulates because PIKfyve immediately converts it to PI(3,5)P₂.

#3.2. In Figure 3, the authors conclude that SnxA and FYVE do not overlap, but rather localize in close proximity. While this is an interesting observation, some degree of apparent overlap can be perceived in the images. Although the qualitative impression is largely convincing, inclusion of a quantitative colocalization analysis (e.g., Pearson's or Manders' coefficients) could further strengthen this conclusion.

We are planning to add precisely this analysis in response to #1.1b.

#3.3. In Figure 4D, SnxA localization is still detectable in cells expressing the kinase-dead PIKfyve construct. If endogenous wild-type PIKfyve is present, residual PI(3,5)P₂ production could explain this signal and influence the interpretation of the experiment. The authors should clearly state which cell lines were used and whether endogenous PIKfyve activity was present in each condition. This information should be provided consistently in the figure legends to avoid ambiguity.

We will clarify the results and legends to make clear that endogenous PIKfyve is indeed expressed in these cells, with either FKBP-PIKfyve-CCR-Kina or FKBP-PIKfyve-CCR-Kina-Dead. Will clarify that over-expressed catalytic PIKfyve fragments will not perturb endogenous PIKfyve activity, explaining basal SnxA localization in figures 4C and 4D.

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Referee #3

Evidence, reproducibility and clarity

• The manuscript by Swayhoover et al. systematically validates the functionality and specificity of the PI(3,5)P₂ biosensor SnxA. The authors demonstrate that SnxA loses its lysosomal localization upon targeted recruitment of MTM1 to LAMP1-positive membranes, as well as following treatment with the selective PIKfyve inhibitor Apilimod. Together, these findings convincingly show that SnxA membrane association critically depends on the presence of PI(3,5)P₂.

• To further assess whether PI(3,5)P₂ is sufficient for SnxA recruitment, the authors established a reconstitution approach in which a PIKfyve construct was co-recruited with the PI 3-kinase MavQ to the mitochondrial membrane, an organelle that normally lacks detectable PI(3,5)P₂. Induced recruitment of the active enzymes led to robust mitochondrial localization of SnxA, whereas no such recruitment was observed when a kinase-dead PIKfyve construct was used. These results demonstrate that ectopic production of PI(3,5)P₂ is sufficient to drive SnxA membrane association.

• Lastly, the authors compare SnxA to previously described PI(3,5)P₂ reporters, ML1Nx2 and 2xPX-SnxA. To this end, SnxA was co-expressed with either reporter, and PI(3,5)P₂ production was induced on Rab5-positive endosomal structures via recruitment of the PIKfyve construct. While 2xPX-SnxA showed partial recruitment to Rab5-positive membranes, this effect was less pronounced than that observed for full-length SnxA. In contrast, ML1Nx2 exhibited apparent membrane association even in cells expressing the kinase-dead PIKfyve construct, and no additional relocalization was observed upon recruitment of the active kinase. These findings suggest that, under the experimental conditions tested, ML1Nx2 lacks substrate specificity and does not reliably report inducible PI(3,5)P₂ production. Overall, this study represents a compelling and well-executed cell biological analysis that supports the functionality and specificity of the recently established SnxA reporter. By providing a rigorously validated tool to monitor PI(3,5)P₂ dynamics in mammalian cells, the work will facilitate future investigations into the still poorly understood mechanisms regulating PI(3,5)P₂ metabolism. The experiments are carefully conducted, and the authors draw appropriate conclusions from their data. I do not have major concerns; however, I list a few minor comments below.

Minor points

1. In Figure 1B, the authors show a rapid depletion of PI3P upon recruitment of MTM1 to LAMP1-positive membranes. The apparent minimal overlap between EEA1-FYVE and LAMP1 signals in the images is intriguing. It would be helpful if the authors could comment on whether this reflects rapid membrane trafficking dynamics or nonspecific membrane targeting of MTM1. In addition, the lysosomal SnxA signal appears to decrease with somewhat slower kinetics compared to PI3P. A short clarification as to whether MTM1 is expected to directly dephosphorylate PI(3,5)P₂, or whether the observed reduction in PI(3,5)P₂ is secondary to depletion of its precursor PI3P, resulting in gradual turnover of the PI(3,5)P₂ pool. Clarification of this point would further refine the mechanistic interpretation, although this point does not detract from the overall conclusions.

2. In Figure 3, the authors conclude that SnxA and FYVE do not overlap, but rather localize in close proximity. While this is an interesting observation, some degree of apparent overlap can be perceived in the images. Although the qualitative impression is largely convincing, inclusion of a quantitative colocalization analysis (e.g., Pearson's or Manders' coefficients) could further strengthen this conclusion.

3. In Figure 4D, SnxA localization is still detectable in cells expressing the kinase-dead PIKfyve construct. If endogenous wild-type PIKfyve is present, residual PI(3,5)P₂ production could explain this signal and influence the interpretation of the experiment. The authors should clearly state which cell lines were used and whether endogenous PIKfyve activity was present in each condition. This information should be provided consistently in the figure legends to avoid ambiguity.

Significance

The manuscript by Swayhoover et al. systematically validates the functionality and specificity of the PI(3,5)P₂ biosensor SnxA. The authors demonstrate that SnxA loses its lysosomal localization upon targeted recruitment of MTM1 to LAMP1-positive membranes, as well as following treatment with the selective PIKfyve inhibitor Apilimod. Together, these findings convincingly show that SnxA membrane association critically depends on the presence of PI(3,5)P₂.

• To further assess whether PI(3,5)P₂ is sufficient for SnxA recruitment, the authors established a reconstitution approach in which a PIKfyve construct was co-recruited with the PI 3-kinase MavQ to the mitochondrial membrane, an organelle that normally lacks detectable PI(3,5)P₂. Induced recruitment of the active enzymes led to robust mitochondrial localization of SnxA, whereas no such recruitment was observed when a kinase-dead PIKfyve construct was used. These results demonstrate that ectopic production of PI(3,5)P₂ is sufficient to drive SnxA membrane association.

• Lastly, the authors compare SnxA to previously described PI(3,5)P₂ reporters, ML1Nx2 and 2xPX-SnxA. To this end, SnxA was co-expressed with either reporter, and PI(3,5)P₂ production was induced on Rab5-positive endosomal structures via recruitment of the PIKfyve construct. While 2xPX-SnxA showed partial recruitment to Rab5-positive membranes, this effect was less pronounced than that observed for full-length SnxA. In contrast, ML1Nx2 exhibited apparent membrane association even in cells expressing the kinase-dead PIKfyve construct, and no additional relocalization was observed upon recruitment of the active kinase. These findings suggest that, under the experimental conditions tested, ML1Nx2 lacks substrate specificity and does not reliably report inducible PI(3,5)P₂ production.

-Overall, this study represents a compelling and well-executed cell biological analysis that supports the functionality and specificity of the recently established SnxA reporter. By providing a rigorously validated tool to monitor PI(3,5)P₂ dynamics in mammalian cells, the work will facilitate future investigations into the still poorly understood mechanisms regulating PI(3,5)P₂ metabolism. The experiments are carefully conducted, and the authors draw appropriate conclusions from their data.

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Referee #2

Evidence, reproducibility and clarity

• Overall, the work is done very thoroughly, and considering the increasing interest in the less studies phosphoinositol species, it is also of significant interest. As outlined by the authors, the work is an extension of relatively recent work on the use of recent work SnxA. However, the very low cellular levels, as well as the (nicely demonstrated) rapid dynamics but a high demand on specificity. The authors also evaluate a tandem sensor (2xPx-SnxA).

• While the data are by enlarge backed up by the presented data, there are two instances in which controls do not show the desired properties in some figures (but do in others). Specifically, the kinase dead control construct experiments in Figures 4D and 5D suffer from a lack of localization of the FKBP-PIKfyve-CCR-Kinase-Dead construct to the Rab5 endosomes or mitochondria respectively. Without robust localization of the control kinase, the dependency on PI(3,5)P2 synthesis (as opposed to physical kinase mediated recruitment) cannot be excluded. The construct shows robust relocalization in Figure 6 when the 2xPx-SnxA is being evaluated. With the combined evidence shown in the paper, this does not create significant doubt about the overall conclusions, but this issue needs to be addressed.

Significance

The authors address a compelling need for the improvement and characterization of sensors that are capable of detecting changes in levels and localization of PI(3,5)P2. Some previous characterization had confirmed the ability of a novel sensor based on the PX domain containing Dictyostelium sorting nexin-like protein SnxA, to detect PI(3,5)P2 throughout the endosomal pathway, specifically on Rab7 enriched endosomes. The low cellular levels of PI(3,5)P2 put an emphasis on the specificity of detection and the authors expanded the characterization of a SnxA based biosensor, including ectopic expression to mitochondria.

Considering the involvement of PI(3,5)P2 in a range f cellular processes, availability of a trusted sensor will be of interest to a broader audience.

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Referee #1

Evidence, reproducibility and clarity

This highly important study by Swayhoover et al. uses state of the art cell biology and microscopy techniques to vigorously and unbiasedly assess biosensors against the phosphoinositide PI(3,5)P2. The independent validation of these biosensors is of crucial importance to the wider cell biology community. Using a range of orthogonal approaches, the authors clearly demonstrate the specificity and high affinity of the recently discovered biosensor SnxA. The ectopic generation of PI(3,5)P2 on mitochondria is a particularly outstanding and novel approach and clearly demonstrates the specificity of SnxA towards PI(3,5)P2 and rules out other factors in its recruitment, such coincidence detection mechanisms. The quantitative comparison against other versions of this biosensor is well done and adds important data to the field. While I do see some flaws in the manuscript, as well as several opportunities to improve both novelty and impact of the work, I do strongly supports its publication.

Major:

• In Fig 1 it appears that both PI3P and PI3,5P2 are present on lysosomes (Lamp1-FRB) and that recruitment of MTM1 (via FKBP) depletes both of them. Additionally, In the images and quantifications, it appears that after recruitment of MTM1, there is no vesicular pools of PI3P or PI3,5P2 left at all. This raises several concerns:

1) What is happening to the pool of PI3P on Rab5 endosomes? The main pool of PI3P is on Rab5 endosomes and separate from LAMP1 lysosomes. Why does recruitment of MTM1 to lysosomes then lead to almost complete depletion of all PI3P (Fig1 B bottom panel), when the lysosomal pool of this lipid should be minor compared to that on early endosomes?

2) The main problem comes from disagreement with figure 3. There it is shown that ".PI(3,5)P2 does not significantly overlap with PI3P". If this is true, then why does recruitment of MTM1 to LAMP1 lead to the depletion of both PI3P and PI3,5P2. This would indicate that they are on the same compartment (LAMP1 positive lysosomes)?

3) A merge and colocalization analysis is at least needed to address how much of SnxA and EEA1-FYVE is localised to LAMP1-FRB. But just by looking at the one cell depicted, the localisation of LAMP1-FRB seems to be rather distinct from EEA1-FYVE and SnxA

• Minor: Fig2 is all in all way to small and it is difficult to actually see the signal in panel A and C. It should also be noted that in these panels (zoomed in to my best ability) that there is clear localisation of SnxA to the plasma membrane. Is this pool lost after Apilimod treatment, or is this unspecific binding? This PM localisation also appears in Fig1 B and 5C and should be discussed.

a) It should also be pointed out that dextran will be taken up through macropinocytosis and might follow different endocytic trafficking to conventional receptor.

b) It also seems that the dextran signal decreases after Ap treatment. Is this the case? Has this been quantified? Would that point towards the whole endocytic structure being degraded and not just PI3,5P2?

c) OPTIONAL: The timeline of PI3,5P2 degradation and vacuolation is a great experiment and very important. However, PI3,5P2 production is critically dependent on prior generation of PI3P. It could be of interest to readers what happens to SnxA localisation when cells are treated with VPS34-IN-1 or Wortmannin. How does loss PI3,5P2 compare between the timing of PIKfyve inhibition and inhibition of PI3K that generate its substrate. The timescales of this might tell us something interesting about the timings of phosphoinositide conversions. Also, treatment with PI3K inhibitors is known to not lead to vacuolisation even though it does also lead to a loss of PI3,5P2, further indicating that there might be more to the vacuolation phenotype than just the loss of PI3,5P2. These experiments would add novelty and detail to the study but do not change the overall findings or conclusions.

Major: Fig3: The distinct localisation of PI3P and PI3,5P2 looks convincing but does not seem to be in line with data in Fig1

• It should be clearly noted and discussed that the structure in Fig3 B is a nascent macropinosomes (the size and proximity to the PM make this clear) and this transition on macropinosomes as been well characterised in Vines et al 2023

• Major minor: Figure 5 is a very powerful approach to produce a completely independent pool of PI3,5P2. As control, the PIKfyve-CCR-Kina construct should be recruited to mitochondria in the absence of the MavQ construct. This should lead to the generation of PI5P (the other known product of PIKfyve) without generating PI3,5P2. This would be a useful control to test that SnxA does not bind to PI5P. (As a side note, this method would be great to use to try and find a bone fide PI5P effector. Maybe by isolating mitos and sending them to Mass Spec after altering their PIP composition? But this is obviously a completely different story)

• Major: Figure 6 is great work, but it must be discussed that SnxA is a constitutive dimer while the 2xPx is a monomer. Therefore, the SnxA dimer will also contain two fluorescent proteins and will therefore also appear brighter than the 2xPx. Therefore, the increased baseline of SnxA might just be due to its nature as dimer and not because it has a higher affinity to PI3,5P2 compared to the 2xPx. OPTIONAL: One way to clear this up would be to make a 2xPx construct that also contains 2 fluorescent proteins. Also, the increase in fluorescence should also be shown as normalised to the initial intensity. From the graphs in 6a it seems that both have an ~1.3 and ~1.5 fold increase?

• OPTIONAL (but important): It would be great to compare the recently described G13V mutant of SnxA that is reported to have a higher affinity to PI3,5P2 (Preprint, Nishimura et al 2025). These experiments would add novelty and detail to the study but do not change the overall findings or conclusions. But as the study sets out to find the best PI3,5P2 probe, this might be very important

• Minor: In the discussion it is stated that "Vines et al. showed SnxA to have higher affinity for PI(3,5)P2 in vitro compared to 2xPx-SnxA" The Kd (to model membranes with 5% PI3,5P2 in POPC background!) for SnxA there is 187+-13nM and for 2xPx 217+-7 nM. Taking the top and bottom ranges of the uncertainty intervals to 200nM and 210nM respectively. While this is still a slightly higher Kd for SnxA, I am unsure how physiologically relevant this difference is.

• Minor: In the discussion it is stated that "But, we could observe a short temporal overlap between the two lipids within a single endosome, lasting only a few minutes". If this statement refers to Figure 3B, then it must be clearly stated that this a macropinosome and not be conflated with canonical endosomes

Significance

This is a strong study with vigorous and well controlled experiments. It is of broad interest to the cell biology community. With the recent discovery of a biosensors against PI(3,5)P2 it is crucial that novel tools undergo the scrutiny of the scientific community. For this, the publication of confirmatory results is of key importance. The authors do an excellent job to discuss their findings in the context of recently published work and clearly highlight where other studies have shown similar results previously. All of the conclusions are underpinned by vigorously controlled experiments. I think the study would benefit from some additional experiments to increase both its, novelty and quality.

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Reply to the reviewers

Manuscript number: RC-2025-03242R

Corresponding author(s): Shinya Kuroda

1. General Statements

We appreciate the reviewers for the critical review of the manuscript and the valuable comments. We have carefully considered the reviewer's comments and have revised our manuscript accordingly.

The reviewers' comments in this letter are in Bold and Italics.

2. Point-by-point description of the revisions

Response to Reviewer #1's Comments

Evidence, reproducibility and clarity:

Major comments

1. This study leaves out lipid metabolism as a major energy metabolism pathway relevant to AD. The authors themselves cite the significance of acylcarnitines and CPT1A in AD (pg. 3, lines 32-33, pg. 4, lines 1-2). Lipid metabolism and homeostasis is known to be disrupted in AD1. Fatty acid oxidation is a known energy source in the prefrontal cortex2 and will also generate acetyl coA, which this study reveals is a significant decreased metabolite in AD. Furthermore, sphingomyelin emerges as one of the major decreased DEMs as well. Thus, lipid metabolism should be highlighted in Figure 3 and discussed throughout the manuscript; otherwise its omission should be clearly stated and justified.

We appreciate the reviewer's insightful comment regarding a critical role of lipid metabolism in AD. We recognize that lipid metabolism is a metabolic pathway deeply involved in AD pathology (Baloni et al., 2022, 2020; Varma et al., 2021). Accordingly, we have revised the Limitations section to more strongly emphasize its role as a vital energy source (pg. 13, lines 15-17). Regarding the visualization of lipid metabolism, we extracted lipid-related pathway from the trans-omic network but found that the regulatory relationships among DEPs and DEMs were excessively complex and interconnected. Thus, interpreting this regulatory network seemed to be more challenging compared to the other energy production pathways presented in our manuscript. Therefore, we have concluded that the pathway analysis in our trans-omic network may not be suitable for deeply elucidating the lipid dysregulation in AD. We have added a statement acknowledging this as a limitation of our current methodology in the revised manuscript (pg. 13, lines 13-22).

The covariates used for differential analysis should be discussed and justified. Notably, age is used as a covariate for transcriptomic analysis but not proteomic and metabolomic analysis, with no justification. Additionally, given the known importance of lipid metabolism in AD and the putative role of APOE in lipid homeostasis3, APOE genetic status should be considered as a covariate, or its omission should be justified.<br />

We appreciate the reviewer's comment regarding the included covariates in differential analyses of our study. The reason we did not include other variables, such as age at death and RIN, is that these data were not available for each sample. Thus, we referred to the original research articles from which proteomic or metabolomic datasets used in our study were derived. Regarding the metabolomic dataset, in the original article (Batra et al., 2023), only two metabolites, 1-methyl-5-imidazoleacetate and N6-carboxymethyllysine, were significantly associated with age. In addition, no metabolites were significantly associated with sex, BMI, and years of education. Regarding the proteomic dataset, in the original article (Johnson et al., 2020), age at death, PMI, and sex were included as covariates in the analyses, though these variables were not found to strongly influence the data (Extended Data Fig.2 in (Johnson et al., 2020)).

The authors make a conclusion statement that suggests intervention: "Collectively, our data suggests that preserving or improving the ability to produce ATP and early intervention in the process of nitrogen metabolism are candidates for the prevention and treatment of dementia" (pg. 12, lines 12-14). This claim is not well-supported by the evidence provided in the study. There are a few limitations: (a) This was an observational, not interventional study; (b) The study did not establish whether the metabolic disruptions are causes or effects in AD; and (c) ATP or other bioenergetic indicators were not directly measured. Therefore, any statements about potential interventions should be removed or qualified as highly speculative.

We agree with the reviewer that the statement regarding potential interventions was not sufficiently supported by our analyses. Accordingly, we have removed the sentence regarding prevention and treatment from the revised manuscript (e.g., we have deleted final paragraph of the previous manuscript).

In conjunction with the last point, the main conclusion of the study is that energy production is down in AD. The data presented in Figure 3 are consistent with this conclusion, but it is far from definitive due to limitations stated above in comments 3a and 3b. The authors should offer additional support for this conclusion: experimental follow-up, flux modeling, analysis of alternative datasets with ATP measurement, causal inference.<br />

We sincerely thank the reviewer for this valuable and constructive suggestion. Regarding flux modeling, we agree that metabolic flux analysis could provide important mechanistic insight. Indeed, previous studies have applied flux modeling in the context of lipid metabolism in Alzheimer's disease (Baloni et al., 2022). We also attempted to perform flux modeling focusing on energy metabolism. However, we found it difficult to obtain biologically meaningful and robust results and therefore decided not to include these analyses in the current manuscript.

With respect to ATP measurements, we fully agree that direct evidence of altered ATP levels would further strengthen our conclusion. However, to the best of our knowledge, there are currently no publicly available large-scale datasets that directly measure ATP levels in human postmortem brain tissues. This limitation makes it challenging to incorporate validation in the present study.

Regarding experimental follow-up, we agree that functional validation is essential to confirm the mechanistic implications of our findings. We are actively considering follow-up experimental studies. However, we consider the present work to be a multi-omic integrative analysis aimed at identifying key molecular alterations and generating biologically important hypotheses. We have revised the Limitation section to more clearly position this manuscript as an observational systems-level analysis (pg. 13, lines 20-22).

The validation analysis did not sufficiently show the generalizability of this study's results. The authors demonstrated a correlation of 0.53 to the MSBB transcriptomics data and 0.60 to the AMP-AD DiverseCohorts proteomics data. Beyond these correlation coefficients, no meaningful comparison between the datasets is offered. How concordant are the differentially expressed features (or pathways) between the datasets? How robust would the trans-omic network be if incorporating the alternate datasets? Is the main conclusion (energy metabolism is down in AD) supported by the validation datasets? We think this analysis should be expanded and described in the main text. Although the results for external metabolomics datasets are reported in Fig S2C, correlation coefficients with the external data are not reported. The authors state, "Note that each study used different definitions for AD and CT groups, had variations in measurement methods and brain regions analyzed." We appreciate these limitations. However, the external data should be re-analyzed using the same definitions of AD and CT, if possible. The limitations and results (which DEMs are shared between datasets) should be discussed in the main text. __

We thank the reviewer for this important comment regarding the generalizability of our findings. In the revised manuscript, we have expanded the validation analyses and summarized the results in Figure S2. First, at the transcriptomic level, Figure S2B and S2C show the overlap between up- and downregulated genes in AD identified in our ROSMAP-derived analyses and those reported in a previously published large-scale meta-analysis of 2,114 postmortem samples across seven brain regions (Wan et al., 2020). A substantial proportion of DEGs were shared, supporting cross-cohort and cross-region robustness to some extent. At the proteomic level, Figure S2E shows a comparison between the ROSMAP and the AMP-AD DiverseCohorts datasets. We highlighted the subset of enzymes involved in the energy metabolism analysis shown in Fig. 3 and calculated a separate correlation coefficient for this subset (Pearson coefficient = 0.86, p-value = 1.5e-7), further supporting our main conclusion. In addition, to assess the concordance between the two datasets in a threshold-independent manner, we additionally performed Rank-Rank Hypergeometric Overlap (RRHO) analysis (Figure S2E). RRHO analysis (Cahill et al., 2018; Plaisier et al., 2010) enables the comparison of ranked protein lists without relying on arbitrary differential expression cutoffs and has been used for cross-dataset comparison in several previous studies (Fröhlich et al., 2024; Maitra et al., 2023). The RRHO heatmaps demonstrated significant enrichment in the concordant quadrants, confirming systematic agreement between datasets beyond simple correlation coefficients. For metabolomics, Figure S2G shows RRHO analyses comparing the ROSMAP metabolomic data with other datasets measured by the same UPLC-MS/MS platform (Batra et al., 2024; Novotny et al., 2023), demonstrating significant concordance in ranked metabolite changes in AD.

The glycolysis analysis and discussion needs more development. Glycolysis and gluconeogenesis share many of the same enzymes, but they are not the same pathway and should not be discussed as such. To make a claim about the overall influence of enzyme and metabolite levels on glycolysis, the authors should focus on the energetically committing steps of glycolysis (hexokinase, phosphofructokinase, pyruvate kinase) in Figure 3A, and include the full/current version of the figure in the supplement. Gluconeogenesis-specific enzymes (pyruvate carboxylase, PEPCK) are not mentioned at all - are they among the DEPs/DEGs?<br />

We appreciate the reviewer's comment regarding the distinction between glycolysis and gluconeogenesis pathway. Among the gluconeogenesis-specific enzyme proteins, G6PC1, FBP1, PC, and PCK2 were measured in our dataset, but none of them were identified as DEPs. In addition, gluconeogenesis is a process that occurs primarily in the liver and kidney rather than the brain. Given this biological context and the lack of significant changes in relevant enzymes, we have revised the terminology throughout the manuscript, replacing "glycolysis/gluconeogenesis pathway" with "glycolysis pathway" in the revised version.

Given that there wasn't good concordance between the DEGs and DEPs, did including the mRNA and transcription factor layers in the network really add anything useful? It seems like the main conclusions of the manuscript were driven by the protein and metabolite layers only. How many of the DE metabolic enzymes were coregulated at the transcript and protein level? It would be useful to include the 5-layer trans-omic network in the supplement to display these results. Given your network, at what level does it appear that energy metabolism is regulated?<br />

It is true that our primary conclusion regarding the regulation of energy metabolism is driven by the changes in protein and metabolite abundance. However, we consider the low concordance between mRNA and protein expression itself to be an important feature of AD pathology, as also reported in previous studies (Johnson et al., 2022; Tasaki et al., 2022). Although we did not perform a further analysis of this discordance, we believe that including the TF and mRNA layers into the metabolic trans-omic network strengthens a system-wide view of metabolic dysregulation in AD.

Regarding the mRNA changes corresponding to the DEP enzymes, please refer to Figure S7A.

Comment further on the results from Figure 2D. What can be learned from identifying metabolites with the greatest degree centrality? What pathways other than energy metabolism are highlighted by the trans-omic network?<br />

We assume that some energetic indicators, including AMP and acetyl-CoA, and nitrogen metabolism-related metabolites, Glu, 2-oxoglutarate, and urea, can be potential key regulators of dysregulated metabolism in AD.

(Suggestion) We suggest the authors leverage their trans-omic network in additional ways beyond giving a snapshot of a few energy metabolism pathways. The analysis of top DEMs could go further. What pathways are impacted beyond energy metabolism? Among the metabolic reactions allosterically regulated by top DEMs, what metabolic pathways are enriched?<br />

We identified the enriched metabolic pathways that were allosterically regulated by DEMs in AD using Fisher's exact test. Alanine, aspartate, and glutamate metabolism pathways were significantly enriched in 2-oxoglutarate, glutarate, alanine, and glutamate-regulating metabolic reactions. Arginine and proline metabolism pathway was enriched in N-methyl-L-arginine and putrescine-regulating metabolic reactions. Arginine biosynthesis pathway was enriched in arginine-regulating metabolic reactions. Glycerophospholipid metabolism pathway was enriched in CDP-ethanolamine-regulating metabolic reactions. Glycine, serine, and threonine metabolism pathway was enriched in serine-regulating metabolic reactions. Purine metabolism pathway was enriched in AMP-regulating metabolic reactions. Pyrimidine metabolism pathway was enriched in deoxyuridine and thymidine-regulating metabolic reactions. Sphingolipid metabolism pathway was enriched in sphingosine-regulating metabolic reactions. However, this analysis did not yield sufficiently valuable insights into the regulatory relationships among biomolecules in AD. Thus, we did not include these results in the revised manuscript.

(Suggestion) Figure 3 shows that most differential signal in AD points to lower energy production due to the combination of differentially expressed metabolites and enzymes, but we are not given much context about the strength of these among all the differential signals. We would suggest including volcano plots where the features of interest, i.e. DE enzymes and metabolites, are colored differently (or a similar figure).<br />

We thank the reviewer for this constructive suggestion. To provide better context regarding the importance of the differential signals, we have added volcano plots for mRNAs, proteins, and metabolites in Figure S4A, B, and C.

(Suggestion) The PPI network could be better leveraged to understand metabolic changes in AD. If nodes are grouped into subnetworks (e.g. by Louvain / Leiden clustering) and tested for pathway enrichment, could you find functional subnetworks of coordinately up- and down- regulated metabolic enzymes? This could yield some pathways of interest beyond the energy metabolism pathways already highlighted.<br />

We appreciate the reviewer's suggestion to utilize the PPI network for subnetwork analysis. However, it is important to note that the proteomic dataset analyzed in this study is derived from the original work of (Johnson et al., 2020). In that paper, the authors already performed a Weighted Gene Co-expression Network Analysis (WGCNA) across several datasets to identify co-expressed modules and functional pathways.

Given this, we assumed that applying additional clustering methods to the same dataset would be unlikely to yield significant biological insights beyond the established findings.

__ ____Minor comments __

12. "All genes" and "all metabolites" should not be the background for the proteomic and metabolic pathway enrichment analysis by Metascape and MetaboAnalyst. The background should be limited to the proteins and metabolites that were measured.

We fully agree with the reviewer that using "all gene" or "all metabolites" as a background is not suitable for enrichment analyses. As suggested, we have revised the enrichment analyses using the measured proteins and metabolites as a background in both Metascape and MetaboAnalyst (Fig. S4D).

Highlight the metabolic enzymes in Fig S2B. Calculate a separate correlation coefficient for the enzymes extracted in the energy metabolism analysis from Fig 3.<br />

We appreciate the reviewer's suggestion to refine the correlation analysis. As requested, we have revised Fig. S2D to explicitly highlight the subset of enzymes involved in the energy metabolism analysis shown in Fig. 3. We calculated a separate correlation coefficient for the subset (Pearson coefficient = 0.86, p-value = 1.5e-7).

Use a multiple hypothesis adjusted p-value or q-value in Figure S3.<br />

We agree with the reviewer regarding the necessity of correcting for multiple comparisons. Accordingly, we have revised Fig. S4D using q-values.

Describe the methods used to calculate the logFC values from the validation dataset.<br />

We have revised the Methods to include a detailed description of the procedure used to calculate the log2FC values for the validation datasets (pg. 21, lines 13-15).

It is difficult to read Figure 3. We would recommend really emphasizing to the reader to refer to Fig S7B as a "key" to this figure. The description of the red/blue arrows and nodes in the methods section (pg. 24, lines 21-36, pg 25, lines 1-4) were also helpful, but very lengthy. We recommend putting an abridged version of this description into the Fig S7 figure legend.<br />

We appreciate the feedback regarding the readability of Fig. 3. As recommended, we have revised the manuscript to explicitly direct readers to Fig. S8B as an essential "key" for interpreting the network visualization (pg. 8, lines 28). Furthermore, we have added an abridged description of the network elements to the legend of Fig. S8B.

The S7 figure legend should refer to panels A and B, not E and F.<br />

We apologize for this oversight. We have corrected the legend of Fig. S8.

(Suggestion) Are any of the differentially expressed metabolites allosteric regulators of the DE transcription factors? This could be interesting to discuss.<br />

We appreciate the reviewer's insightful suggestion about the potential allosteric regulation of the DETFs by DEMs. We conducted an extensive literature search to identify any reports related to this perspective. However, to the best of our knowledge, no such direct interactions have been reported to date.

Significance:

The study's strength lies in leveraging three omics modalities across large patient cohorts (n ~ 150-240) to identify coherent signals between transcriptomics, proteomics, and metabolomics in postmortem DLPFC tissue. It was encouraging to see that the main result, showing downregulation for TCA, oxidative phosphorylation, and ketone body metabolism, emerged from consistent signals across both proteomics and metabolomics. This result was consistent with previous findings in other models cited by the author4,5 and other studies 6,7 demonstrating deficiency in energy-producing pathways in AD. Another strength of the study is the application of thoughtful methodology to connect differentially expressed proteins and metabolites via an intermediate data layer of metabolic reactions. The authors leverage the KEGG and BRENDA databases and apply sound logic to estimate the effects of enzyme level and metabolite level on pathway activity, with metabolites serving as substrate, product, or allosteric regulator for reactions. This trans-omic network methodology was developed in previous studies cited by the author8,9. However, as written, this study is limited in its contribution of new knowledge to the AD research field. The main conclusion (energy production is down in AD, due to regulatory disruption of energy metabolism) is not strongly supported (see comments 1, 3, and 4 for elaboration). The evidence could be improved by orthogonal approaches: further experimentation, further integration of external datasets, causal modeling, or flux modeling. Alternatively, even in the absence of new experimental and computational approaches, the story could be made more complete by further leveraging the trans-omic network to provide insights into (a) the regulation of energy metabolism; and (b) the impacts of key disrupted metabolites (see comments 7-9). The study is also limited in its demonstrating the power of these methodologies to provide integrative insights. As mentioned above, the integration of enzyme levels and metabolite levels is clearly useful (Figure 3). In contrast, the utility of the mRNA and transcription factor layers was not evident. The study did not appear to improve or expand upon trans-omic network methodology described in the previous works. Finally, the various analyses (analyzing the trans-omic network for nodes with the highest degree centrality, the PPI analysis, and viewing the energy metabolism pathways in the network) provided disparate results that were only tenuously connected in the discussion section.

Response to Reviewer #2's Comments____

Evidence, reproducibility and clarity: Summary

This manuscript integrates public transcriptomic, proteomic, and metabolomic datasets from ROSMAP DLPFC samples to construct a multi-layer metabolic trans-omic network in Alzheimer's disease. By linking transcription factors, enzyme mRNAs, proteins, metabolic reactions, and metabolites, the authors report coordinated downregulation of the TCA cycle, oxidative phosphorylation, and ketone body metabolism, along with mixed regulatory signals in glycolysis/gluconeogenesis. They interpret these patterns as indicative of broad energetic dysfunction and alterations in amino-acid/nitrogen metabolism in AD. While the framework is conceptually appealing, much of the analysis remains descriptive, and several biological interpretations extend beyond what the data can robustly support. The reliance on bulk tissue without accounting for cell-type composition, limited covariate adjustment, and the absence of validation or sensitivity analyses reduce confidence in the mechanistic conclusions. Overall, the study provides a preliminary systems-level overview, but additional rigor is needed before the proposed trans-omic regulatory insights can be considered convincing.

Major Comments

1. Interpretation requires more cautious phrasing, and validation is essential. The manuscript frequently asserts that specific pathways are "inhibited" or that energetic deficits are "compensated," but these conclusions extend beyond what the descriptive, bulk-level data can support. Because no metabolic flux, causality, or direct functional measurements are included, the results should be framed as putative regulatory shifts, not confirmed impairments. Critically, key claims about pathway inhibition would require flux modeling, perturbation analyses, or experimental validation to be convincing. Without such validation, the mechanistic interpretations remain speculative.

We thank the reviewer for this crucial comment. We fully agree that, given the descriptive and bulk-level nature of our analysis, mechanistic interpretations must be made with caution. In the absence of direct metabolic flux measurements or experimental validation, our findings should be interpreted as putative regulatory shifts rather than confirmed functional impairments. Accordingly, we have revised the manuscript to temper mechanistic claims. We have replaced definitive statements with more speculative phrasing (e.g., "Our analysis revealed a putative coordinated downregulation ..." instead of "Our analysis revealed a coordinated downregulation ..." in Abstract section; "we demonstrate the systems-level view of the potential dysregulated energy production ..." instead of "we demonstrate the systems-level view of the dysregulated energy production ..." in pg. 10, lines 25-26).

Although the authors acknowledge this in the limitations, bulk-level differences may primarily reflect altered proportions of neurons, astrocytes, microglia, and oligodendrocytes rather than true within-cell-type regulation. Incorporating a cell-type deconvolution or performing a sensitivity analysis would substantially improve interpretability. This issue also impacts the trans-omic network: if the molecules included originate from different cell types, the inferred regulatory relationships may not reflect true intracellular processes.

We appreciate the reviewer's point that bulk-level differences can reflect altered proportions of different brain cell types, subsequently affecting the inferred trans-omic network analysis. To assess the changes in cell type proportions of the samples that we used in our study, we additionally used public single-cell transcriptomic datasets, which were obtained from DLPFC tissue of 465 subjects in the ROSMAP cohort (Green et al., 2024). For each omic data that we used in our analyses, we matched the same subjects and calculated the following cell type proportions, astrocytes, excitatory neurons, inhibitory neurons, microglias, oligodendrocytes, and OPCs. Then, we statistically compared the cell type proportions between control subjects and patients with AD (Fig. S3). In the transcriptomic data, we confirmed that the proportion of inhibitory neurons in the AD group was smaller than in the CT group, and that the proportion of oligodendrocytes in the AD group was larger than in the CT group. In the proteomic data, we did not observe any statistically significant changes in the cell type proportion between the two group. In the metabolomic data, we found that the proportion of inhibitory neurons in the AD group was smaller than in the CT group (pg. 6, lines 8-11).

Differential analysis covariates. For the differential expression analyses, only gender and PMI were included as covariates. Additional variables, such as age at death, RIN, neuropathological measures, and comorbidities, can strongly influence molecular profiles and should be considered to ensure that the observed differences reflect AD-related biology rather than confounding pathological or technical factors.

We appreciate the reviewer's comment regarding the included covariates in differential analyses of our study. The reason we did not include other variables, including age at death and RIN, is that these data for each sample were not available. Thus, we referred to original research articles from which proteomic or metabolomic datasets used in our study were derived. Regarding the metabolomic dataset, in the original article (Batra et al., 2023), only two metabolites, 1-methyl-5-imidazoleacetate and N6-carboxymethyllysine, were significantly associated with age. In addition, no metabolites were significantly associated with sex, BMI, or education. Regarding the proteomic dataset, in the original article, age at death, PMI, and sex were included as covariates in the analyses, though these variables were not found to strongly influence the data (Extended Data Fig.2 in (Johnson et al., 2020)).

Network stability and sample non-overlap. Proteomic, transcriptomic, and metabolomic data come from partially overlapping individuals. The authors should test whether the reconstructed network is robust to: different significance thresholds, restricting analyses to overlapping samples and alternative definitions of AD vs control.

__ __We appreciate the reviewer's comment for the trans-omic network stability. In our study, the number of individuals for whom all omic modalities were measured was relatively small (n=25 in CT and n=35 in AD). This limited overlap reduces statistical power and can affect the downstream network construction. We have acknowledged this limitation in the revised manuscript and clarified that the reconstructed networks should be interpreted with caution regarding reproducibility and generalizability (pg. 13, lines 13-23).

Minor Comments

1. Some TF enrichment and regulatory inferences lack explicit mention of multiple-testing correction.

We apologize for the lack of clarity in our original description. We have corrected for multiple-testing for the TF inference. Thus, we have revised the Methods section to explicitly describe the correction method used and the threshold applied (pg. 23, lines 23-24).

The limitations section is strong but should explicitly discuss the influence of postmortem interval on metabolite levels.<br />

We appreciate the reviewer's comment about the effect of postmortem interval on changes in metabolite levels. Accordingly, we have added the description of this perspective in our revised manuscript (pg. 13, lines 1-5).

__*Reviewer #2 (Significance (Required)):

Significance *__

The study extends a trans-omic integration framework, originally applied to metabolic disease, into the context of Alzheimer's pathology. Although the biological findings largely confirm known alterations in mitochondrial and energy metabolism, the network-based approach offers a structured way to view cross-layer regulatory changes. Its main advance is conceptual rather than biological, providing a unified framework rather than uncovering fundamentally new mechanisms. This work will primarily interest researchers in neurodegeneration and systems biology, as well as computational groups developing multi-omics integration methods.

Response to Reviewer #3's Comments

Evidence, reproducibility and clarity

This study leverages existing transcriptomic, metabalomic and proteomic datasets from prefrontal cortex (PFC) to assess metabolic dysregulation in Alzheimer's disease (AD). They found a downregulation of multiple metabolic pathways, including TCA cycle, oxidative phosphorylation, and ketone metabolism, that may explain bioenergetic alterations in AD. The study used matching ROSMAP omics datasets from the DLPFC that have allowed more robust data integration. However, the datasets are all generated using bulk tissue, which makes data interpretation difficult. For example, the AD changes they observed may be due to shifts in cell type proportion with disease (e.g. cell death, neuron inflammation). Did the authors account for any potential shifts in cell type proportion in their analysis?* *

__If the assumption is that the changes in AD are cell intrinsic, which cell types are likely to be impacted? Can the authors integrate any existing single-cell analysis to infer which cell types may be driving the signals they detect, and whether this accounts for some of the antagonistic regulatory effects that were detected?______

We thank the reviewer for their insightful comments. We agree that the use of bulk tissue datasets cannot account for cell-type heterogeneity. As noted in our Limitations section (pg. 12, lines 24-27), we recognize that previous studies have found that the Braak stage is correlated positively with microglia and astrocyte proportions and negatively with oligodendrocyte proportion (Hannon et al., 2024; Shireby et al., 2022). Regarding the integration of single-cell analysis, we have referenced recent snRNA-seq findings (Mathys et al., 2024) in our Limitations section (pg. 12, lines 28-32) to deconvolve our bulk signatures.

Furthermore, in our revised manuscript, we additionally used public single-cell transcriptomic datasets, which were obtained from DLPFC tissue of 465 subjects in the ROSMAP cohort (Green et al., 2024). For each omic data that we used in our analyses, we matched the same subjects and calculated the following cell type proportions, astrocytes, excitatory neurons, inhibitory neurons, microglia, oligodendrocytes, and OPCs. Then, we statistically compared the cell type proportions between control subjects and patients with AD (Fig. S3). In the transcriptomic data, we confirmed that the proportion of inhibitory neurons in the AD group was smaller than in the CT group, and that the proportion of oligodendrocytes in the AD group was larger than in the CT group. In the proteomic data, we did not observe any statistically significant changes in the cell type proportion between the two groups. In the metabolomic data, we found that the proportion of inhibitory neurons in the AD group was smaller than in the CT group (pg. 6, lines 8-11).

Significance

The manuscript provides multimodal insight into metabolic dysregulation in AD in the PFC. Given that metabolic dysfunction is likely to play a major in disease pathogenesis, this is a study of importance. However, the findings lack granularity at the cell type level, which limits the impact of the study.

Reference

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Referee #3

Evidence, reproducibility and clarity

This study leverages existing transcriptomic, metabalomic and proteomic datasets from prefrontal cortex (PFC) to assess metabolic dysregulation in Alzheimer's disease (AD). They found a downregulation of multiple metabolic pathways, including TCA cycle, oxidative phosphorylation, and ketone metabolism, that may explain bioenergetic alterations in AD.

The study used matching ROSMAP omics datasets from the DLPFC that have allowed more robust data integration. However, the datasets are all generated using bulk tissue, which makes data interpretation difficult. For example, the AD changes they observed may be due to shifts in cell type proportion with disease (e.g. cell death, neuron inflammation). Did the authors account for any potential shifts in cell type proportion in their analysis?

If the assumption is that the changes in AD are cell intrinsic, which cell types are likely to be impacted? Can the authors integrate any existing single-cell analysis to infer which cell types may be driving the signals they detect, and whether this accounts for some of the antagonistic regulatory effects that were detected?

Significance

The manuscript provides multimodal insight into metabolic dysregulation in AD in the PFC. Given that metabolic dysfunction is likely to play a major in disease pathogenesis, this is a study of importance. However, the findings lack granularity at the cell type level, which limits the impact of the study.

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

Summary

This manuscript integrates public transcriptomic, proteomic, and metabolomic datasets from ROSMAP DLPFC samples to construct a multi-layer metabolic trans-omic network in Alzheimer's disease. By linking transcription factors, enzyme mRNAs, proteins, metabolic reactions, and metabolites, the authors report coordinated downregulation of the TCA cycle, oxidative phosphorylation, and ketone body metabolism, along with mixed regulatory signals in glycolysis/gluconeogenesis. They interpret these patterns as indicative of broad energetic dysfunction and alterations in amino-acid/nitrogen metabolism in AD. While the framework is conceptually appealing, much of the analysis remains descriptive, and several biological interpretations extend beyond what the data can robustly support. The reliance on bulk tissue without accounting for cell-type composition, limited covariate adjustment, and the absence of validation or sensitivity analyses reduce confidence in the mechanistic conclusions. Overall, the study provides a preliminary systems-level overview, but additional rigor is needed before the proposed trans-omic regulatory insights can be considered convincing.

Major Comments

1. Interpretation requires more cautious phrasing, and validation is essential. The manuscript frequently asserts that specific pathways are "inhibited" or that energetic deficits are "compensated," but these conclusions extend beyond what the descriptive, bulk-level data can support. Because no metabolic flux, causality, or direct functional measurements are included, the results should be framed as putative regulatory shifts, not confirmed impairments. Critically, key claims about pathway inhibition would require flux modeling, perturbation analyses, or experimental validation to be convincing. Without such validation, the mechanistic interpretations remain speculative.
2. Although the authors acknowledge this in the limitations, bulk-level differences may primarily reflect altered proportions of neurons, astrocytes, microglia, and oligodendrocytes rather than true within-cell-type regulation. Incorporating a cell-type deconvolution or performing a sensitivity analysis would substantially improve interpretability. This issue also impacts the trans-omic network: if the molecules included originate from different cell types, the inferred regulatory relationships may not reflect true intracellular processes.
3. Differential analysis covariates. For the differential expression analyses, only gender and PMI were included as covariates. Additional variables, such as age at death, RIN, neuropathological measures, and comorbidities, can strongly influence molecular profiles and should be considered to ensure that the observed differences reflect AD-related biology rather than confounding pathological or technical factors.
4. Network stability and sample non-overlap. Proteomic, transcriptomic, and metabolomic data come from partially overlapping individuals. The authors should test whether the reconstructed network is robust to: different significance thresholds, restricting analyses to overlapping samples and alternative definitions of AD vs control.

Minor Comments

1. Some TF enrichment and regulatory inferences lack explicit mention of multiple-testing correction.
2. The limitations section is strong but should explicitly discuss the influence of postmortem interval on metabolite levels.

Significance

The study extends a trans-omic integration framework, originally applied to metabolic disease, into the context of Alzheimer's pathology. Although the biological findings largely confirm known alterations in mitochondrial and energy metabolism, the network-based approach offers a structured way to view cross-layer regulatory changes. Its main advance is conceptual rather than biological, providing a unified framework rather than uncovering fundamentally new mechanisms. This work will primarily interest researchers in neurodegeneration and systems biology, as well as computational groups developing multi-omics integration methods.

Reviewer expertise

My background is in Alzheimer's disease, multi-omics integration, and computational systems biology. I am not a specialist in enzymology or allosteric regulation and therefore cannot fully evaluate the biochemical specificity of those annotations.

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Referee #1

Evidence, reproducibility and clarity

Major comments

1. This study leaves out lipid metabolism as a major energy metabolism pathway relevant to AD. The authors themselves cite the significance of acylcarnitines and CPT1A in AD (pg. 3, lines 32-33, pg. 4, lines 1-2). Lipid metabolism and homeostasis is known to be disrupted in AD1. Fatty acid oxidation is a known energy source in the prefrontal cortex2 and will also generate acetyl coA, which this study reveals is a significant decreased metabolite in AD. Furthermore, sphingomyelin emerges as one of the major decreased DEMs as well. Thus, lipid metabolism should be highlighted in Figure 3 and discussed throughout the manuscript; otherwise its omission should be clearly stated and justified.
2. The covariates used for differential analysis should be discussed and justified. Notably, age is used as a covariate for transcriptomic analysis but not proteomic and metabolomic analysis, with no justification. Additionally, given the known importance of lipid metabolism in AD and the putative role of APOE in lipid homeostasis3, APOE genetic status should be considered as a covariate, or its omission should be justified.
3. The authors make a conclusion statement that suggests intervention: "Collectively, our data suggests that preserving or improving the ability to produce ATP and early intervention in the process of nitrogen metabolism are candidates for the prevention and treatment of dementia" (pg. 12, lines 12-14). This claim is not well-supported by the evidence provided in the study. There are a few limitations: (a) This was an observational, not interventional study; (b) The study did not establish whether the metabolic disruptions are causes or effects in AD; and (c) ATP or other bioenergetic indicators were not directly measured. Therefore, any statements about potential interventions should be removed or qualified as highly speculative.
4. In conjunction with the last point, the main conclusion of the study is that energy production is down in AD. The data presented in Figure 3 are consistent with this conclusion, but it is far from definitive due to limitations stated above in comments 3a and 3b. The authors should offer additional support for this conclusion: experimental follow-up, flux modeling, analysis of alternative datasets with ATP measurement, causal inference..
5. The validation analysis did not sufficiently show the generalizability of this study's results. The authors demonstrated a correlation of 0.53 to the MSBB transcriptomics data and 0.60 to the AMP-AD DiverseCohorts proteomics data. Beyond these correlation coefficients, no meaningful comparison between the datasets is offered. How concordant are the differentially expressed features (or pathways) between the datasets? How robust would the trans-omic network be if incorporating the alternate datasets? Is the main conclusion (energy metabolism is down in AD) supported by the validation datasets? We think this analysis should be expanded and described in the main text.

Although the results for external metabolomics datasets are reported in Fig S2C, correlation coefficients with the external data are not reported. The authors state, "Note that each study used different definitions for AD and CT groups, had variations in measurement methods and brain regions analyzed." We appreciate these limitations. However, the external data should be re-analyzed using the same definitions of AD and CT, if possible. The limitations and results (which DEMs are shared between datasets) should be discussed in the main text. 6. The glycolysis analysis and discussion needs more development. Glycolysis and gluconeogenesis share many of the same enzymes, but they are not the same pathway and should not be discussed as such. To make a claim about the overall influence of enzyme and metabolite levels on glycolysis, the authors should focus on the energetically committing steps of glycolysis (hexokinase, phosphofructokinase, pyruvate kinase) in Figure 3A, and include the full/current version of the figure in the supplement. Gluconeogenesis-specific enzymes (pyruvate carboxylase, PEPCK) are not mentioned at all - are they among the DEPs/DEGs? 7. Given that there wasn't good concordance between the DEGs and DEPs, did including the mRNA and transcription factor layers in the network really add anything useful? It seems like the main conclusions of the manuscript were driven by the protein and metabolite layers only. How many of the DE metabolic enzymes were coregulated at the transcript and protein level? It would be useful to include the 5-layer trans-omic network in the supplement to display these results. Given your network, at what level does it appear that energy metabolism is regulated? 8. Comment further on the results from Figure 2D. What can be learned from identifying metabolites with the greatest degree centrality? What pathways other than energy metabolism are highlighted by the trans-omic network? 9. (Suggestion) We suggest the authors leverage their trans-omic network in additional ways beyond giving a snapshot of a few energy metabolism pathways. The analysis of top DEMs could go further. What pathways are impacted beyond energy metabolism? Among the metabolic reactions allosterically regulated by top DEMs, what metabolic pathways are enriched? 10. (Suggestion) Figure 3 shows that most differential signal in AD points to lower energy production due to the combination of differentially expressed metabolites and enzymes, but we are not given much context about the strength of these among all the differential signals. We would suggest including volcano plots where the features of interest, i.e. DE enzymes and metabolites, are colored differently (or a similar figure). 11. (Suggestion) The PPI network could be better leveraged to understand metabolic changes in AD. If nodes are grouped into subnetworks (e.g. by Louvain / Leiden clustering) and tested for pathway enrichment, could you find functional subnetworks of coordinately up- and down- regulated metabolic enzymes? This could yield some pathways of interest beyond the energy metabolism pathways already highlighted.

Minor comments

1. "All genes" and "all metabolites" should not be the background for the proteomic and metabolic pathway enrichment analysis by Metascape and MetaboAnalyst. The background should be limited to the proteins and metabolites that were measured.
2. Highlight the metabolic enzymes in Fig S2B. Calculate a separate correlation coefficient for the enzymes extracted in the energy metabolism analysis from Fig 3.
3. Use a multiple hypothesis adjusted p-value or q-value in Figure S3.
4. Describe the methods used to calculate the logFC values from the validation dataset.
5. It is difficult to read Figure 3. We would recommend really emphasizing to the reader to refer to Fig S7B as a "key" to this figure. The description of the red/blue arrows and nodes in the methods section (pg. 24, lines 21-36, pg 25, lines 1-4) were also helpful, but very lengthy. We recommend putting an abridged version of this description into the Fig S7 figure legend.

6. The S7 figure legend should refer to panels A and B, not E and F.

7. (Suggestion) Are any of the differentially expressed metabolites allosteric regulators of the DE transcription factors? This could be interesting to discuss.

Significance

The study's strength lies in leveraging three omics modalities across large patient cohorts (n ~ 150-240) to identify coherent signals between transcriptomics, proteomics, and metabolomics in postmortem DLPFC tissue. It was encouraging to see that the main result, showing downregulation for TCA, oxidative phosphorylation, and ketone body metabolism, emerged from consistent signals across both proteomics and metabolomics. This result was consistent with previous findings in other models cited by the author4,5 and other studies 6,7 demonstrating deficiency in energy-producing pathways in AD. Another strength of the study is the application of thoughtful methodology to connect differentially expressed proteins and metabolites via an intermediate data layer of metabolic reactions. The authors leverage the KEGG and BRENDA databases and apply sound logic to estimate the effects of enzyme level and metabolite level on pathway activity, with metabolites serving as substrate, product, or allosteric regulator for reactions. This trans-omic network methodology was developed in previous studies cited by the author8,9. However, as written, this study is limited in its contribution of new knowledge to the AD research field. The main conclusion (energy production is down in AD, due to regulatory disruption of energy metabolism) is not strongly supported (see comments 1, 3, and 4 for elaboration). The evidence could be improved by orthogonal approaches: further experimentation, further integration of external datasets, causal modeling, or flux modeling. Alternatively, even in the absence of new experimental and computational approaches, the story could be made more complete by further leveraging the trans-omic network to provide insights into (a) the regulation of energy metabolism; and (b) the impacts of key disrupted metabolites (see comments 7-9). The study is also limited in its demonstrating the power of these methodologies to provide integrative insights. As mentioned above, the integration of enzyme levels and metabolite levels is clearly useful (Figure 3). In contrast, the utility of the mRNA and transcription factor layers was not evident. The study did not appear to improve or expand upon trans-omic network methodology described in the previous works. Finally, the various analyses (analyzing the trans-omic network for nodes with the highest degree centrality, the PPI analysis, and viewing the energy metabolism pathways in the network) provided disparate results that were only tenuously connected in the discussion section.

References

1. Yin F. Lipid metabolism and Alzheimer's disease: clinical evidence, mechanistic link and therapeutic promise. FEBS J. 2023;290(6):1420-1453. doi:10.1111/febs.16344
2. Ju Y, Li S, Kong X, Zhao Q. Exploring fatty acid metabolism in Alzheimer's disease: the key role of CPT1A. Sci Rep. 2024;14(1):31483. doi:10.1038/s41598-024-82999-z
3. Sienski G, Narayan P, Bonner JM, et al. APOE4 disrupts intracellular lipid homeostasis in human iPSC-derived glia. Sci Transl Med. 2021;13(583):eaaz4564. doi:10.1126/scitranslmed.aaz4564
4. Zhang C, Rissman RA, Feng J. Characterization of ATP Alternations in an Alzheimer's Transgenic Mouse Model. J Alzheimers Dis JAD. 2015;44(2):375-378. doi:10.3233/JAD-141890
5. Jia D, Wang F, Yu H. Systemic alterations of tricarboxylic acid cycle enzymes in Alzheimer's disease. Front Neurosci. 2023;17:1206688. doi:10.3389/fnins.2023.1206688
6. Sang C, Philbert SA, Hartland D, et al. Coenzyme A-Dependent Tricarboxylic Acid Cycle Enzymes Are Decreased in Alzheimer's Disease Consistent With Cerebral Pantothenate Deficiency. Front Aging Neurosci. 2022;14. doi:10.3389/fnagi.2022.893159
7. Patel V, Mill J, Okonkwo OC, Salamat S, Li L, Raife T. Global Energy Metabolism Deficit in Alzheimer Disease Brain. J Prev Alzheimers Dis. 2024;11(1):171-178. doi:10.14283/jpad.2023.91
8. Egami R, Kokaji T, Hatano A, et al. Trans-omic analysis reveals obesity-associated dysregulation of inter-organ metabolic cycles between the liver and skeletal muscle. iScience. 2021;24(3):102217. doi:10.1016/j.isci.2021.102217
9. Bai Y, Morita K, Kokaji T, et al. Trans-omic analysis reveals opposite metabolic dysregulation between feeding and fasting in liver associated with obesity. iScience. 2024;27(3):109121. doi:10.1016/j.isci.2024.109121

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Reply to the reviewers

Manuscript number: RC- 2025-03341

Corresponding author(s): Thomas, Leonard

1. General Statements [optional]* *

The reviews are positive, constructive, and balanced. The reviewers highlighted the novelty, scope, technical rigor, and strength of evidence of the study. The reviewers also noted the technological advance in modeling of multi-domain proteins that we report. In summary, there are two major advances reported in this study, both of which have important implications, both within the field of lipid signaling and in the broader field of in silico structural modeling.

Lipid signaling. We have elucidated the mechanism by which a protein kinase is allosterically activated by a specific lipid second messenger (PIP3) at atomic resolution. To the best of our knowledge, this has not been achieved for any kinase to date. Our findings have implications for (a) the spatial and temporal confinement of Tec signaling in cells by PIP3, (b) the rationalization of disease-causing mutations in XLA, and (c) the development of novel therapeutics that could be of clinical value in the treatment of B-cell malignancies. As such, we believe that this study will be of interest to a wide spectrum of basic scientists in the cell signaling community, as well as translational, and clinical scientists.

__In silico structural modeling. __Whilst developed primarily to answer the biological question of PIP3-mediated activation of the Tec kinases (see above), the improvement in AlphaFold modeling that we report has significant implications for all scientists concerned with structural modeling in silico, specifically with respect to the modeling of both multi-domain proteins and protein complexes. Given the widespread adoption of AlphaFold as a hypothesis generator, the audience for which these developments are relevant is actually very large, transcending all fields of the biological sciences.

2. Description of the planned revisions

• *The major suggestion made by reviewers #2 and #3 was the inclusion of a negative control in the lipid nanodisc assays (Figure 5) to confirm that it is PIP3 that specifically activates MbTEC. This is a constructive and valuable addition to our study, particularly in light of the fact that PI(4,5)P2 is present in cells at 2-4 orders of magnitude greater concentration than PIP3. This experiment will be combined with reviewer #2's suggestion to perform a PIP3 titration in the lipid nanodiscs.

• *

Reviewer #2____

Although the nanodisc experiments clearly show PIP3-dependent activation, titrating the PIP3 content in nanodiscs (e.g., 0.1%, 0.5%, 1%, 3%, 5% of PIP3) to determine whether MbTEC activation shows a graded response to lipid abundance would strengthen the conclusions. This would support the suggested allosteric mechanism and aid in differentiating between digital and analogue activation behaviour.

• We thank the reviewer for the nice suggestion, which we will combine with the negative control suggested by the reviewer in the next comment.

A good negative control for Figure 5C, would be a nanodisc containing another phosphoinositide. Given prior evidence that TEC-family PH domains display selectivity for PIP3, it would nevertheless be informative to test nanodiscs containing other phosphoinositides (e.g., PI(4,5)P2, PI(3,4)P2, and PI3P).

• See response above. Reviewer #3

Fig 5B/C: The nanodisc experiment lack some controls. In order to conclude that PIP3 is indeed critical for the observed enhance autophosphorylation of MbTEC, nanodiscs with e.g. PI3P, PI4P or PI5P should be used that are not expected to bind the MbTEC PH domain with high affinity. Likewise, or alternatively, a mutant PH domain with largely reduced PIP3 binding affinity would support trust in this central result of the paper. (estimated time investment: 1-2 months).

• We appreciate the reviewer's suggestion, which was also proposed by reviewer #2. These experiments are planned as the number one priority (see response above).

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

Reviewer #1

Major comment: We think the proposal is overall coherent and reasonable and found it interesting. It is not, however, conclusive. Modeling played a key role in supporting this proposal, but the modelling itself was dependent on choices of parameters made by the authors. The reported AlphaFold 3 model depended on a customized MSA strategy: the authors report divergent placement of the PH domain with respect to the kinase domain in their AlphaFold 3 runs. In light of this observation they used a manually curated TEC family MSA with taxonomic reweighting. This helped the model convergence but it introduced arbitrarity in the modeling step.

• We believe that it is necessary to clarify what exactly our custom AF pipeline does so as to avoid confusion, but also to render our work more impactful for future studies that employ AlphaFold. The divergent placement of the PH domain in AF's standard configuration arises from the inclusion of sequences in the MSA that do not belong to the Tec gene family (Supplementary Figure 4C) but are structurally related at the individual domain level and therefore identified by the profile Hidden Markov Models used by AF to generate deep MSAs. These sequences are unrelated to Tec phylogenetically and therefore have evolved under different selection pressures. What our custom pipeline does is exclude these sequences from the MSA, such that the evolutionary covariance signature exploited by AF to guide inter-residue distance restraints comes only from bona fide Tec sequences. In a second step, we sample the sequences to ensure taxonomic balance (sequence databases are heavily biased in terms of taxonomic representation). This step increases sequence diversity and, with it, the strength of the co-variance signal. Therefore, rather than introducing "arbitrariness" in the modeling, we actually reduce it.

• Since the advance that we report in modeling multi-domain proteins with AlphaFold is applicable to all multi-domain proteins and protein complexes, we believe that it is valuable to convey the significance of the input MSA in as clear a fashion as possible. To illustrate why AlphaFold fails in its standard configuration, we have therefore performed an in silico analysis of the MSA automatically generated by AF when it is prompted to predict the structure of MbTec. We now include this analysis as a new Supplementary Figure (Supplementary Figure 4C). As can be seen, of the 50,000 sequences in the AF3-generated MSA, only 1,898 contain the complete set of regulatory PH, SH3, SH2 and kinase domains that characterize the Tec kinases. The remaining 48,102 sequences, while containing one or more of the individual domains found in Tec, are phylogenetically unrelated. This means that the co-variance signature that AF relies upon for accurate prediction of inter-domain interactions is contained in

  Minor comment: In two places the authors wrote "PIP3 is necessary and sufficient for both MbTEC activation and inactivation." This seems logically impossible. Revision is required.

• We appreciate the reviewer's confusion here. This conclusion stemmed from the observation that PIP3 engagement is sufficient to promote full activation of MbTec on lipid nanodiscs in vitro (the synergistic effect of the hydrophobic stack mutation is lost in this context due to the presence of the polyproline motif in the PH-SH3 linker). However, in vivo, the SH2 domain is essential for BTK activation (by mediating its recruitment to activated receptors) and therefore it is incorrect to state that PIP3 is necessary and sufficient. It is necessary, but not sufficient - this is, again, analogous to an AND gate in an electronic circuit. We have revised the manuscript accordingly. Significance

It attempted to clarify the role of the PH domain in TEC activation from a mechanistic perspective. If confirmed, it can potentially lead to novel approaches of drug discovery targeting TEC kinases.

• Whilst we shied away from a discussion of therapeutic potential in our discussion to avoid unnecessary hype, the reviewer raises an important point, especially in light of the recent clinical success of BTK inhibitors in treating B-cell malignancies. As such, we have used the request made by Reviewer #2 to compare MbTec with Akt to highlight the potential for a new therapeutic modality in Tec kinase inhibition. The recent FDA approval of Capivasertib (November, 2023), an allosteric inhibitor of Akt, for the treatment of hormone-receptor (HR) positive, HER2-negative advanced or metastatic breast cancer provides a nice proof-of-concept. This discussion can be found in the response to Reviewer #2. Reviewer #3 also alluded to the "blockbuster drugs" used to treat B-cell malignancies, so we felt it appropriate to at least comment on the potential implications of our findings for the development of novel therapeutics. Reviewer #2

• The inference for Figure 3 that PH domain exerts a strong autoinhibitory influence on kinase activity that cannot be overcome by disruption of the SH3-kinase interaction would benefit from further clarification. It is not immediately clear from the data that PH-domain-mediated inhibition should be seen as dominant rather than synergistic with SH3-kinase linker interactions. Although the autophosphorylation stoichiometry was measured for MbTEC32K L396A and MbTECFL L396A, a more thorough quantitative evaluation of the relative contributions of PH-domain removal versus SH3-linker disruption would be possible if this analysis were extended to MbTEC32K. Discussing whether these inhibitory components might instead work together/cooperatively to limit kinase activity or is it one dominant over the other , the authors are urged to thoroughly explain the reasoning behind the conclusion provided.

• The reviewer raises an interesting question regarding the relative contributions of the various regulatory domains to autoinhibition. Ultimately, what our data show, both for MbTec autophosphorylation and substrate phosphorylation, is that disruption of the SH3-kinase interface results in kinase activation. The amplitude of the activation, however, is dependent on whether the PH domain is present or not. In the presence of the PH domain, the activation is very modest, whereas when it is removed, the amplitude is an order of magnitude greater. This reflects the fact that SH3 domain displacement without PH domain displacement does not permit acquisition of a conformation compatible with activation loop autophosphorylation. This implies that PIP3-dependent allosteric activation is a prerequisite for complete activation of Tec. PH domain deletion is also not permissive for complete activation, which requires SH3 domain displacement on top to drive autophosphorylation, an observation consistent with previous experimental data on Src. As the reviewer indicates, these are synergistic with one another - Tec is a coincidence detector of multiple signals, all of which are required for full activation. Our conclusion that the inhibitory influence of the PH domain cannot be overcome by displacement of the SH3 and SH2 domain, however, is important, since it strongly implies that PIP3 is necessary for Tec activation (i.e. that Tec is an AND gate and not an OR gate). We have revised our description of these results to better reflect the relative contributions of the various regulator domains:

"These observations indicate that the PH and SH3 domains exert synergistic inhibitory effects on the kinase domain and that disengagement of both domains by ligand binding is required for complete activation of MbTec. This is the equivalent of an AND gate in an electronic circuit, as opposed to an OR gate."

It would also be valuable if the authors in the discussion section can draw a contrast with PIP3-dependent activation mechanism of AKT. This would be helpful in highlighting the uniqueness of PIP3 dependent TEC activation.

• We thank the reviewer for highlighting the value of comparing MbTec to Akt, for which the activation mechanism has been intensively studied, both in our lab and in many others. There are, indeed, some interesting similarities, which we now comment on in the following paragraph, which has been incorporated into our discussion section: "It is worth noting that the regulation of MbTec by PIP3 is analogous, although not entirely homologous, to the regulation of the Ser/Thr kinases Akt and PDK1. Like Tec, Akt and PDK1 contain PIP3-sensing PH domains which mediate autoinhibition of their respective kinase domains (PMIDs: 28157504 and 35387990). Although the autoinhibitory interfaces of Tec and Akt are structurally different, both interfaces impair activation loop phosphorylation and substrate binding, as well as PIP3 binding (PMIDs: 28157504, 29632185, 3438531). The specific autoinhibitory conformation of Akt has been exploited in the development of allosteric inhibitors, which exhibit significantly improved on-target specificity and have recently been approved for the treatment of cancer (PMID: 38592948). As such, our findings open a new potential therapeutic modality for the development of selective Tec kinase inhibitors. Given the recent success of ATP-competitive BTK inhibitors in treating B-cell malignancies (PMIDs: 26639149, 36511784), there is enormous therapeutic potential."

*Minor Comments

*

Y579 and R581 comes without a significant context. Can the authors elaborate on these residues a bit.

• We have tried to better introduce the rationale behind mutation of these residues by rephrasing this part of the results. The changes from the previous version are underlined:

"Consistent with the loss of an energetically favorable interface, deletion of the PH domain resulted in a 6{degree sign}C reduction in thermal stability (Figure 2F, Supplementary Figure 6C). We next tested the specificity of the predicted PH-kinase interaction by mutating Y579 and R581, which are conserved residues in the interface (Figure 2G). Mutation of Y579 and R581 to alanine reduced thermal stability by 3{degree sign}C, while their mutation to asparate and glutamate respectively resulted in the same thermal stability as MbTEC32K lacking its PH domain (Figure 2F, Supplementary Figure 6D). These observations indicate that substitution of Y579 and R581 with alanine weakens the autoinhibitory conformation by reducing van der Waals contacts, but substitution with charged residues that introduce unfavorable interactions is sufficient to completely disrupt the interface. Consistently, MbTEC32K bound to the PH domain with an affinity of 4.0 mM, but binding of MbTEC32K Y579D R581E was barely detected (Figure 2H)." +

Figure 2H - In the legend make wt as WT so that it matches the figure panel

• Fixed.

• Supplementary Figure 1J - Adjust the orientation of intensity on y axis

• Fixed (now Supplementary Figure 2J).

• Supplementary Figure 1H - In the figure it should be Y579 and R581

• Fixed (now Supplementary Figure 2H).

• Can the authors add that 5C is the representative autoradiographs for each construct from panel 5B. Make it clear.

• Fixed.

• Write the units for intensity on the y axis for the entire supplementary figure 1 • Supplementary Figure 2J and 2K - Make the 6 subscript in the legend for Gly 6.

• Fixed (now Supplementary Figure 3J-K).

• Can the authors include RRID wherever applicable in the methods section.

• We have added in the RRID reference for the cell line employed in this study.

• Include a space between i and was in the sentence " Each sequence iwas assigned a raw weight .

• Fixed.

• I think MSA is coming twice in the line above structure inference in the methods section. MSAs is repeating after balanced MSA. Kindly look into it.

• Fixed.

  The work has been done using the TEC kinase from the choanoflagellate M.brevicollis, presumably for practical reasons of expression and purification. PIP3 signalling, to my knowledge, has not formally been demonstrated in choanoflagellates. This remains a concern in respect of the relevance of these findings to true metazoans which is the setting in which Class I PI3kinase generated PIP3 signalling is seen.

• We appreciate the reviewer's concerns regarding the relevance of our findings to PIP3 signaling in metazoans. Whilst the production and sensing of PIP3 has not formally been demonstrated in a choanoflagellate, we believe that sufficient circumstantial evidence exists that should allay these concerns. Specifically:

• Evolutionary evidence exists for the presence of the PI3K machinery in the last eukaryotic ancestor (LECA) (PMID: 26482564), approximately 1.2-1.8 billion years ago. Choanoflagellates, are, by comparison quite young (600-650 My).
• Choanoflagellates have an extensive tyrosine kinase signaling network, including RTKs (PMID: 18621719)
• PI3K/PIP3/PTEN signaling has been robustly demonstrated in organisms that predate choanoflagellates by hundreds of millions of years, including Amoebozoa e.g. D. discoideum and E. histolytica (PMIDs: 9778249, 11352940, 12062103, 12062104, 12802064).
• Monosiga brevicollis encodes:
• class I PI3K p110 and p85 homologs (Manning et al, PNAS 2008)
• a PTEN homolog
• note that class I PI3Kd is responsible for the plasma membrane PIP3 signal in metazoan immune cells, meaning that a homolog of this enzyme is present in choanoflagellates
• Choanoflagellates encode homologs of metazoan proteins that are known to respond specifically to PIP3, including:
• MbTec
• PDK1 (NCBI Reference Sequence: XP_004995400.1)
• Akt (NCBI Reference Sequence: XP_001743446.1)
• A recent kinase inhibitor screen in the choanoflagellate S. rosetta revealed the activity of known PI3K inhibitors (regulation of growth, phosphotyrosine signaling etc) (PMID: 40226336)
• Conclusion: choanoflagellates inherited an ancient lipid-signaling toolkit.
• Nevertheless, we believe that the reviewer makes an important point that is important to clarify for the uninitiated reader. We therefore propose the following additional paragraph to our discussion section that deals explicitly with these concerns:

"Although PIP3 signaling has not been explicitly demonstrated in a choanoflagellate, the machineries for its production predate choanoflagellates by at least 500 My (PMID: 26482564). PI3K-mediated production, PH domain-mediated sensing, and PTEN-mediated degradation of PIP3 have all been robustly demonstrated to control chemotaxis in the slime mold Dictyostelium discoideum (PMIDs: 9778249, 11352940, 11389841, 12062103, 12062104, 12802064). While the Tec kinases emerged more recently (PMID: 30183386), PI3K, PTEN, PDK1, and Akt are all found in choanoflagellates, suggesting that choanoflagellates inherited an ancient lipid signaling toolkit and that the Tec kinases were a novel evolutionary addition to the toolbox."

Reviewer #3____

Points to be addressed:

Fig 1B: For the sequence alignment, a few more residues before/after the four critical selected residues should be shown. This allows the reader to evaluate how conserved these residues really are. (estimated time investment: ~1 day max.)

• Figure 1B is not actually a conventional sequence alignment, since it shows four residues that are structurally related, but not found in a contiguous sequence. However, we have added a new Supplementary Figure panel (Supplementary Figure 1A) to show the sequence motifs for each residue.

  Fig. 2 I/J/K: It is more customary to show HDX-MS results mapped on a structural cartoon representation (and not surface representation). The current representation makes it impossible to see which functional areas of the different domains show increased/decreased HDX. In addition, mapping HDX changes on a linear sequence/sec structure plot (as also commonly used to represent HDX-MS data) should be shown in SI. (estimated time investment: Reviewer #1

This is important because the whole thesis of this manuscript rest on the model's suggestion that the kinase domain sequesters the PIP3 binding site of the PH domain. The authors found that in cells full-length MbTEC transiently associated with the membrane but the isolated PH domain enjoyed more prolonged membrane association. The authors interpreted this difference in membrane association in terms of different sequestration of the PIP3-binding PH domain by the kinase domain, but the PH-kinase interaction is based on a model and it needs further validation.

• Model validation, particularly in the era of AlphaFold, is critical, as the reviewer correctly notes. However, we dispute the reviewer's assertion that the PH-kinase interface derived from our model needs further validation. The following is a summary of all the orthogonal ways in which we validated the model. In terms of publishing standards, we believe we have exceeded what is widely accepted as robust evidence for a specific interface.
• The pair-alignment error (PAE) plot (Figure 1H) exhibits prediction errors in the PH-kinase interface which are (a) extremely low and (b) comparable with those in the SH3-kinase, SH2-kinase, and SH3-SH2 interfaces, all of which are superimposable with experimental structures.
• Comparison of the model with experimental small-angle X-ray scattering (SAXS) in solution revealed a near-perfect fit (Figure 2A). This demonstrates that the global conformation of the model is an accurate reflection of the conformation of MbTEC in solution.
• Mutation of the interface on the kinase side leads to a loss of thermal stability equivalent to deletion of the PH domain (Figure 2F-G) and a failure to bind the PH domain in trans (Figure 2H).
• Changes in HDX-MS of the interface-mutated protein (Figure 2I-L) are comparable to those in the PH domain-deleted construct (Supplementary Figure 6E-J).
• Reciprocal mutation of the interface on the PH domain leads to a reduction in binding affinity for the SH3-SH2-kinase (32K) protein (Figure 4C).

While autophosphorylation is dramatically enhanced by PIP3 containing nanodiscs, the interpretation can be complicated, as the manuscript itself acknowledged that membrane based experiments cannot readily deconvolute local concentration effects from allosteric effects, because concentrating proteins on a membrane can promote dimerization dependent autophosphorylation.

• It is precisely for these reasons that we conducted the experiments detailed in Figure 3, since they do not convolute allosteric activation with local concentration on a membrane. These experiments underpin our conclusions that MbTec is specifically activated by dissociation of its PH domain from the kinase domain and not just by local concentration on a PIP3-containing membrane. Whilst the experiments in Figure 3 do not say anything about the specificity of the PH-kinase interface (which we addressed with other experiments), they unambiguously confirm the inhibitory effect of the PH domain that other studies have reported previously. Reviewer #2

To elaborate on the point of sufficiency, can the authors utilise FRB-FKBP system to synthesize PIP3 ectopically and see if it leads to the recruitment of FL and PH in addition to PDGF stimulation. It will also be valuable if the authors can use PI3K inhibitors post PDGF stimulation to validate this point further. A colocalization with PIP3 biosensor post PDGF stimulation will also be a great control.

• The reviewer's suggestion to use the FKBP-FRB system to synthesize PIP3 ectopically is elegant but, in our opinion, not necessary. The specific recruitment of Tec kinases to the plasma membrane in response to growth factor-stimulated production of PIP3 is well established (e.g. Varnai et al, JBC 1999). As such, a PIP3 biosensor is not necessary, since the Tec kinases are well established PIP3 sensors in cells.

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Referee #3

Evidence, reproducibility and clarity

The 5 human TEC kinases are cytoplasmic tyrosine kinases containing a prototypic (Src-like) SH2-SH2-kinase domain module with critical roles in various signaling pathways, in particular T- and B-cell signaling. One Tec kinase family member, Btk, is the target of major blockbuster drugs that revolutionized outcome of patients with a variety of B-cell malignancies. While major insights into the structure and regulation of Tec kinases by phosphorylation, as well as intra- and inter-molecular protein-protein interactions could be obtained over the past 3 decades, the role and precise mechanisms of TEC kinase regulation by binding to phosphoinositides at membranes, via its PH-TH unit, are much less clear.

In this manuscript, the authors study the structure and regulation of an ancestral TEC kinase from the choanoflagellate M. brevicollis (MbTEC), which has a largely reduced set of tyrosine kinases (as compared to mammals), and therefore might offer a focused look on conserved essential kinase regulation that diversified and acquired cell-type specific fine-tuning during evolution. The manuscript first provides a nice workflow to obtain an accurate model of MbTEC using AlphaFold 3 modeling. SAXS supports the predicted compact conformation of MbTEC in solution. Removal of the PH domain resulted in lower thermal stability indicating an energetically favorable intramolecular interface, which was subsequently supported by HDX-MS measurements using full-length and 3 domain core (SH2-SH2-kinase domain: 32K) and possible PH-KD interface mutations of MbTEC. Kinase activity (autophosphorylation and substrate phosphorylation) assays support an autoinhibitory effect of the PH domain of MbTEC activation. Making use of a gain-of-function mutant, initially identified in human Btk PH domain, and in vitro experiments with nanodiscs containing PIP3 show strong activation of MbTEC autophosphorylation. Overall, the manuscript supports a model of PIP3-stimulated relief from PH domain-mediated autoinhibition of MbTEC resulting in full activation also involving disruption of the SH2-kinase linker interaction with the SH3 domain and displacement of the SH2 domain. The authors have used several different structural biology and biochemical assays, all of which allow for relatively precise (semi-)quantative answers to the underlying research questions. Hence, the claims and conclusions are very well supported and leave (very) little to be desired (see points below). This is a nice and clean structural biochemistry paper with generally well controlled experiments and appropriate choice of research methods. The manuscript text is well written, previous work appropriately mentioned/discussed and results are carefully interpreted and gauged towards a final model.

Points to be addressed:

Fig 1B: For the sequence alignment, a few more residues before/after the four critical selected residues should be shown. This allows the reader to evaluate how conserved these residues really are. (estimated time investment: ~1 day max.) Fig. 2 I/J/K: It is more customary to show HDX-MS results mapped on a structural cartoon representation (and not surface representation). The current representation makes it impossible to see which functional areas of the different domains show increased/decreased HDX. In addition, mapping HDX changes on a linear sequence/sec structure plot (as also commonly used to represent HDX-MS data) should be shown in SI. (estimated time investment: <1 week) Fig 5B/C: The nanodisc experiment lack some controls. In order to conclude that PIP3 is indeed critical for the observed enhance autophosphorylation of MbTEC, nanodiscs with e.g. PI3P, PI4P or PI5P should be used that are not expected to bind the MbTEC PH domain with high affinity. Likewise, or alternatively, a mutant PH domain with largely reduced PIP3 binding affinity would support trust in this central result of the paper. (estimated time investment: 1-2 months).

Significance

MbTEC kinase structure and regulation has not previously been studied. Hence, novelty is very good. Given the overall conservation of the structure and regulatory mechanisms of TEC kinases (and related SRC and ABL kinases), as well as the large number of prior studies on these kinases (by Prof. Leonard and several others in the field), many aspects of this study are not overly surprising and more confirmatory than groundbreaking. On the other hand, it is a well-controlled and experimentally "clean" study. It uses a state-of-the-art combination of modern structural/biochemical methods, provides some important technological advance to reliably model multi domain signaling proteins using AlphaFold 3. The detailed dissection of MbTEC regulation provides some novel aspects and offers a convincing model for TEC kinase activation with implications for the human/mouse protein. I am convinced that the manuscript will be of interest for the broader signaling community, as well as basic scientists in the fields of structural biology and membrane cell biology.

I do have sufficient expertise to evaluate this manuscript, as I have used essentially all of the described methods in my lab before and have been working on proteins related to MbTEC for my entire scientific career.

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Referee #2

Evidence, reproducibility and clarity

Overall Summary

The authors have tried to put forward a comprehensive structural and biochemical analysis of an ancestral TEC kinase from Monosiga brevicollis (MbTEC). The authors have used a wide array of state-of-the art approaches such as protein biochemistry, mutagenesis, thermal stability assays, SAXS, AlphaFold 3 modeling with curated MSAs, HDX-MS, kinase assays, lipid nanodiscs, mass spectrometry, and cell-based imaging to propose a detailed mechanism for autoinhibition of MbTEC and PIP3-dependent allosteric activation.

Overall Comment

The overall study presented is quite scientifically challenging and conceptually ambitious. The authors are to be commended for coming up with a manuscript with impressive technical rigor , experimental thoroughness and care with which the manuscript is written and presented.

Major Comments

1. The inference for Figure 3 that PH domain exerts a strong autoinhibitory influence on kinase activity that cannot be overcome by disruption of the SH3-kinase interaction would benefit from further clarification. It is not immediately clear from the data that PH-domain-mediated inhibition should be seen as dominant rather than synergistic with SH3-kinase linker interactions. Although the autophosphorylation stoichiometry was measured for MbTEC32K L396A and MbTECFL L396A, a more thorough quantitative evaluation of the relative contributions of PH-domain removal versus SH3-linker disruption would be possible if this analysis were extended to MbTEC32K. Discussing whether these inhibitory components might instead work together/cooperatively to limit kinase activity or is it one dominant over the other , the authors are urged to thoroughly explain the reasoning behind the conclusion provided.
2. To elaborate on the point of sufficiency, can the authors utilise FRB-FKBP system to synthesize PIP3 ectopically and see if it leads to the recruitment of FL and PH in addition to PDGF stimulation. It will also be valuable if the authors can use PI3K inhibitors post PDGF stimulation to validate this point further. A colocalization with PIP3 biosensor post PDGF stimulation will also be a great control.
3. Although the nanodisc experiments clearly show PIP3-dependent activation, titrating the PIP3 content in nanodiscs (e.g., 0.1%, 0.5%, 1%, 3%, 5% of PIP3) to determine whether MbTEC activation shows a graded response to lipid abundance would strengthen the conclusions. This would support the suggested allosteric mechanism and aid in differentiating between digital and analogue activation behaviour.
4. A good negative control for Figure 5C, would be a nanodisc containing another phosphoinositide. Given prior evidence that TEC-family PH domains display selectivity for PIP3, it would nevertheless be informative to test nanodiscs containing other phosphoinositides (e.g., PI(4,5)P2, PI(3,4)P2, and PI3P)
5. It would also be valuable if the authors in the discussion section can draw a contrast with PIP3-dependent activation mechanism of AKT . This would be helpful in highlighting the uniqueness of PIP3 dependent TEC activation.

Minor Comments

• Y579 and R581 comes without a significant context. Can the authors elaborate on these residues a bit.
• Figure 2H - In the legend make wt as WT so that it matches the figure panel
• Supplementary Figure 1J - Adjust the orientation of intensity on y axis
• Supplementary Figure 1H - In the figure it should be Y579 and R581
• Can the authors add that 5C is the representative autoradiographs for each construct from panel 5B. Make it clear.
• Write the units for intensity on the y axis for the entire supplementary figure 1
• Supplementary Figure 2J and 2K - Make the 6 subscript in the legend for Gly 6.
• Can the authors include RRID wherever applicable in the methods section.
• Include a space between i and was in the sentence " Each sequence iwas assigned a raw weight .
• I think MSA is coming twice in the line above structure inference in the methods section. MSAs is repeating after balanced MSA. Kindly look into it.

Significance

General assessment

This is a study on the TEC family of kinases that have an important role in the immune cells. Thus, alterations in their function is linked to both primary immunodeficiency as well as hematological malignancies. Thus understanding their mechanism of activation is of fundamental importance understanding protein kinase regulation as well as developing potential therapy for blood cell disorders.

The work has been done using the TEC kinase from the choanoflagellate M.brevicollis, presumably for practical reasons of expression and purification. PIP3 signalling, to my knowledge, has not formally been demonstrated in choanoflagellates. This remains a concern in respect of the relevance of these findings to true metazoans which is the setting in which Class I PI3kinase generated PIP3 signalling is seen.

Advance

This study advances details of the molecular mechanism by which PIP3 interacts with and regulates TEC kinase function. This is a study in basic structural biology.

Audience

This study will be of interest to structural biologists and those with an interest in understanding phosphoinositide regulated protein function.

My expertise

Biochemistry and cell biology, phosphoinsoitde signalling

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Referee #1

Evidence, reproducibility and clarity

Summary: This manuscript focuses on PIP3 dependent activation in TEC family kinases. It used the choanoflagellate Monosiga brevicollis TEC kinase MbTEC as the model system. The authors proposed that MbTEC adopts a compact solution conformation in its autoinhibited state, with the PH domain bound with the kinase domain. Based on a AlphaFold3 model, the PH-kinase interaction was proposed to sequester the PIP3 binding site of the PH domain, hindering the membrane interaction of the PH domain, and in turn disrupting TEC activation. The study organized data collected from many different experiments, including structure modeling, solution measurements, mutagenesis, activity assays, in vitro membrane reconstitution, and cellular localization assays.

Major comment: We think the proposal is overall coherent and reasonable and found it interesting. It is not, however, conclusive. Modeling played a key role in supporting this proposal, but the modelling itself was dependent on choices of parameters made by the authors. The reported AlphaFold 3 model depended on a customized MSA strategy: the authors report divergent placement of the PH domain with respect to the kinase domain in their AlphaFold 3 runs. In light of this observation the they used a manually curated TEC family MSA with taxonomic reweighting. This helped the model convergence but it introduced arbitrarity in the modeling step. This is important because the whole thesis of this manuscript rest on the model's suggestion that the kinase domain sequesters the PIP3 binding site of the PH domain. The authors found that in cells full-length MbTEC transiently associated with the membrane but the isolated PH domain enjoyed more prolonged membrane association. The authors interpreted this difference in membrane association in terms of different sequestration of the PIP3-binding PH domain by the kinase domain, but the PH-kinase interaction is based on a model and it needs further validation. While autophosphorylation is dramatically enhanced by PIP3 containing nanodiscs, the interpretation can be complicated, as the manuscript itself acknowledged that membrane based experiments cannot readily deconvolute local concentration effects from allosteric effects, because concentrating proteins on a membrane can promote dimerization dependent autophosphorylation.

Minor comment: In two places the authors wrote "PIP3 is necessary and sufficient for both MbTEC activation and inactivation." This seems logically impossible. Revision is required.

Significance

It attempted to clarify the role of the PH domain in TEC activation from a mechanistic perspective. If confirmed, it can potentially lead to novel approaches of drug discovery targeting TEC kinases.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this paper, the authors combine advanced quantitative mass spectrometry-based proteomics with the PRIMMUS cell sorting technique to profile cell cycle proteins across the G1, S, and G2/M phases in CD8 T cells, embryonic stem cells (mESCs), and NIH3T3 fibroblasts. Their well-designed experimental approach-avoiding artifacts from synchronization-yields an impressive and detailed dataset on cell cycle dynamics. The experimental approach to interrogate three different cell lines for cell cycle protein dynamics, without using synchronization, is technically excellent. The data extracted from that initial experiment, which is shown in figures 2, 3, 4 and 5, is clearly described and well presented.

My concern is with conceptual advance of study. The author set out to determine how cell cycle control mechanisms could give rise to rapid proliferation in CD8 t cells, but it is not clear they have addressed that question. The data do not clearly support a model in which mESCs or CD8 T cells exhibit dampened cell cycle protein periodicity compared to 3T3 fibroblasts, nor for a change in APC/C being a key driver. Notably, the depletion of Emi1 appears to most significantly impact later cell cycle stages, as has been reported previously by others, and thus it is unclear that in this system it is promoting S-phase entry. And, while the impact on re-replication is clear, this is a very well reported phenotype. Overall, I am very impressed by the technical aspects of the study, but thought the authors could put more effort toward developing more meaningful interpretations of the data, which felt under-developed.

Comments and recommendations:

• There does not appear to be any statistical comparative analysis accompanying the proteomics data. While the differences highlighted in the text are generally clear from the figures, including statistical comparisons would strengthen the analysis and provide greater confidence in the reported findings.
• It is unclear what the box and whiskers represent in these plots. By convention, box plots typically display the interquartile range, with the central line indicating the median and the whiskers representing the minimum and maximum values or a defined range. If the authors are using a different convention, it should be clearly stated in the figure legends. Alternatively, I recommend using a different data representation to avoid potential confusion.
• Line 133 and figure 2B and D. It's unclear to me what 'common cell cycle regulated protein' are. The methods: "Fold changes were calculated and ANOVAs performed to identify significantly changing proteins in each cell line using the following filtering criteria: p < 0.05 and fold change > 2." does not fully clarify the analysis. For example, it's not clear what the fold changes are being compared to-is it a specific cell cycle phase, a baseline, or another reference point? Additionally, is the reported p-value corrected for multiple hypothesis testing? Overall, the methodology could benefit from further clarification.
• In Figure 2B, it is unclear how the data are normalized. Is it appropriate to compare values across rows, columns, or both? Additionally, the ordering of the CD8 T cell G2/M samples appears to be ascending from top to bottom-what is the rationale behind this ordering? Clarifying the normalization method and how to interpret comparisons within the figure would help improve its readability. As it is now, I am not clear on how this data supports the statement where it is called in the text "There was a core set of 121 proteins that were consistently cell cycle regulated across all three cell types" (lines 130-132). It would be interesting to know how these data compare the authors prior proteomics data on cell cycle proteins and to that of authors.
• In Figure 2C, are these the most frequent GO terms among the "cell cycle-regulated proteins"? It is unclear whether this represents a curated list of commonly known cell cycle-related terms or if these are the top GO terms identified through enrichment analysis. Clarifying this distinction would help readers better understand how these terms were selected and what the figure is intended to convey.
• The interpretation of differences in some APC/C components is not clear to me, particularly given the relationship to APC/C substrate expression. For example, ANAPC10 is down in CD8 cells, but the APC/C appears highly active given the high differential between substrate abundance between G1 and S/G2/M cells.
• I have some concerns regarding the Emi1 knockout experiments. First, the knockout does not appear to be particularly efficient. In addition, the results do not necessarily support the proposed conclusion. If Emi1 was a key driver of G1/S progression, I would think you would observe more 2N cells, not fewer. The relationship to DNA damage, made in Fig 6f is unclear.
• In the flow cytometry data in Figure 6C, the Emi1 knockout cells are EdU-positive and have >4N DNA content. This is consistent with a re-replication phenotype and for a vital role of Emi1 in preventing re-activation of the APC/C in late S or G2 phase. It is difficult to square this with the assertion that it is promoting G1/S progression. Notably, this is a well reported Emi1 phenotype.

Minor comments:

• Some figures lack error bars (e.g., Figures 2C, 2D, and 5A). I also recommend including individual data points on all graphs, as this is now required by many journals. Since most of the graphs likely represent experimental triplicates, adding these elements should be straightforward and will allow readers to see actual spread of the data.
• The terminology used to refer to CD8 T cells is inconsistent across the manuscript-for example, "CD8T" in Figure 2 and "CD8" in Figure 3. Standardizing this terminology throughout the figures and text would improve clarity.
• The authors frequently refer to "increases in pRB-," which is somewhat confusing. I recommend rephrasing this as "decrease in pRB" to make the interpretation clearer and easier to follow.

Significance

Significance and Advance

Strength: Excellent deep, quantitative proteomic dataset of cell cycle proteome dynamics across three independent cell lines. Done without chemical or other synchronization. This incrementally improves on previous proteomics datasets.

Weaknesses: Limited conceptual advance in our understanding of cell cycle proteomes, or insight into how different cell types proliferate at different rates.

Audience: interested audiences include those study cell cycle control, proteomics.

My expertise: cell cycle control and protein dynamics.

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Referee #2

Evidence, reproducibility and clarity

Summary

This study uses proteomics as an approach to understand regulatory mechanisms contributing to a short cell division cycle in CD8 T cells. While the cell cycle machinery has been studied in mouse embryonic stem cells (mESCs) and these discoveries have provided a framework for understanding atypically short cell cycles, whether those mechanisms are conserved in other cell types that undergo a short cycle has not been clear. Analysis of the cellular proteome was performed at three different cell-cycle stages (G1, S, G2/M) and across three cell lines (CD8 T cells and mESCs and fibroblast 3T3 cells as comparators for short and normal cycles, respectively). An important innovation here is the application of a PRIMMUS protocol, which uses markers of cell cycle stage and sorting rather than treatments, such as inhibitors, that can have unwanted perturbations. The authors find both similarities and differences between CD8 T cells and mESCs. Of particular interest, CycE levels are constitutively high in both cell types with a short cycle compared to fibroblast cells, but APC/C substrates are uniquely lower during G1 in CD8 T cells. Using CRISPR knock-out, the APC/C inhibitor Emi1 is then implicated as a key regulator of G1/S control in CD8 T cells as well as phenotypic fate.

Major Comments:

Overall, the conclusions are fairly made from the data. In particular, the proteomics data and analysis are of high technical quality. The data and methods are clearly presented in a manner that could be reproduced, and experiments are, with one exception noted gere, performed with appropriate replicates and statistical analysis. I have only two major comments.

1. From the description of the CRISPR methods and results, the origin of the Emi 1KO cells used in all the experiments is unclear. Only one Emi1 KO sample or experiment is shown along with control in each panel. A number of questions should be answered in order to clarify. Was this sample originated from the total cells grown out of the gRNA treatment (and on which the TIDE analysis was performed)? If so, which exon was the gRNA targeting in the cells used in subsequent experiments? Were single clones ever grown? Ideally, experiments should be performed with multiple single clonal lines, and at least one from each exon used, if possible. Alternatively, a population generated from each of the two guids should be used in all the experiments as a proper biological replicate.

It may be that homozygous deletion of Emi1 is not possible because of the effects on proliferation. If so, the authors should comment on this along with why the protein level in Sup. Fig. 2b is still so high in the KO line. Considering the inefficiency of the overall KO, it is especially important to understand Emi1 expression throughout the polyclonal population to interpret the results. Are there some cells expressing normal levels and some cells expressing no Emi1? If monoclonal, are the observed effects from haploinsufficiency? More description of the method and caveats to the interpretation of results are needed here, and results would be made more robust if more than one clone or gRNA treatment were used. It would be expected this may take 2-3 months with reasonable resources to perform this additional analysis, if not done already. 2. OPTIONAL. One shortcoming of the manuscript is the lack of insights into why knock out of Emi1 leads to G1 arrest. Follow up experiments on the APC/C substrates in Fig. S1b or analysis of proteins that are upregulated or downregulated by Emi KO would increase the significance of the manuscript. These experiments may be time consuming and could be considered beyond the scope of this study, but they would increase the impact of the study.

Minor comments:

1. Some brief aspects of the methods could be added to the description of results to help improve clarity in a few places. For example, the threshold for including the 121 proteins in Fig. 2b and what antibodies were used for staining in the PRIMMUS approach would be important enough that it should be stated in results with no need to look up detailed method.
2. It should be clarified that in most cases, use of the term "abundance" in comparing protein levels is actually a relative abundance for a specific cell type. For example in the following sentence, relative and not absolute abundances are being compared : "In mESC, there was higher abundance in G1 phase compared to CD8 T cells and NIH3T3 (Fig.136 2d)." Clarifying upon first use of the term abundance would be sufficient.
3. In some of the protein abundance panels there does not appear to be any mark in the graph, which is consistent with there being no observation of protein. This absence of any observation should be made explicit in the figure captions.
4. It should be clarified with its first use (line 264) that "pRb" means phosphorylated Rb.

Significance

The key conclusions are significant in that they advance our understanding of how cell cycle regulatory mechanisms can be adapted in cell types with short cell cycles. Results are also relevant in particular for the biology of T cells, and the finding that Emi1 controls the cell cycle and cell fate in CD8 T cells is noteworthy. These represent advances in our mechanistic understanding of cell division. In addition to the significance of the conclusions, the greatest strength of the manuscript is the technical quality of the proteomics data and the fair conclusions drawn from them. The results will be of interest to scientists studying basic research in cell, immune, and cancer biology.

The greatest limitation of the study is the lack of insights into how Emi1 is driving S phase and how its loss leads to accumulation of cells in G1. This result is quite interesting, because it is opposite what may be expected considering the known function of Emi1 as an APC/C substrate inhibitor and the observation in Fig. 5 that APC/C substrates are similarly low in CD8 T cells and 3T3 cells. This discrepancy and the logic of testing Emi KO should at least be more thoroughly discussed, and additional experiments, as described above, would increase the impact of the study. A second limitation is the lack of conclusions from many comparisons of protein levels among the cell type and cell-cycle phases. For example, the significance of similarities and differences in levels of the Cdks (Fig. 4) and Cdh1 (Fig. 5) is left undiscussed.

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Referee #1

Evidence, reproducibility and clarity

In this study by Lewis and colleagues, the authors use highly quantitative proteomics to compare cell cycle patterns in T lymphocytes to mouse embryonic stem cells and differentiated fibroblasts. The work is significant because the cell cycle field has been dominated by only a few paradigms based on model systems such as yeasts, cancer-derived cell lines, and fibroblasts. The different cell cycles in other cell types have not been thoroughly investigated because they are less experimentally tractable. Prior studies have drawn conclusions about embryonic stem cells that turned out later to be primarily from attempts to induce synchronization prior to analysis. Here, the authors apply their previously-described method for detecting proteins according to cell cycle phase by flow-sorting and then mass spectrometry. They find expected cell cycle fluctuations in the three cell lines, but also a few unexpected differences. Primarily, cyclin E protein appears to be expressed at higher levels in the fast-proliferating mESCs and CD8 cells compared to NIH3TS and to be less cell cycle-regulated. The mechanism and functional relevance for this difference are not considered.<br /> The authors chose to focus several experiments on the APC/C ubiquitin ligase inhibitor, Emi1, which they find appropriately cell cycle-regulated in CD8 and mESCs but expressed at higher levels in CD8 cells. They show that CD8 differentiation is associated with cell cycle changes and that perturbing the cell cycle in CD8 cells affects their differentiation (which is not surprising). Altogether this study provides an excellent resource for the field from the detailed high-quality proteomics data sets (though see point #8). On the other hand, the experiments with EMI1-KO and differentiating cells seem largely unrelated to the cell cycle analysis itself; these results may be mostly indirect consequences of cell cycle perturbation rather than specific to EMI1 function. This is a very thorough, rigorous, and valuable proteomics characterization of cell cycle differences, but the choice of follow-up functional experiments isn't logical in my opinion.

Major points:

1. It is not clear how the quantification accounts for differences in cell size or nuclear/cytoplasmic fractions among the different cell types. For example, ESCs are typically small with relatively less cytoplasm. Since a great many cell cycle proteins are nuclear, normalizing to total protein analyzed and not cell number could make these proteins appear more abundant. In other words, does 1 ug of protein from mESCs represent the same number of cells or nuclei as 1 ug of protein from NIH3T3?
2. The motivation for the project was given as wanting to understand if fast-cycling CD8 T cells resemble fast-cycling mESCs, which the authors show they partially do. The molecular phenotype in common is cyclin E abundance, but we are left without an understanding for how that occurs. Are there differences in expression of the E3 ligase for cyclin E?
3. We also don't learn if the constitutive cyclin E is why cells cycle quickly because no experiments to change cyclin E are provided.
4. In an unexpected turn for the project, the authors generated inducibly Emi1-null CD8 T cells and analyzed them for replication, re-replication, and phosphorylated Rb. This section is fine, but the rationale isn't obvious, particularly if constitutive cyclin E (not an APC/C substrate) is the proposed driver of fast proliferation. Emi1 isn't the general reason for fast proliferation if it is only high during G1 for CD8 and not mESCs. Emi1 loss has also been known to promote re-replication for quite a few years, a finding the authors cite. The replication-dependent DNA damage and cell cycle arrest are both well-known outcomes from re-replication. So, although the data are of good quality, I'm not sure that showing Emi1 has the same role in CD8 cells as what was reported in other cells adds much to the field. The authors could choose to save Figure 6 for a more APC/C-focused study and use EMI1 as a general cell proliferation marker in Figure 7.
5. What is the cell cycle distribution of the IL-15 and IL-2 differentiated cells? If they are different, then some of the protein abundance changes to regulated proteins such as p21 might be a symptom of cell cycle differences rather than differentiation. It seems IL-15 is more cell cycle promoting form Figure S3, but that isn't clear from the assays presented.
6. The change in the CD62L marker is argued to be unrelated to cell cycle and somehow more directly downstream of Emi1. The connection here is tenuous, in part because there's no comparison to a similar cell cycle perturbation independent of Emi1. How would Emi1 modulate CD62L if CDC62L does not show evidence of being an APC/C substrate?
7. As presented, Emi1 has a unique effect on the immune phenotype. It is also possible that many cell cycle perturbations would similarly affect differentiation and not only Emi1. Can the authors distinguish Emi1-specific effects from more common cell cycle perturbation effects? Alternatively, interpreting the EMI1-KO data more generally could avoid confusion.
8. The authors should provide legends to the supplementary tables in the text and/or the tables themselves. Several column headers in the tables are not defined.

Minor points:

• a. Figure 4g is titled Cdkn2a (which would be p16) but the legend says its Cdkn1a (p21). The p21 protein was undetected in NIH3T3? One would expect it to be in the G1 cells at least.
• b. Line 56: cyclin E is not an APC/C substrate as implied by the text. If Skp2 is a bona fide substrate (not sure that's true), then APC/C activity would have opposite effects on Cyclin E vs Cyclin A.
• c. What is the red arrow in Figure 6C?
• d. Figure 7b is protein copy number whereas all other graphs are for ppm. The legend on line 686 has "cite immPRES" but this citation didn't make it into the submitted manuscript.

Significance

The work is significant because the cell cycle field has been dominated by only a few paradigms based on model systems such as yeasts, cancer-derived cell lines, and fibroblasts. The different cell cycles in other cell types have not been thoroughly investigated because they are less experimentally tractable. Prior studies have drawn conclusions about embryonic stem cells that turned out later to be primarily from attempts to induce synchronization prior to analysis. This is a very thorough, rigorous, and valuable proteomics characterization of cell cycle differences, but the choice of follow-up functional experiments isn't logical in my opinion.

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Reviewer #1

Evidence, reproducibility and clarity

Summary of findings and key conclusions This manuscript asks how pharmacologic targeting of the outer mitochondrial membrane protein MIRO1 (RHOT1) with a MIRO1-binding compound (MR3) reshapes immunosuppressive programs in the glioma tumor microenvironment (TME). The core of the paper is a cross-species transcriptomic comparison that combines an in vivo mouse dataset with an ex vivo human perturbation dataset. Model systems and approach (as described): • Mouse in vivo: GL261-Luc intracranial glioma in C57BL/6J mice; MR3 is administered intracranially at the implantation site (10 µM in 5 µL DMSO) on days 11 and 18, and tumors are harvested on day 22 for single-nucleus RNA-seq (snRNA-seq). • Mouse snRNA-seq: NeuN-based nuclei sorting, 10x Genomics v3.1; alignment to mm10; Seurat-based integration and annotation. Tumor-cell calling is supported by CNV inference (SCEVAN/CopyKAT). One MR3-treated sample is excluded after QC, leaving 3 control vs 2 MR3-treated samples (11,940 NeuN− nuclei). • Human ex vivo: freshly resected glioma cores from 3 patients are cultured with 10 µM MR3 or DMSO for 24 h, followed by bulk RNA-seq (STAR alignment to hg19; DESeq2 for differential expression). • Cross-species integration: the analysis is restricted to 1:1 orthologs and protein-coding genes shared across datasets; inferred cell-cell signaling is explored with CellChat. Main findings (as presented): • MR3 shifts expression of a subset of glioma-associated genes toward a non-tumor-like direction ("rescued genes") and is associated with large changes in inferred cell-type composition in the mouse snRNA-seq dataset (including a marked drop in the fraction of nuclei annotated as tumor: 44.5% to 4.3%; Fig. 1E). • Across TCGA-vs-GTEx (glioma-upregulated genes) and three MR3 response analyses (mouse snRNA-seq, mouse pseudo-bulk, and human bulk RNA-seq), PARP11/Parp11 is reported as the only gene that is consistently upregulated in glioma and consistently downregulated by MR3 (Fig. 2B). • Within the mouse myeloid compartment, Parp11 is most enriched in MAC4 and MAC1, while MAC1 shows high Cd274 (Pdl1/PD-L1). MR3 reduces Parp11 in MAC4/MAC1 and reduces Cd274 in MAC1 (Fig. 2H). • CellChat analysis suggests that in controls MAC1 is the dominant sender of PD-L1/PD-1 signaling to CD8+ T cells (Fig. 3C), and that this PD-L1/PD-1 interaction is strongly diminished after MR3 (Fig. 3E). • The authors propose a paracrine model in which MAC4-derived PGE2 (via Ptges3) sustains Parp11 expression in MAC1 through cAMP/PKA/CREB, promoting PD-L1-mediated T-cell suppression; MR3 disrupts this circuitry (Fig. 4). Major comments 1. Strength of the conclusions Two parts of the story felt well supported by the data as shown. First, the cross-species convergence on PARP11/Parp11 is a clear and potentially useful result (Fig. 2B). Second, the myeloid subclustering plus CellChat analysis makes a coherent case that PD-L1/PD-1 signaling in this model is dominated by a specific macrophage subset (MAC1) and changes after MR3 (Fig. 2H, Fig. 3). Where I was less convinced is when the manuscript moves from "transcriptomic and modeling evidence" to causal statements such as "MIRO1-mediated axis driving immunosuppression" and "MR3 reduces tumor burden by reactivating immunity." At the moment, several central inferences remain indirect: • Causality is inferred primarily from transcriptomic shifts and ligand-receptor inference rather than functional immune readouts.

-We thank the Reviewer for the constructive evaluation. We have toned down the claims throughout the manuscript with tracking.

• __ On-target attribution to MIRO1 hinges on MR3 being a MIRO1 binder; the study does not include a genetic MIRO1 perturbation or a target-engagement/epistasis test in the relevant immune compartments (and the authors acknowledge this limitation in the Discussion).__ -We have examined on-target activity of MR3 in our other papers. For example, by depleting Miro1 with CRISPRi in glioma cells (Miro1 KD cells), we found that it phenocopied the effect of MR3. We also expressed Miro1-7A, a drug-resistant mutant of Miro1 predicted to be unable to bind MR3 (1) in Miro1 KD glioma cells, which rendered glioma cells insensitive to MR3 treatment. These data demonstrate that in cellular glioma models, Miro1 is the target of MR3 and MR3 exerts its functions via directly binding to Miro1.

We have also excluded off-target effect of MR3 by examining other mitochondrial GTPases (1, 2) including Miro2.

We agree these data were not done specifically in immune compartments, and have acknowledged it in Discussion and added more explanation in Introduction citing our published papers.

• __ The very large reduction in "tumor cell proportion" (Fig. 1E) is striking but is still a composition measure of recovered nuclei; it is not, on its own, a direct measurement of tumor size/burden and could be sensitive to differential nuclei recovery or cell loss during processing.__ -We agree that the "tumor cell proportion" in Fig. 1E represents the composition of recovered nuclei and is not, by itself, a direct measurement of tumor size or burden. We have removed "tumor burden" throughout the manuscript to avoid confusion.

To determine whether the observed reduction might reflect technical bias, we examined the quality control metrics across all samples. Of the six initial samples (three control and three treated), one treated sample (TN1) showed clear quality concerns and was therefore excluded from downstream analysis.

For the remaining samples, the distributions of detected genes per nucleus and total RNA counts per nucleus were similar between groups. The percentage of mitochondrial reads was consistently low, and only a small fraction of nuclei was removed during filtering, indicating overall comparable nuclei quality. Notably, the treated samples yielded similar or even higher total numbers of recovered nuclei, despite showing a lower tumor cell proportion. Please refer to new Fig. S1A for these results.

Together, these observations suggest that the decrease in tumor cell proportion is unlikely to be explained simply by differential nuclei recovery, sequencing depth, or filtering effects. That said, we recognize that compositional differences in single-nucleus RNA sequencing data do not provide a direct measurement of tumor burden. We have revised the manuscript to clarify this point and to indicate that independent future approaches would be required for definitive assessment.

I think the paper can go forward in its current scope, but the strength of the claims should match the level of evidence. If the authors want to keep strong, causal language in the title/abstract ("driving immunosuppression," "reduces tumor burden"), then I consider one or two targeted validation experiments essential (see below). Alternatively, the authors can temper the language and position the mechanistic model more explicitly as a hypothesis generated from the transcriptomic analysis.

-We thank the Reviewer! We have toned down the claims throughout the manuscript to make the data consistent with the conclusion.

__ Statements that should be labeled as preliminary/speculative (unless additional validation is added) • MAC4-derived PGE2 as the upstream driver of MAC1 Parp11/PD-L1: plausible and nicely consistent with Ptges3 being MAC4-high in controls and reduced with MR3 (Fig. 4A), but not demonstrated.__

-We have changed the conclusion of this part to:

Together, these bioinformatic findings suggest that MAC4 may produce PGE₂, which could act on nearby MAC1 cells in a paracrine manner to increase Parp11 expression, although this model needs to be functionally validated.

• __ MIRO1 _→ mtDNA _→ cGAS/STING _→_ Ptges3 as a mechanistic chain: interesting, but currently framed largely by pathway knowledge plus modest expression changes (Supplementary Fig. S5).__ -We have added: "which requires future functional investigation."

• __ "MR3 reactivates anti-tumor immunity to reduce tumor burden": the gene set enrichment and CellChat shifts are consistent with immune activation, but immune-mediated tumor control is not directly tested.__ -We have toned down these claims on tumor burden and only conclude as: MR3 may enhance anti-tumor immune responses.

__ Replication and statistics Mouse snRNA-seq replication is limited after QC (3 control vs 2 MR3-treated animals). With n=2 treated, it is hard to know whether some of the biggest composition and cluster-level changes are robust to animal-to-animal variability.__

-As also explained to Rev 2, we originally planned 3 mice per group. Despite losing one after QC, sample-level pseudobulk PCA analysis (treating each mouse as one replicate) of the mice shows clear separation of treated from untreated groups (new Fig. S2C), supporting technical reproducibility despite a small n. The two MR3-treated samples clustered together and were clearly separated from controls, indicating that the transcriptional effect of MR3 exceeds inter-animal variability (new Fig. S2C). The reduction in tumor cell proportion was also observed in both treated animals (new Fig. S2F). We have added this description to the Results (Page 5, lines 116-118) and included a new figure showing the tumor cell proportion for each animal (new Fig. S2F).

We acknowledge this is a limitation, but as the Reviewer also pointed out that our paper's significance is to transcriptomically link Miro1 to well-known immune suppression factors in glioma TME and integrate 3 glioma databases which will facilitate researchers in the field to advance their own research. Thus, our methods and resource should be still valid and useful to the community.

Relatedly, the snRNA-seq differential expression is performed with Seurat FindMarkers (Wilcoxon rank-sum). Per-cell testing can inflate significance if biological replicate structure is not accounted for (pseudoreplication). I suggest the authors clarify exactly how they handled sample-level replication for the key DE results and, where possible, re-run the main DE comparisons using a sample-aware approach (e.g., pseudo-bulk within cell types/subclusters).

-We thank the reviewer for raising this important point. In the original analysis, differential expression was performed using Seurat's FindMarkers function which performs per-cell testing. We acknowledge that this approach can overestimate significance if biological replicate structure is not explicitly accounted for.

To address this, we re-ran the key differential expression analyses using a pseudo-bulk approach: counts were aggregated per cell type/subcluster per sample, and DE testing was performed across samples rather than individual cells. The main results and conclusions remain consistent with the original analysis, while this approach ensures that statistical significance properly reflects biological replication (new FigS3. D-F).

For the human bulk RNA-seq, the methods indicate 3 patient tissues split across MR3 vs DMSO for 24 h. In DESeq2, a paired design (including patient as a blocking factor) would be important to avoid patient-to-patient variability dominating the treatment signal; the manuscript should confirm whether the design formula accounted for this.

-In the revised manuscript, we re-ran the DESeq2 analysis using a paired design with patient as a blocking factor and compared DMSO and MR3 within each patient (P1-P3). The results are consistent with our previous analysis. PARP11 remains significantly downregulated (raw p-value Finally, several places in the Methods define significance using p-value cutoffs (e.g., GEPIA3 TCGA/GTEx analysis uses p 1; human DE uses p = 1). Because multiple testing is substantial in all of these analyses, I recommend reporting FDR-adjusted values consistently (and being explicit about whether figures/tables show raw or adjusted p-values).

-We have now used FDR-adjusted values for the TCGA/GTEx analysis and have updated Fig. 1C (top left), Results, and Methods accordingly. PARP11 remains significant after FDR correction.

For the human bulk RNA-seq, very few genes pass an adjusted p 2FC| > 1 across all four differential expression analyses and updated the corresponding description in Methods.

__ Do the data support the macrophage-to-CD8 suppression claim? The CellChat PD-L1/PD-1 network figures are suggestive (Fig. 3C/E), but ligand-receptor inference is not the same as demonstrating functional T-cell inhibition. At minimum, I would like to see one orthogonal readout (flow or immunostaining) showing that PD-L1__ protein on myeloid cells and PD-1 on CD8 T cells change in the expected directions after MR3, and that CD8 T cells show an activation/effector signature at the protein level.

-We agree this would be clearly the next step in functional studies, but the current manuscript is focused on transcriptomic analysis and method building, so we have toned down any claims at the functional level.

In addition, we have observed that T cells after MR3 treatment show upregulation of cytotoxicity- and IFN-response-related genes consistent with enhanced effector function at the transcriptional level. We have added new Fig. S6A and explanation in Result.

__ PARP11: mediator vs marker The cross-species PARP11 result is the most convincing and potentially generalizable finding in the manuscript (Fig. 2B). However, in the specific context of this study, PARP11 is still best supported as a conserved MR3-responsive candidate rather than a demonstrated causal driver of PD-L1-mediated suppression. If the authors want to argue PARP11 is an effector of the pathway (rather than a marker), they should either soften the language or add a minimal functional linkage experiment within the existing scope (see "Optional" experiments below).__

-We have softened the overall language throughout the manuscript to emphasize the correlation and PARP11 as a marker and to reflect the bioinformatic nature of the study. As this paper's main goal is method development and resource building, with already 11 figures, we think functional experiments could be done in another paper.

__ Reproducibility and clarity of methods I appreciate that the authors provide a code/data portal (MiroScape) and a GitHub link. To make the study as reproducible as possible, I recommend: • Deposit raw sequencing reads for both mouse and human datasets (GEO/SRA) and include accession numbers in the manuscript.__

-We have just deposited all raw data. Accession numbers will be provided once it is public.

• __ Provide a short, consolidated "computational reproducibility" note with software versions and key parameters (Seurat, CellChat, STAR, DESeq2, etc.).__ -Added

• __ Clarify pseudo-bulk construction (what is aggregated, at what level, and how many biological replicates contribute to each pseudo-bulk comparison).__ -Added

• __ Add a brief summary of MR3 provenance/validation and what "MIRO1-binding" means operationally in the context of these experiments (especially for readers outside the MIRO1 field).__ -We have added this in Introduction.

Experiments requested (kept within the existing claims) I am intentionally not suggesting new lines of experimentation. The experiments below are aimed only at supporting the paper's current central claims. I separate them into items I consider essential vs optional, depending on how strongly the authors want to phrase mechanistic conclusions.

-We thank the Reviewer. We have toned down the claims to reflect the bioinformatic nature of the paper. We will perform suggested experiments below in another paper.

Essential if the title/abstract continue to use strong causal language • Protein-level validation of the PD-L1/PD-1 axis and CD8 activation in the GL261 model. A focused flow cytometry panel (myeloid PD-L1; CD8 PD-1 plus one or two effector markers such as GZMB/IFNG/Ki67) or multiplex IF/IHC on tumor sections would substantially strengthen the central MAC1 ____→____ CD8 claim. • An orthogonal measure of tumor burden in the same treatment paradigm. The manuscript currently treats the drop in the fraction of nuclei annotated as tumor (Fig. 1E) as a reduction in tumor burden; I recommend including IVIS longitudinal data and/or histologic tumor area/volume at harvest to support this statement. • If feasible, modestly increase in vivo biological replication (the snRNA-seq analysis currently has n=2 treated after QC). Even adding one additional treated animal that passes QC would help. Feasibility (rough guidance only; core pricing varies widely by institution): a repeat GL261 cohort to harvest tumors for flow and/or histology typically takes ~3-6 weeks end-to-end. A small flow panel plus core time is often on the order of a few thousand USD (antibodies and cytometry), while basic histology/IF quantification might be in the hundreds to low-thousands. If the authors already have stored tissue from the existing cohort, some of this could be faster/cheaper. Optional (only if the authors want the MAC4 ____→____ PGE2 ____→____ Parp11 mechanism to be more than a model) • Measure PGE2 (ELISA or targeted lipidomics) in tumor lysates/conditioned media from control vs MR3-treated samples, or provide a closer proxy for PGE2 pathway engagement in the relevant clusters. Optional (only if the authors want to argue PARP11 is an effector) • A minimal functional linkage experiment (in vitro) testing whether PARP11 perturbation phenocopies the relevant aspect of MR3 in macrophages (e.g., PD-L1 levels and/or the ability to suppress CD8 activation in a co-culture). This could be done with a PARP11 inhibitor or knockdown. I do not think in vivo genetics are required for this manuscript, but some functional tie would prevent overinterpretation.

__ Minor comments A. Analysis/experimental clarifications that seem straightforward • Human DESeq2: please clarify whether the DESeq2 design was paired by patient (i.e., patient as a blocking factor).__

-See above. We re-ran the human differential expression analysis using a paired design with patient as a blocking factor and explained in Methods.

• __ snRNA-seq DE: please clarify whether any sample-aware method was used for the key DE conclusions (especially Parp11/Cd274 changes) rather than per-cell statistics alone.__ -See above. The key DE results are based on sample-level pseudobulk (each mouse as one replicate). The two MR3-treated samples cluster together in pseudobulk PCA (new Fig. S2C), and the tumor reduction is seen in both animals (new Fig. S2F), supporting robustness to animal variability.

• __ CellChat: because min.cells filtering is used (min.cells = 20), please note this explicitly in figure legends where subclusters appear only in one condition, so readers understand why certain labels are missing.__ -We have edited the Fig 3 legend accordingly.

__ Figure and text consistency issues I noticed several figure/legend/citation issues that look like simple fixes: • Fig. 3 legend panel labeling: the legend text refers to the PD-L1/PD-1 chord plot as (C) MR3− and (D) MR3+, but (D) is the heatmap panel; the chord plots are (C) and (E). This should likely read (C) MR3− and (E) MR3+.__

-Yes, and corrected.

• __ Fig. 5 panel reference: the Results text refers to the Cross Species module as Fig. 5F, but the Fig. 5 legend defines panels (A-E) and labels (E) as "Cross Species module." Please reconcile (either change the text to Fig. 5E or add a panel F).__ -Changed to "E".

• __ Discussion figure citation: the Discussion cites Ptges3/PGE2 evidence as "(Figure 3)," but Ptges3 is shown in Fig. 4A and the model is in Fig. 4B.__ -Added "Figure 4A-B" there.

• __ Fig. 1D numbers: the Results text states 509/1,602 (mouse) and 15/106 (human) "rescued" genes (Fig. 1D), but the Fig. 1D pie charts are labeled with different totals (mouse total 3490; human total 104). Please reconcile the denominators and ensure the figure matches the text and analysis choice (bulk vs snRNA vs filtered gene sets).__ -For the cross-species analysis, we only counted genes with human-mouse orthologs so that the two datasets were compared in the same gene space. This avoids inflation from species-specific genes. We have added a clarification in the figure legend.

• __ Fig. 2 legend: there is a stray quote in "lymphoid subclusters" (appears as subclusters").__ -removed.

__ Presentation and framing • Tone down or carefully qualify statements equating snRNA-seq composition shifts with reduced tumor burden (or add an orthogonal tumor-burden measurement as suggested above).__

-We have removed "tumor burden" throughout the manuscript.

• __ Where possible, tie mechanistic language explicitly to the level of evidence ("consistent with," "suggests," "model proposes") so readers do not over-interpret the transcriptomic inference.__ -done.

• __ Consider adding a small schematic in the Results or a short "interpretation" sentence in the figure legends explaining what the CellChat plots do and do not show, since non-specialists can misread these as direct interaction measurements.__ -We have added explanations in Fig 3 legends for CellChat and emphasized the transcriptomic nature of the data.

__ Prior literature The PARP11 immunotherapy literature is cited appropriately. For the PGE2 angle, it may help readers if the authors add one or two glioma-focused references on PGE2-mediated myeloid/T-cell suppression (if not already in the full reference list).__

-We have added two more papers showing PGE2 may induce MDSCs and immunosuppresion in glioma (3) (4).

Significance

Nature and significance of the advance The advance here is primarily conceptual and resource-oriented. Conceptually, the work connects a mitochondrial regulator (MIRO1) to a specific, testable immunosuppressive circuit in the glioma TME. Technically, the cross-species perturbation framework and the accompanying MiroScape portal should be useful to groups looking for conserved, drug-responsive immune programs.

Context within the existing literature Immunosuppression in glioma and the importance of tumor-associated myeloid populations are well established, as is the limited success of checkpoint blockade in GBM. The manuscript's proposed MAC4/MAC1 paracrine model and its emphasis on PD-L1/PD-1 signaling adds a focused, hypothesis-generating view of how particular macrophage states might sustain CD8 dysfunction. The identification of PARP11 as a conserved MR3-responsive gene also fits with emerging work implicating PARP11 in immunoregulatory programs and response to immunotherapy.

Audience • Neuro-oncology and glioma TME researchers (myeloid heterogeneity, immune suppression). • Tumor immunology groups interested in myeloid-driven checkpoint resistance. • Researchers working on mitochondrial stress signaling and immunometabolism. • Computational biologists building cross-species or multi-modal integration frameworks. Reviewer expertise and limitations Keywords: glioma microenvironment; macrophage/microglia biology; tumor immunology; single-cell/nucleus transcriptomics; computational ligand-receptor inference. Limitations: I am not a medicinal chemist, so I cannot deeply evaluate MR3 chemistry, PK/PD, or specificity beyond what is presented. I also did not evaluate the full web-portal implementation beyond the manuscript description.

Reviewer #2

Evidence, reproducibility and clarity

The authors study responses to MIRO1 inhibition in a mouse model of GL261 GBM and in human tissue pieces treated ex vivo. They provide an interesting link between mitochondrial function and potential therapeutic outcomes in a tumor type that is typically challenging to treat. The manuscript is written clearly, in correct English language and figures are well structured and easy to interpret. -We thank the Reviewer for the positive comments. We want to clarify that the compound binds to Miro1 and doesn't inhibit Miro1's GTPase activity (1). We have now added explanation in Introduction.

__ Major critique: 1. However, I need to stress that study is based of few experiments with low robustness. The predominant experiment is single-nuclei RNAseq analysis of GL261 tumors implanted into mice, constituting 3 CTRL and 2 treated mice, due to removal of 3rd animal following sequencing (low recovery of high quality nuclei). Therefore, the sample group is small. This is understandable for snRNA-seq experiment (although 3 animals in treated group is somewhat necessary), but the efficiency of treatment with MR3 should be better documented in a larger cohort of animals. Crucial changes in distribution of cell types or polarisation of myeloid cells should be confirmed with flow cytometry, which is more feasible on a larger cohort.__

-We agree. As explained to Rev 3, the current paper is focused on conceptual and methodical advances and providing a resource to the community, which is already big with 11 figures. As Rev 1 mentioned, our paper's significance is to transcriptomically link Miro1 to well-known immune suppression factors in glioma TME and integrate 3 glioma databases which will facilitate researchers in the field to advance their own research. Importantly, PCA analysis of the mice at the animal level showed clear separation of treated from untreated groups and the reduction in tumor cell proportion was also observed in both treated animals (new Fig. S2C, F), supporting technical reproducibility despite a small n. Thus, our methods and resource should be still valid and useful to the community. Exploring the tumor-reducing efficacy of MR3 or combined treatments (e.g. with anti-PD-L1 or PARP11 inhibitor) in larger cohorts is an exciting next step.

__ Human model does not seem robust (also, only 3 patients). Very few genes are affected by treatment (incomparably less than in mice), which poses a question if the model is sufficient to study the effect of the treatment. This should be at least discussed and arguments should be stated why such model is suitable.__

-We agree and the observed variability in treatment response is actually expected and consistent with the well-established molecular and phenotypic heterogeneity of human glioma. Importantly, despite this diversity, we identified one gene (PARP11) consistently altered across all patient's samples and mouse model. This cross-species reproducibility supports the biological and translational relevance of the finding of PARP11. We have now added this to Discussion.

In addition, we reanalyzed the human bulk RNA-seq using a paired design with patient as a blocking factor as suggested by another reviewer, which increased the number of DE genes (new Fig. 1C).

__ Fig. S1E shows that actually few genes are commonly affected between human and mouse experiments. So conclusion about "conserved" modulation by MR3 seem an overstatement.__

-We meant "Parp11" is conserved. We have deleted "conserved" throughout the manuscript when we didn't refer specifically Parp11 to avoid confusion.

__ Mechanistic conclusions about PARP11, PGE, PD-L1 etc are not documented by any wet lab experiments, just by bioinformatic modelling.__ -We have scrutinized the Main Text to emphasize this.

Minor: 1. Authors should discuss choice of GL261 model. It is immunogenic and does not resemble human GBM ideally, so the choice should be explained.

-Although GL261 model demonstrates higher immunogenicity compared to human GBM, this feature enables evaluation of immune-modulating therapies and mechanisms in an immune-competent setting. This model still preserves critical aspects of glioma biology, including immunosuppressive TME, invasive behavior, and intracranial growth (5). Thus, this model provides a suitable platform for our study of mechanistic investigation of immune cells in the TME. We have now added this to Method.

__ In clustering of mouse snRNAseq data, T cells seem underclustered, e.g. Treg cluster clearly constitutes half of Il2ra-positive and negative cells, the latter probably being conventional CD4+ T cells (usually CD4+ T cells in GL261 are 50:50 Treg and conventional). This can affect further conclusions on cell:cell interactions.__

-We thank the reviewer for this important observation. We agree that in the former annotation, it was improper to annotate all the CD4+ T cells as Treg cells, given the limited expression of Foxp3, Il2ra and other Treg marker genes. Consequently, the previously annotated "Treg cluster" likely includes both regulatory-like and conventional CD4+ T cells.

We have further clustered the CD4+ T cell population and found that if we divided CD4+ T cells into conventional CD4+ T and Treg cells, it yielded few Treg cells for downstream analysis (~50). This would compromise the robustness and reliability of our following analysis (CellChat/DEA/etc).

To address this, we have revised our annotation and now refer to this population more conservatively as "regulatory-like CD4+ T cells" rather than bona fide Tregs. Importantly, this subset still exhibits elevated expression of immunoregulatory molecules and is associated with CD8+ T cell dysfunction, preserving the main conclusions regarding immune suppression within the tumor microenvironment. We have updated the Results, Figures, and Discussion accordingly to clarify this revised annotation and its implications for cell-cell interactions.

Please refer to following new figures for the updated annotation and associated results:

Fig. 2G-H, Fig. 3A-G, Fig. S4C-D,G, Fig. S5-B-G, Fig. S6A.

Significance

The study provides an interesting conclusion and potentially relevant discovery. However, in opinion of this reviewer, the performed experiments do not strengthen this sufficiently, especially in terms of mechanical insights and weak data on human samples. In the line of general literature on new treatments of GBM and testing thereof in mouse model, this study lacks mechanistic insights and solid data on therapeutic efficiency.

-As mentioned above, the goal of this paper is to provide novel methods to integrate datasets, resource building, and identify markers in the glioma TME. It will serve as useful resources to the community and form the foundation for future therapeutic validation in larger cohorts. We have acknowledged the limitations in the revised manuscript.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): ____

The authors of "Cross-Species Transcriptomic Integration Reveals a Conserved, MIRO1-Mediated Macrophage-to-T-Cell Signaling Axis Driving Immunosuppression in Glioma" present transcriptomic, both bulk RNA Seq and single nucleus RNA Seq, from GL261 murine gliomas treated with the Miro1 targeting compound MR3. RNA Seq data from human tumor explants treated with MR3 is also presented. The authors compared DEGs from their treated tissues with publicly available RNA Seq data sets comparing DEGs from normal tissue and Glioma tumors. The goal being to identify genes modulated by MR3 that may be underlying glioma growth, TME changes, and immunosuppression. There is a significant amount of data presented, with in-depth analysis conducted on the sequencing data sets. The manuscript is lacking in mechanistic depth and this reviewer feels that the results are over-interpreted, especially without any additional conformational assays run to confirm the interpretation of the sequencing data. There were many bold statements made (lines 109-110, 117, 130-131, 142-144, 163-165) that I felt did not have enough evidence to back up their claims. __

-We have toned down these places mentioned above:

Line 109-110: Deleted now

Line 117: Deleted now

Line 130-131: Deleted now

Line 142-144: Deleted: "highly differentially expressed", the rest of the sentence is supported by our data.

Line 163-165: Deleted now

As explained later, our paper is focused on bioinformatic analysis and resource and method building. In-depth functional studies will be performed in another paper.

__A significant concern is the lack of conformation that MR3 is targeting Miro1 in these models. __

-We have done this in another manuscript where we show that in cellular glioma models, Miro1 is the target of MR3 and MR3 exerts its functions via directly binding to Miro1.

__Previous publications from the authors have shown evidence that MR3 reduces Miro1 expression in cell and fly models. Sometimes this requires the co application of FCCP or antimycin A. Thus, the results attributed within cannot be attributed to Miro1 changes but rather any on or off-target effect of MR3. __

-We originally discovered MR3 by ligand-based in silico modeling and thermal shift direct binding assay (1, 2). Thus, MR3 is a Miro1 binder (stated in Abstract and Introduction too, now we have added more background in Introduction). Indeed, sometimes we saw MR3 reduced Miro1 protein levels under certain conditions, for example, in vivo in flies after days of feeding (1, 2), or in PD cells upon Antimycin A or CCCP treatment (1, 2, 6, 7). MR3 mostly likely exerts its function via altering Miro1 protein-protein interactions (8) and Miro1 protein is subsequently degraded in proteasomes following complex dissociation or after posttranslational modifications (1, 2) (8). We have stated this hypothesis in Result section (page 10, possible model).

In our other papers we have excluded off-target effect of MR3 by examining other mitochondrial GTPases (1, 2) including Miro2, and by showing Miro1 KD glioma cells phenocopied the effects of MR3 and drug-resistant Miro1 mutant in glioma cells rendered insensitivity to MR3. These data show Miro1 is the main target of MR3.

We have added more explanations to the Introduction.

__Understanding that mouse studies are expensive and time-consuming, and the acquisition of human tissue is not trivial, the sample sets are still small. Further confirmation of findings in cell models, organoids etc. would strengthen the findings and justify the smaller sample size of mice and human tissue. __

-We agree and we have another in-depth study. However, the current paper is focused on conceptual and methodical advances and providing a resource to the community, which is already big with 11 figures. As Rev 1 mentioned, our paper's significance is to transcriptomically link Miro1 to well-known immune suppression factors in glioma TME and integrate 3 glioma databases which will facilitate researchers in the field to advance their own research. Thoroughly understanding Miro1's role in glioma TME is our next goal as stated in Discussion and is beyond the scope of the current study.

__The website MiroScape will be a very useful tool in the proper hands. ____

1. Confirm activity of MR3 on Miro1 in relevant samples. Direct downregulation? Modulation of other targets known to be altered by MR3? __

-As mentioned above, we have shown in tumor cells, MR3 disrupts pathogenic Miro1-protein interactions without the need to reduce Miro1 protein. There is currently no other target known to be altered by MR3, not even Miro2, demonstrated before (1, 2). We have added more explanations in Main Text.

__ Conduct further mechanistic work to validate claims inferred by differentially expressed genes.__

-As mentioned above, our current paper is focused on bioinformatic methods and resource building. Further mechanistic work will be performed in another paper.

__ Significantly temper claims related cell targeting, direct communication between cells and overarching responses inferred from Sequencing data. -Done. See above and Main Text.

Reviewer #3 (Significance (Required)):

My laboratories expertise lies in signaling related to mitochondrial structure and function. We have investigated the Miro1 protein and effects on cellular responses related to Miro1 expression. We have tested the MR3 compound in our own systems with limited success. Therefore my major concerns lie in validating the on-target activity of the compound in their models. __-As explained above, in our other papers we have thoroughly examined on-target activity of MR3 by courter-screening other Miro1 related/similar proteins (1, 2, 6, 7) and by using Miro1 KD cells. We have now added more explanations in Main Text.

__ With additional mechanistic validation this could be a very significant study. Using advanced model systems as the authors do allows for a comprehensive understanding of tissue responses. This is far advanced from simple single cell line culture studies but also adds significant complexity to the interpretation of the data. I am a strong believer that Sequecing data must be validated with functional assays.__

-We agree and are actively conducting those studies. However, bioinformatic analysis and method and resource building are sometimes too comprehensive to combine with functional data which may take years to obtain. We think our paper's method, markers identified in TME, and resources will be very useful to the community.

References

1. Hsieh CH, Li L, Vanhauwaert R, Nguyen KT, Davis MD, Bu G, Wszolek ZK, Wang X. Miro1 Marks Parkinson's Disease Subset and Miro1 Reducer Rescues Neuron Loss in Parkinson's Models. Cell metabolism. 2019;30(6):1131-40 e7. Epub 2019/10/01. doi: 10.1016/j.cmet.2019.08.023. PubMed PMID: 31564441; PMCID: PMC6893131.
2. Li L, Conradson DM, Bharat V, Kim MJ, Hsieh CH, Minhas PS, Papakyrikos AM, Durairaj AS, Ludlam A, Andreasson KI, Partridge L, Cianfrocco MA, Wang X. A mitochondrial membrane-bridging machinery mediates signal transduction of intramitochondrial oxidation. Nat Metab. 2021. Epub 2021/09/11. doi: 10.1038/s42255-021-00443-2. PubMed PMID: 34504353.
3. Mi Y, Guo N, Luan J, Cheng J, Hu Z, Jiang P, Jin W, Gao X. The Emerging Role of Myeloid-Derived Suppressor Cells in the Glioma Immune Suppressive Microenvironment. Front Immunol. 2020;11:737. Epub 2020/05/12. doi: 10.3389/fimmu.2020.00737. PubMed PMID: 32391020; PMCID: PMC7193311.
4. Dean PT, Hooks SB. Pleiotropic effects of the COX-2/PGE2 axis in the glioblastoma tumor microenvironment. Front Oncol. 2022;12:1116014. Epub 20230126. doi: 10.3389/fonc.2022.1116014. PubMed PMID: 36776369; PMCID: PMC9909545.
5. Mathios D, Kim JE, Mangraviti A, Phallen J, Park CK, Jackson CM, Garzon-Muvdi T, Kim E, Theodros D, Polanczyk M, Martin AM, Suk I, Ye X, Tyler B, Bettegowda C, Brem H, Pardoll DM, Lim M. Anti-PD-1 antitumor immunity is enhanced by local and abrogated by systemic chemotherapy in GBM. Science translational medicine. 2016;8(370):370ra180. Epub 2016/12/23. doi: 10.1126/scitranslmed.aag2942. PubMed PMID: 28003545; PMCID: PMC5724383.
6. Bharat V, Durairaj AS, Vanhauwaert R, Li L, Muir CM, Chandra S, Kwak CS, Le Guen Y, Nandakishore P, Hsieh CH, Rensi SE, Altman RB, Greicius MD, Feng L, Wang X. A mitochondrial inside-out iron-calcium signal reveals drug targets for Parkinson's disease. Cell Rep. 2023;42(12):113544. Epub 2023/12/07. doi: 10.1016/j.celrep.2023.113544. PubMed PMID: 38060381.
7. Bharat V, Hsieh CH, Wang X. Mitochondrial Defects in Fibroblasts of Pathogenic MAPT Patients. Front Cell Dev Biol. 2021;9:765408. Epub 2021/11/23. doi: 10.3389/fcell.2021.765408. PubMed PMID: 34805172; PMCID: PMC8595217.
8. Kwak CS, Du Z, Creery JS, Wilkerson EM, Major MB, Elias JE, Wang X. Optogenetic Proximity Labeling Maps Spatially Resolved Mitochondrial Surface Proteomes and a Locally Regulated Ribosome Pool. bioRxiv. 2025. Epub 2026/01/07. doi: 10.64898/2025.12.21.693523. PubMed PMID: 41497653; PMCID: PMC12767525.

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Referee #3

Evidence, reproducibility and clarity

The authors of "Cross-Species Transcriptomic Integration Reveals a Conserved, MIRO1-Mediated Macrophage-to-T-Cell Signaling Axis Driving Immunosuppression in Glioma" present transcriptomic, both bulk RNA Seq and single nucleus RNA Seq, from GL261 murine gliomas treated with the Miro1 targeting compound MR3. RNA Seq data from human tumor explants treated with MR3 is also presented. The authors compared DEGs from their treated tissues with publicly available RNA Seq data sets comparing DEGs from normal tissue and Glioma tumors. The goal being to identify genes modulated by MR3 that may be underlying glioma growth, TME changes, and immunosuppression. There is a significant amount of data presented, with in-depth analysis conducted on the sequencing data sets. The manuscript is lacking in mechanistic depth and this reviewer feels that the results are over-interpreted, especially without any additional conformational assays run to confirm the interpretation of the sequencing data. There were many bold statements made (lines 109-110, 117, 130-131, 142-144, 163-165) that I felt did not have enough evidence to back up their claims. A significant concern is the lack of conformation that MR3 is targeting Miro1 in these models. Previous publications from the authors have shown evidence that MR3 reduces Miro1 expression in cell and fly models. Sometimes this requires the co application of FCCP or antimycin A. Thus, the results attributed within cannot be attributed to Miro1 changes but rather any on or off-target effect of MR3. Understanding that mouse studies are expensive and time-consuming, and the acquisition of human tissue is not trivial, the sample sets are still small. Further confirmation of findings in cell models, organoids etc. would strengthen the findings and justify the smaller sample size of mice and human tissue. The website MiroScape will be a very useful tool in the proper hands.

1. Confirm activity of MR3 on Miro1 in relevant samples. Direct downregulation? Modulation of other targets known to be altered by MR3?
2. Conduct further mechanistic work to validate claims inferred by differentially expressed genes.
3. Significantly temper claims related cell targeting, direct communication between cells and overarching responses inferred from Sequencing data.

Significance

My laboratories expertise lies in signaling related to mitochondrial structure and function. We have investigated the Miro1 protein and effects on cellular responses related to Miro1 expression. We have tested the MR3 compound in our own systems with limited success. Therefore my major concerns lie in validating the on-target activity of the compound in their models.

With additional mechanistic validation this could be a very significant study. Using advanced model systems as the authors do allows for a comprehensive understanding of tissue responses. This is far advanced from simple single cell line culture studies but also adds significant complexity to the interpretation of the data. I am a strong believer that Sequecing data must be validated with functional assays.

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Referee #2

Evidence, reproducibility and clarity

The authors study responses to MIRO1 inhibition in a mouse model of GL261 GBM and in human tissue pieces treated ex vivo. They provide an interesting link between mitochondrial function and potential therapeutic outcomes in a tumor type that is typically challenging to treat. The manuscript is written clearly, in correct English language and figures are well structured and easy to interpret.

Major critique:

1. However, I need to stress that study is based of few experiments with low robustness. The predominant experiment is single-nuclei RNAseq analysis of GL261 tumors implanted into mice, constituting 3 CTRL and 2 treated mice, due to removal of 3rd animal following sequencing (low recovery of high quality nuclei). Therefore, the sample group is small. This is understandable for snRNA-seq experiment (although 3 animals in treated group is somewhat necessary), but the efficiency of treatment with MR3 should be better documented in a larger cohort of animals. Crucial changes in distribution of cell types or polarisation of myeloid cells should be confirmed with flow cytometry, which is more feasible on a larger cohort.
2. Human model does not seem robust (also, only 3 patients). Very few genes are affected by treatment (incomparably less than in mice), which poses a question if the model is sufficient to study the effect of the treatment. This should be at least discussed and arguments should be stated why such model is suitable.
3. Fig. S1E shows that actually few genes are commonly affected between human and mouse experiments. So conclusion about "conserved" modulation by MR3 seem an overstatement.
4. Mechanistic conclusions about PARP11, PGE, PD-L1 etc are not documented by any wet lab experiments, just by bioinformatic modelling.

Minor:

1. Authors should discuss choice of GL261 model. It is immunogenic and does not resemble human GBM ideally, so the choice should be explained.
2. In clustering of mouse snRNAseq data, T cells seem underclustered, e.g. Treg cluster clearly constitutes half of Il2ra-positive and negative cells, the latter probably being conventional CD4+ T cells (usually CD4+ T cells in GL261 are 50:50 Treg and conventional). This can affect further conclusions on cell:cell interactions.

Significance

The study provides an interesting conclusion and potentially relevant discovery. However, in opinion of this reviewer, the performed experiments do not strengthen this sufficiently, especially in terms of mechanical insights and weak data on human samples. In the line of general literature on new treatments of GBM and testing thereof in mouse model, this study lacks mechanistic insights and solid data on therapeutic efficiency.

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Referee #1

Evidence, reproducibility and clarity

Summary of findings and key conclusions

This manuscript asks how pharmacologic targeting of the outer mitochondrial membrane protein MIRO1 (RHOT1) with a MIRO1-binding compound (MR3) reshapes immunosuppressive programs in the glioma tumor microenvironment (TME). The core of the paper is a cross-species transcriptomic comparison that combines an in vivo mouse dataset with an ex vivo human perturbation dataset.

Model systems and approach (as described):

• Mouse in vivo: GL261-Luc intracranial glioma in C57BL/6J mice; MR3 is administered intracranially at the implantation site (10 µM in 5 µL DMSO) on days 11 and 18, and tumors are harvested on day 22 for single-nucleus RNA-seq (snRNA-seq).
• Mouse snRNA-seq: NeuN-based nuclei sorting, 10x Genomics v3.1; alignment to mm10; Seurat-based integration and annotation. Tumor-cell calling is supported by CNV inference (SCEVAN/CopyKAT). One MR3-treated sample is excluded after QC, leaving 3 control vs 2 MR3-treated samples (11,940 NeuN− nuclei).
• Human ex vivo: freshly resected glioma cores from 3 patients are cultured with 10 µM MR3 or DMSO for 24 h, followed by bulk RNA-seq (STAR alignment to hg19; DESeq2 for differential expression).
• Cross-species integration: the analysis is restricted to 1:1 orthologs and protein-coding genes shared across datasets; inferred cell-cell signaling is explored with CellChat.

Main findings (as presented):

• MR3 shifts expression of a subset of glioma-associated genes toward a non-tumor-like direction ("rescued genes") and is associated with large changes in inferred cell-type composition in the mouse snRNA-seq dataset (including a marked drop in the fraction of nuclei annotated as tumor: 44.5% to 4.3%; Fig. 1E).
• Across TCGA-vs-GTEx (glioma-upregulated genes) and three MR3 response analyses (mouse snRNA-seq, mouse pseudo-bulk, and human bulk RNA-seq), PARP11/Parp11 is reported as the only gene that is consistently upregulated in glioma and consistently downregulated by MR3 (Fig. 2B).
• Within the mouse myeloid compartment, Parp11 is most enriched in MAC4 and MAC1, while MAC1 shows high Cd274 (Pdl1/PD-L1). MR3 reduces Parp11 in MAC4/MAC1 and reduces Cd274 in MAC1 (Fig. 2H).
• CellChat analysis suggests that in controls MAC1 is the dominant sender of PD-L1/PD-1 signaling to CD8+ T cells (Fig. 3C), and that this PD-L1/PD-1 interaction is strongly diminished after MR3 (Fig. 3E).
• The authors propose a paracrine model in which MAC4-derived PGE2 (via Ptges3) sustains Parp11 expression in MAC1 through cAMP/PKA/CREB, promoting PD-L1-mediated T-cell suppression; MR3 disrupts this circuitry (Fig. 4).

Major comments

1. Strength of the conclusions Two parts of the story felt well supported by the data as shown. First, the cross-species convergence on PARP11/Parp11 is a clear and potentially useful result (Fig. 2B). Second, the myeloid subclustering plus CellChat analysis makes a coherent case that PD-L1/PD-1 signaling in this model is dominated by a specific macrophage subset (MAC1) and changes after MR3 (Fig. 2H, Fig. 3). Where I was less convinced is when the manuscript moves from "transcriptomic and modeling evidence" to causal statements such as "MIRO1-mediated axis driving immunosuppression" and "MR3 reduces tumor burden by reactivating immunity." At the moment, several central inferences remain indirect:
   • Causality is inferred primarily from transcriptomic shifts and ligand-receptor inference rather than functional immune readouts.
   • On-target attribution to MIRO1 hinges on MR3 being a MIRO1 binder; the study does not include a genetic MIRO1 perturbation or a target-engagement/epistasis test in the relevant immune compartments (and the authors acknowledge this limitation in the Discussion).
   • The very large reduction in "tumor cell proportion" (Fig. 1E) is striking but is still a composition measure of recovered nuclei; it is not, on its own, a direct measurement of tumor size/burden and could be sensitive to differential nuclei recovery or cell loss during processing. I think the paper can go forward in its current scope, but the strength of the claims should match the level of evidence. If the authors want to keep strong, causal language in the title/abstract ("driving immunosuppression," "reduces tumor burden"), then I consider one or two targeted validation experiments essential (see below). Alternatively, the authors can temper the language and position the mechanistic model more explicitly as a hypothesis generated from the transcriptomic analysis.
2. Statements that should be labeled as preliminary/speculative (unless additional validation is added)
   • MAC4-derived PGE2 as the upstream driver of MAC1 Parp11/PD-L1: plausible and nicely consistent with Ptges3 being MAC4-high in controls and reduced with MR3 (Fig. 4A), but not demonstrated.
   • MIRO1 → mtDNA → cGAS/STING → Ptges3 as a mechanistic chain: interesting, but currently framed largely by pathway knowledge plus modest expression changes (Supplementary Fig. S5).
   • "MR3 reactivates anti-tumor immunity to reduce tumor burden": the gene set enrichment and CellChat shifts are consistent with immune activation, but immune-mediated tumor control is not directly tested.
3. Replication and statistics Mouse snRNA-seq replication is limited after QC (3 control vs 2 MR3-treated animals). With n=2 treated, it is hard to know whether some of the biggest composition and cluster-level changes are robust to animal-to-animal variability. Relatedly, the snRNA-seq differential expression is performed with Seurat FindMarkers (Wilcoxon rank-sum). Per-cell testing can inflate significance if biological replicate structure is not accounted for (pseudoreplication). I suggest the authors clarify exactly how they handled sample-level replication for the key DE results and, where possible, re-run the main DE comparisons using a sample-aware approach (e.g., pseudo-bulk within cell types/subclusters). For the human bulk RNA-seq, the methods indicate 3 patient tissues split across MR3 vs DMSO for 24 h. In DESeq2, a paired design (including patient as a blocking factor) would be important to avoid patient-to-patient variability dominating the treatment signal; the manuscript should confirm whether the design formula accounted for this. Finally, several places in the Methods define significance using p-value cutoffs (e.g., GEPIA3 TCGA/GTEx analysis uses p < 0.05 and |log2FC| > 1; human DE uses p < 0.05 and log2FC >= 1). Because multiple testing is substantial in all of these analyses, I recommend reporting FDR-adjusted values consistently (and being explicit about whether figures/tables show raw or adjusted p-values).
4. Do the data support the macrophage-to-CD8 suppression claim? The CellChat PD-L1/PD-1 network figures are suggestive (Fig. 3C/E), but ligand-receptor inference is not the same as demonstrating functional T-cell inhibition. At minimum, I would like to see one orthogonal readout (flow or immunostaining) showing that PD-L1 protein on myeloid cells and PD-1 on CD8 T cells change in the expected directions after MR3, and that CD8 T cells show an activation/effector signature at the protein level.
5. PARP11: mediator vs marker The cross-species PARP11 result is the most convincing and potentially generalizable finding in the manuscript (Fig. 2B). However, in the specific context of this study, PARP11 is still best supported as a conserved MR3-responsive candidate rather than a demonstrated causal driver of PD-L1-mediated suppression. If the authors want to argue PARP11 is an effector of the pathway (rather than a marker), they should either soften the language or add a minimal functional linkage experiment within the existing scope (see "Optional" experiments below).
6. Reproducibility and clarity of methods I appreciate that the authors provide a code/data portal (MiroScape) and a GitHub link. To make the study as reproducible as possible, I recommend:
   • Deposit raw sequencing reads for both mouse and human datasets (GEO/SRA) and include accession numbers in the manuscript.
   • Provide a short, consolidated "computational reproducibility" note with software versions and key parameters (Seurat, CellChat, STAR, DESeq2, etc.).
   • Clarify pseudo-bulk construction (what is aggregated, at what level, and how many biological replicates contribute to each pseudo-bulk comparison).
   • Add a brief summary of MR3 provenance/validation and what "MIRO1-binding" means operationally in the context of these experiments (especially for readers outside the MIRO1 field). Experiments requested (kept within the existing claims) I am intentionally not suggesting new lines of experimentation. The experiments below are aimed only at supporting the paper's current central claims. I separate them into items I consider essential vs optional, depending on how strongly the authors want to phrase mechanistic conclusions. Essential if the title/abstract continue to use strong causal language
   • Protein-level validation of the PD-L1/PD-1 axis and CD8 activation in the GL261 model. A focused flow cytometry panel (myeloid PD-L1; CD8 PD-1 plus one or two effector markers such as GZMB/IFNG/Ki67) or multiplex IF/IHC on tumor sections would substantially strengthen the central MAC1 → CD8 claim.
   • An orthogonal measure of tumor burden in the same treatment paradigm. The manuscript currently treats the drop in the fraction of nuclei annotated as tumor (Fig. 1E) as a reduction in tumor burden; I recommend including IVIS longitudinal data and/or histologic tumor area/volume at harvest to support this statement.
   • If feasible, modestly increase in vivo biological replication (the snRNA-seq analysis currently has n=2 treated after QC). Even adding one additional treated animal that passes QC would help. Feasibility (rough guidance only; core pricing varies widely by institution): a repeat GL261 cohort to harvest tumors for flow and/or histology typically takes ~3-6 weeks end-to-end. A small flow panel plus core time is often on the order of a few thousand USD (antibodies and cytometry), while basic histology/IF quantification might be in the hundreds to low-thousands. If the authors already have stored tissue from the existing cohort, some of this could be faster/cheaper. Optional (only if the authors want the MAC4 → PGE2 → Parp11 mechanism to be more than a model)
   • Measure PGE2 (ELISA or targeted lipidomics) in tumor lysates/conditioned media from control vs MR3-treated samples, or provide a closer proxy for PGE2 pathway engagement in the relevant clusters. Optional (only if the authors want to argue PARP11 is an effector)
   • A minimal functional linkage experiment (in vitro) testing whether PARP11 perturbation phenocopies the relevant aspect of MR3 in macrophages (e.g., PD-L1 levels and/or the ability to suppress CD8 activation in a co-culture). This could be done with a PARP11 inhibitor or knockdown. I do not think in vivo genetics are required for this manuscript, but some functional tie would prevent overinterpretation.

Minor comments

A. Analysis/experimental clarifications that seem straightforward

• Human DESeq2: please clarify whether the DESeq2 design was paired by patient (i.e., patient as a blocking factor).
• snRNA-seq DE: please clarify whether any sample-aware method was used for the key DE conclusions (especially Parp11/Cd274 changes) rather than per-cell statistics alone.
• CellChat: because min.cells filtering is used (min.cells = 20), please note this explicitly in figure legends where subclusters appear only in one condition, so readers understand why certain labels are missing.

B. Figure and text consistency issues

I noticed several figure/legend/citation issues that look like simple fixes: - Fig. 3 legend panel labeling: the legend text refers to the PD-L1/PD-1 chord plot as (C) MR3− and (D) MR3+, but (D) is the heatmap panel; the chord plots are (C) and (E). This should likely read (C) MR3− and (E) MR3+. - Fig. 5 panel reference: the Results text refers to the Cross Species module as Fig. 5F, but the Fig. 5 legend defines panels (A-E) and labels (E) as "Cross Species module." Please reconcile (either change the text to Fig. 5E or add a panel F). - Discussion figure citation: the Discussion cites Ptges3/PGE2 evidence as "(Figure 3)," but Ptges3 is shown in Fig. 4A and the model is in Fig. 4B. - Fig. 1D numbers: the Results text states 509/1,602 (mouse) and 15/106 (human) "rescued" genes (Fig. 1D), but the Fig. 1D pie charts are labeled with different totals (mouse total 3490; human total 104). Please reconcile the denominators and ensure the figure matches the text and analysis choice (bulk vs snRNA vs filtered gene sets). - Fig. 2 legend: there is a stray quote in "lymphoid subclusters" (appears as subclusters").

C. Presentation and framing

• Tone down or carefully qualify statements equating snRNA-seq composition shifts with reduced tumor burden (or add an orthogonal tumor-burden measurement as suggested above).
• Where possible, tie mechanistic language explicitly to the level of evidence ("consistent with," "suggests," "model proposes") so readers do not over-interpret the transcriptomic inference.
• Consider adding a small schematic in the Results or a short "interpretation" sentence in the figure legends explaining what the CellChat plots do and do not show, since non-specialists can misread these as direct interaction measurements.

D. Prior literature The PARP11 immunotherapy literature is cited appropriately. For the PGE2 angle, it may help readers if the authors add one or two glioma-focused references on PGE2-mediated myeloid/T-cell suppression (if not already in the full reference list).

Significance

Nature and significance of the advance

The advance here is primarily conceptual and resource-oriented. Conceptually, the work connects a mitochondrial regulator (MIRO1) to a specific, testable immunosuppressive circuit in the glioma TME. Technically, the cross-species perturbation framework and the accompanying MiroScape portal should be useful to groups looking for conserved, drug-responsive immune programs.

Context within the existing literature

Immunosuppression in glioma and the importance of tumor-associated myeloid populations are well established, as is the limited success of checkpoint blockade in GBM. The manuscript's proposed MAC4/MAC1 paracrine model and its emphasis on PD-L1/PD-1 signaling adds a focused, hypothesis-generating view of how particular macrophage states might sustain CD8 dysfunction. The identification of PARP11 as a conserved MR3-responsive gene also fits with emerging work implicating PARP11 in immunoregulatory programs and response to immunotherapy.

Audience

• Neuro-oncology and glioma TME researchers (myeloid heterogeneity, immune suppression).
• Tumor immunology groups interested in myeloid-driven checkpoint resistance.
• Researchers working on mitochondrial stress signaling and immunometabolism.
• Computational biologists building cross-species or multi-modal integration frameworks.

Reviewer expertise and limitations

Keywords: glioma microenvironment; macrophage/microglia biology; tumor immunology; single-cell/nucleus transcriptomics; computational ligand-receptor inference. Limitations: I am not a medicinal chemist, so I cannot deeply evaluate MR3 chemistry, PK/PD, or specificity beyond what is presented. I also did not evaluate the full web-portal implementation beyond the manuscript description.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity (Required)

Ali et al investigate the composition of putative kinetochore subcomplexes in the unicellular eukaryote Tetrahymena thermophila. Up to the point of this study, only a CENP-A ortholog and two subunits of the microtubule-binding Ndc80 complex had been clearly identified. This left open the question, whether Tetrahmena kinetochores follow the conventional organization found in common model systems such as yeast or human cells, or contain many unconventional proteins. The authors combine proximity biotinylation coupled to mass spectrometry with deep homology searches and structure predictions.

Extensive bioinformatic analysis of the T. thermophila genome allows the authors to annotate 16 genes as kinetochore genes (KiTT). Using sequence comparisons with known kinetochore proteins, they were able to relate their novel KiTT proteins to the conserved kinetochore components Cenp A, Cenp C, the KMN network, as well as auxiliary proteins. In particular, the authors were able to complete the organization of the Ndc80 complex and identify subunits of the Mtw1/Mis12 complex and a Knl1 ortholog. This characterizes a KMN network as the centerpiece of the Tetrahymena kinetochore architecture.

The CCAN seems to be represented solely by CENP-C, with key binding interfaces to KMN and CENP-A being preserved. An interesting aspect is that neither a Dam1-, nor a Ska homolog seems to support the Ndc80 complex. Instead, the authors identify a Kinesin-6 homolog that may potentially compensate for the absence of these factors.

The study is well-designed, the results are thoughtfully discussed and the expertly conducted experiments highlight the power of combining experimental identification (BioID) with bioinformatic analyses.

We appreciate the favorable assessment of our manuscript and would like to extend our thanks for the reviewers’ constructive criticisms and insightful comments. Where possible we aim to incorporate them (see below).

Major comments The functional validation of the newly identified subunits using RNAi feels somewhat limited in this study. I understand there a technical limitations in this system, but whenever possible, I would at least expect the authors to explore differential effects on different parts of the kinetochore using the reagents they have at hand. In the particular, the authors show the effects of depleting KiTT12 (the kinesin-6 homolog) on Ndc80 kinetochore localization. It would be important to check effects also on CENP-A (using the anti-CNA1 antibody), or on other subunits. Given the available reagents, this should be readily possible.

We agree that examining the effect of KiTT12 depletion on inner kinetochore components will strengthen the functional interpretation. While we do not expect, based on KiTT12’s relative location, a direct impact of KiTT12 RNAi on CNA1 (CENP-A) or CENP-C, we will perform immunofluorescence analyses using anti-CNA1 and anti-CENP-C antibodies in KiTT12 RNAi cells (and KiTT2 (NUF2) RNAi as control). These experiments will allow us to determine whether KiTT12 depletion specifically affects outer kinetochore integrity (as suggested by Ndc80 mislocalization) or more broadly perturbs kinetochore architecture (CNA1/CENP-C). We will include quantitative analyses of signal intensity and kinetochore organization to clarify potential hierarchical dependencies.

The organization of the Knl1 ortholog and the question of whether a mitotic checkpoint is present, deserves some additional discussion. Interestingly, the positional organization of a PP1 binding motif at the N-terminus of a long disordered domain seems conserved. On the other hand, MELT motifs appear to be absent. The authors should discuss the implications of this some more. Is there an Mps1 homolog? What about the error correction machinery including Aurora B and the CPC? The putative MadBub homolog does not seem to localize to kinetochores, but maybe this is not detectable, unless the respective conditions (unattached kinetochores) are generated. Is it known, how the system reacts to spindle depolymerization?

Tetrahymena does not appear to have a spindle checkpoint, given prior reports that chromosome segregation is not halted by microtubule depolymerization [Kaczanowski et al. 1985]. In line with this, the SAC protein orthologs that are present lack the motifs to mount a sufficient response and halt the cell cycle. We thus agree that the architecture of the Tetrahymena KNL1 ortholog and possible other SAC-related proteins raises important evolutionary questions. We will expand the discussion to address:

• The absence of canonical MELT motifs in the Tetrahymena KNL1 ortholog.
• The absence of a detectable Mps1 ortholog in our homology searches.
• The divergence of the Tetrahymena MadBub protein and its lack of conserved KEN–ABBA–KEN motifs typically required for APC/C inhibition.

• The absence of Mad2 and Mad2-binding motif in Cdc20. Relevant REFS:

• Kaczanowski et al. 1985, Experimental Cell Research

• Loidl et al. 2009, Molecular Biology of the Cell

• Kops et al. 2020, Current Biology

Minor comments - Introduction: When introducing the Tetrahymena kinetochore, please add some sentences on microtubule/spindle organization in the MIC. What is known about the kinetochore-microtubule attachment site in Tetrahymena?

We will expand the introduction to include a concise description of spindle organization in the micronucleus (MIC), including known features of centromere clustering, spindle assembly, and microtubule attachment sites during MIC mitosis.

Relevant REFs:

• Davidson et al. 1975, Biosystems

• Lafountain Jr et al. 1979, Chromosoma

• Lafountain Jr et al. 1980, Cell Motility

• Line 128: putative homology to Spc24 (E=13), comment on why this was considered, what cutoffs were applied etc..

We will clarify the homology detection criteria, including E-value thresholds, domain architecture considerations, reciprocal searches, and structure-based validation. We will explain why this candidate was retained despite weak sequence similarity and how structural prediction strengthened confidence. In (very) short, we used the ‘top hit’ principle. E=13 for spc24 was simply the first hit and upon AlphaFold-predicted structures, the protein was clearly similar to spc24.

• Line 135: briefly mention and discuss conservation of the RWD folds in the Spc24-25 orthologs.

We will expand this section to explicitly describe conservation of the RWD fold and how structural modeling supports ortholog assignment despite sequence divergence. The E-values mentioned in line 128 for instance are for the RWD domain-only, not the full-length protein, we will further indicate this in the text.

• Line 194: Maybe replace "show" with "suggest", given there is no experimental data behind the CENP-C identification

We agree and will revise wording to “suggest” to avoid overstatement. However, we do want to point out that CENP-C/KiTT8 was identified experimentally as well through the BioID pipeline, and also an antibody was raised against KiTT8 that places this protein at the inner kinetochore.

• Figure 7B: please add the information for the RNAi target directly to the Figure

We will add the requested information directly to the figure.

• Figures in the combined pdf: please add the respective Figure number or Supplementary Figure number directly on the Figure.

We will add the figure numbers to the supplementary figure files.

Significance (Required)

While functional studies are often conducted in very few model organisms, exploring the evolutionary variations of kinetochore architecture can help to understand the design principles of kinetochores. I also helps to assign functions to specific subcomplexes and can reveal how adaptations of a core machinery occurs. Tetrahymena is historically an important experimental system that has had a great impact on the understanding of multiple aspects of nuclear biology. Deciphering the organization of the chromosome segregation machinery in this organism is therefore of great interest to researchers interested in mitosis and genome stability.

Reviewer #2

Evidence, reproducibility and clarity (Required)

Summary Ali, Raas et al. provide a comprehensive molecular characterization of the kinetochore in the ciliate Tetrahymena thermophila. By integrating proximity proteomics (TurboID) with structure-based "deep" homology detection, they identify 16 kinetochore proteins (KiTT1-16), including nine highly diverged "cryptic" orthologs of conserved LECA components and four lineage-specific proteins. Their results demonstrate that while the Tetrahymena kinetochore lacks a conventional CCAN complex, it maintains a recognizable outer kinetochore structure supplemented by novel proteins essential for faithful chromosome segregation.

Major comments 1. Representation of known kinetochore diversity - Since this manuscript wants to highlight that it is important to characterize kinetochore components in different eukaryotic clades, it would be good to highlight the known diversity from the literature in Figure 1, e.g. indicating species/clades for which components have been experimentally validated vs. only computationally inferred. - It would be good to specifically highlight this on the figure for the clade closest to Tetrahymena in which KT components have been experimentally validated (Apicomplexa?). - L58-64: the sentences 'we have a limited understanding about kinetochore composition and function from other branches of the eukaryotic tree of life' and 'these surveys also uncovered a surprisingly extensive diversity of kinetochore composition across eukaryotes' seem to contradict each other. Instead of/in addition to the literature described in the introduction, as suggested above, having known diversity indicated on a figure would therefore be helpful. This could be done quite roughly, just mentioning the number of verified KT components and the number of species for which this was done.

We will add a more elaborate version of Figure 1a (or include an extended version to the supplement), summarizing the requested information in the above three points. Indeed, our mention of diversity in lineages is an inferred one, not a directly tested one. We will amend the text to clarify this.

• L46-L56: when explaining the structure of the KT, it would be good to already refer to a figure, like the diagram of a human KT in 1B. As it is now, the introduction first explains the general structure, and then goes into diversity. This is fine, but it would be easier to understand if the figure panels followed this order.

We will include additional references to figure 1b at the appropriate places in the introduction.

The data can sometimes be represented in a more straightforward manner: - L120-...: After reading through the whole text, I understand why the authors choose to talk about Spc24 and Spc25 first (since Spc25 is also used in the TurboID experiment). However, the presented pipeline for these two proteins is much less convincing than for the other proteins. Spc24/25: 'Some homology > slight structure similarity > right localization in immunostaining' vs. the pipeline for the other proteins: 'TurboID > confirmation using homology + immunostaining' (what is depicted in Fig. 2C). The latter is very convincing, but by starting off with the less convincing pipeline, the reader starts off on the wrong track. Since Spc24 is not used in the end for the first TurboID results, is Spc25 necessary at this point or can this come later?

We used this ‘story line’ because it was the way it happened. It felt wrong to us to pretend we hadn’t already found Spc24 and Spc25 by bioinformatic means before doing the TurboID, which might also have caused concerns with some readers as to our ability to detect orthologs for these and other proteins. Of note: a re-analysis of the Spc24-BioID experiment revealed that it was previously wrongfully considered unusable, hence we now include it in our NDC80-C based TurboID discovery pipeline in Figure 2. We will where possible revise the narrative structure to more clearly explain the logic of the discovery pipeline, while maintaining transparency about the historical order in which candidates were identified. We will streamline the Spc24/25 section and more prominently introduce the TurboID-driven identification pipeline (Figure 2C) to guide the reader.

• It is very good and thorough that the authors noticed that some of the KT proteins were simply missed because they were not part of the original predicted proteome. However, why weren't the TurboID analyses simply redone with the new proteome? The authors could still note that it was important to use the most recent version, but it would be much more straightforward for readers to immediately have the most up to date analysis.

We thank the reviewer for pointing this out. We agree that remapping to the most recent proteome annotation will improve clarity. We will remap the TurboID datasets to the updated Tetrahymena proteome, which includes Nnf1 and Csm1, and report whether additional components are identified. Of note: in a preliminary analysis with the newest version of the proteome we do not find any new proteins in the NDC80-C-TurboID experiments. We will also clarify in the manuscript what “not in original proteome” refers to and revise Figure 2C accordingly.

Figure 4 and accompanying paragraph: this is an interesting analysis, but impossible to interpret without comparing with the branch length of other Tetrahymena proteins or Tetrahymena as a species (if I interpreted the analysis correctly). L251: 'this underscores the high rates of evolution of kinetochore proteins'. This could be true, but this isn't proven here because there is no comparison with the evolutionary rate of other proteins in Tetrahymena.

The reviewer is correct in arguing that without comparisons to other proteins, the statement that kinetochores proteins in Tetrahymena evolved at high rates is incorrect, or at least not supported by the present data. What we meant was to say that they evolved at high/increased rates compared to kinetochore proteins of other species. This in our view explains why we have missed them in past searches, regardless of whether this is specific to the kinetochore in Tetrahymena or to Tetrahymena proteins in general. We will amend the text to reflect this more clearly. We will explicitly acknowledge analytical limitations and remove claims regarding lineage-specific acceleration.

Figure 5: For further validation and to better show the layered structure of the Tetrahymena kinetochore it would be nice to have a couple of images here with increased resolution by using expansion microscopy.

We agree that improved spatial resolution would strengthen the layered organization model. We will attempt to perform expansion microscopy (ExM) on selected tagged kinetochore components and incorporate representative images into the revised manuscript (main or supplementary figures).

Minor comments - Abstract: if you are going to call out individual components, maybe also point out the few that were already known (KiTT1-2 and 14). Otherwise the reader might be confused about the missing numbers.

We will revise this in the abstract.

• L37: is 'cryptic ortholog' an official term? Doesn't this just depend on the starting point of the homology search and the number of experimentally verified hits you have in certain parts of the tree? Just wondering.

This is a valid question. Indeed, ‘cryptic’ refers to the starting point of our study (based on our previous analyses) and the process towards identifying them as being canonical. We chose this term because we feel it signifies to the reader that identifying these orthologs required approaches beyond conventional orthology searches.

• For future submissions, it would be useful to have the figure numbers indicated on the figures, because now it was sometimes difficult to keep track.

As mentioned above, we will add the figure numbers to the revision.

• L51: mentioning the SAC might make it a bit too complicated for people not 100% familiar with all the complexes. Either leave it out until later, or have a short sentence explaining what the SAC is.

We will leave out the spindle assembly checkpoint (SAC) in the beginning and will bring it up at a later point, also explaining its explicit function.

• Figure 1A: the identity of the black 'nuclei' is not explained for the Ciliophora and Apicomplexa in the figure or figure legend.

We apologise for the confusing black organelles in apicomplexans, these are actually the micronemes and apical complex, characteristic features of these parasites. We will change the color to that of the clade so that it is clear that only ciliates have two types of nuclei (nuclear dimorphism).

• In Figure 1B, instead of saying 'absent', wouldn't it be more correct to say something like 'not found/detected/identified'?

We agree and will replace ‘absent’ by ‘not detected’.

• Figure 1C. During interphase, sometimes homologous chromosomes seem to cluster at the centromeres (5 foci - example on the left), but sometimes they don't (10 foci - example on the right). Is this something you observe a lot? Is it strain-dependent?

We thank the reviewer for making a very good point. In principle we take the cells showing 5 foci to be interphase cells. We interpret the cells with 10 foci to be cells just prior to mitosis. So these would be G2 cells where the homologous chromosomes have been replicated and the sister pairs are still seen together here. However, if this would be the case one would expect to see 20 centromeres/kinetochores in metaphase and this is not always observed. To prevent confusion on this point, we will replace the right panel in 1C for one that contains 5 foci and will make it more clear that these foci indeed represent homologous chromosomes. In addition, we will make panels to clearly show the behaviour of chromosomes over the different stages of mitosis.

• Figure 1C (and later in Fig. 5): centromeres don't seem to align during metaphase. Is this true, or are these examples showing late metaphase/early anaphase?

Indeed, a true metaphase similar to classic textbook images does not seem to be present. In 3D reconstructions we do see that kinetochores sit close to the nuclear envelope forming a sphere on the outside of the spindle, but almost never exactly in the same plane. Whether this means we simply have not caught true metaphase state, or there is none (like for instance in apicomplexans, which also do not appear to have a spindle checkpoint), is unclear at this point. We will further review our images and will use consistent stages for these images, and will revise terminology on metaphase state if warranted.

• Why was STU2 included in the kinetochore? Wouldn't it be better classified as a MAP as in Fig. 3A? I saw this is actually discussed in the discussion, but maybe this explanation should come earlier.

We thank the reviewer for pointing this out and will add a short sentence about the MAP function of STU2, and kinetochore localization in other lineages in the introduction.

• Figure 2A: 'strong similarity'. For a TM score of 0.4 and 0.54, I am not sure I would say 'strong similarity'. Visually, they also look different. TM is also not explained in the legend.

What we meant to say with ‘strong similarity’ is that a domain is predicted with a matching set of secondary structure elements to the RWD domains in yeast Spc24/Spc25. As for the TM score, a score of ≥ 0.5 has been shown to be a robust metric for fold similarity significance , which is the case for the comparison of the putative T. thermophila Spc25 ortholog and the yeast ortholog. However, we acknowledge that the T. thermophila Spc24 ortholog shows additional beta sheets compared to its yeast counterpart and has a TM score below 0.5, and so we will tone down this statement and remove ‘strong similarity’. We nonetheless maintain that this protein is a Spc24 ortholog with derived properties in its RWD domain.

Relevant reference on TM score interpretation:

Xu & Yang 2010 Bioinformatics (https://pmc.ncbi.nlm.nih.gov/articles/PMC2913670/)

• Fig. 2D: why not PC2? Please explain this somewhere.

We thank the reviewer for this question. We shall add an elaborate explanation of the PC selection in the method section. In short, PC2 (together with PC1 or PC3) did not reveal any separate cluster/cloud of points surrounding the NDC80-C components (KiTT1-4). Since PC3 did reveal such a cluster, we opted to select PC3.

• Fig. 3C-D: 'striking similarity', again, it is hard to evaluate whether this is true from the figures and TM values alone (all are >0.5). Either change the phrasing, or explain how much similarity one would expect between homologs.

Please see our response to the previous question regarding the significance of a TM score of ≥ 0.5.

• How certain are you that these are all diverged homologs? For example, for KNL1, could another RWD domain-containing protein have evolved to become a kinetochore protein?

In most cases we consider multiple lines of evidence: AF2/3, HHsearch and overall protein topology, in the case of RWD KT proteins, a coiled-coil followed by a single or double RWD. In the case of SPC24, SPC25 and CSM1 we have clear best hits for both structure and sequence searches. For KNL1 (double RWD), we have a newer version of our eukaryote-wide ortholog alignment now usable for HHsearches, which reveals KiTT7 (KNL1) to be the best hit also. As such, the RWD domain proteins that we uncover are not merely some RWD, but are specifically those of the kinetochore that are found in other lineages. In addition, there are only very few double RWD proteins present amongst eukaryotes, which makes the proposed scenario of homolog replacement for KNL1 unlikely.

• Fig. 5: why wasn't CNA1 used as a marker of the inner kinetochore or tested?

The CNA1 antibody gave quite some background (see figure 1C), we therefore favored the use of the CENPC/KiTT8 antibody.

• Fig. 8: There is a time axis below, but I'm not sure what is indicated on this axis. Are the events above mapped on this axis?

We agree this axis may be confusing. The idea was to show a number of ancestral nodes relevant for the evolutionary events noted in this figure. We will add clear references in the figure to each of these ancestors.

• L347-349: 'convergent evolution'. Is the loss of the CCAN convergent evolution, or was it already lost in the SAR common ancestor?

This was indeed convergent evolution. Amongst Stramenopila most CCAN subunits can be detected (see for instance van Hooff et al. 2017). In addition, the alveolate ancestor already had the CCAN as we can clearly detect orthologs in Colponemida. We will add this piece of information to the presence/absence plot in either Figure 1 or in the supplemental (see comment above to Reviewer 1).

Significance (Required)

General Assessment: The study is robust, thorough, and well-written. The analyses are technically sound, and the authors avoid overstating their conclusions. Key strengths include the successful identification of diverged components using a "deep homology" pipeline and the functional validation of novel subunits. To improve the study, the data representation could be made more straightforward, and the manuscript structure could be condensed to better highlight the most convincing results. Finally, the claims on the speed of evolution of the kinetochore components need to be better supported.

Advance: The study provides the first molecular map of a ciliate kinetochore. By uncovering "cryptic" orthologs that escaped previous detection, the work demonstrates that many "missing" complexes in diverse eukaryotes are likely present but highly diverged.

Audience: This work will interest evolutionary cell biologists studying mitosis and kinetochores (especially those interested in eukaryotic diversity), as well as the ciliate research community. It also serves as a methodological roadmap for researchers using structural homology to identify divergent proteins in other non-model organisms.

Expertise: My field of expertise includes evolutionary cell biology, kinetochores, centromeres, microbiology, microscopy and phylogenetics.

Reviewer #3

Evidence, reproducibility and clarity (Required)

Kinetochores are protein complexes essential for chromosome segregation in all eukaryotes. Unexpectedly, despite their crucial function, many kinetochore components evolve rapidly, which can hinder their identification based solely on sequence comparisons. In this study, the authors combine experimental and computational analyses to provide insights into the composition of the kinetochore protein complex in the ciliate Tetrahymena thermophila. This study makes an important contribution because kinetochore components in Tetrahymena have not previously been investigated experimentally, and the composition of the Tetrahymena complex was largely unknown.

Starting with previously identified orthologs of the outer kinetochore proteins Ndc80 and Nuf2, the authors computationally identified the two additional members of the Ndc80 complex, Spc24 and Spc25. All four components were subjected to BioID analyses, leading to the identification of 23 additional candidates, some of which are factors known to be associated with centromeric chromatin in other eukaryotes (condensin, etc.). Focusing on a subset of unknown components, the authors provide experimental support for their kinetochore participation using microscopy and confirm distant homology with several known kinetochore components in other eukaryotes. Four components referred to as KiTT10-13, however, lack detectable orthology to known kinetochore components.

Relative localization analyses using super-resolution microscopy revealed that KiTT10, 11, and 13 are more proximal to the inner kinetochore component CENP-C, while KiTT12 localizes closer to outer kinetochore components. Remote homology and phylogenetic analyses identify divergent WD40 or SANT domains in KiTT10 and 11, as well as a kinesin motor domain for the outer-kinetochore proximal KiTT12. Finally, RNAi-mediated depletion of KiTT12 demonstrated its requirement for accurate chromosome segregation and Ndc80 localization.

Overall, I think this manuscript is interesting and makes an important contribution to the field of kinetochore biology. The results of this study, particularly regarding the novel kinetochore components identified, will likely also spark follow-up studies. My major comment concerns the discussion and presentation of the data:

Major Comments At times, the explanation of homology search appears very technical and would not be accessible to non-experts..

We thank the reviewer for raising this point. Given that the homology detection approach is an important part of the message of our manuscript, we do think that it is warranted to keep some technicalities in the results section. However, we do agree that quite some detail could be quite easily transferred to a specific supplementary section about our homology detection approach. We will rewrite the results section to better suit non-experts.

Moreover, the authors could include more details about their analysis of TurboID data to improve clarity.

I was initially confused what does "not in original proteome" mean in the figure before understanding that two different proteome versions were used. I think it would be less confusing for the reader if the authors simply map their bioID data to the most recent version of the Tetrahymena proteome, which includes both Nnf1 and Csm1. Is it possible that this might also reveal the presence of other components in addition to the two that were specifically targeted?

We agree that mapping to the most recent proteome annotation will eliminate confusion. We will remap all TurboID datasets to the updated proteome and report whether additional candidates are detected. We will revise the figure legends to clearly explain enrichment categories and annotation differences between proteome versions (or in a supplementary section). So far we have not detected any new proteins in a re-analysis of the MS data for components of the NDC80-C.

The data presentation in Figure 2 is confusing and requires clarification of the analyses performed. The Figure legend for panel 2C is incomplete. For example, there is no mapping for the character "*" in the legend. The legend can be revised for better clarity. Also, more than 23 proteins are shown in the 2D inset; were those not enriched in the other BioID experiments? It would be helpful to include a legend for these hits as well.

We will revise Figure 2 and its legend to:

• Clearly define all symbols (including “*”).
• Provide a complete legend for enriched hits.
• Clarify PCA interpretation.
• Explicitly state how many proteins are included and how they were categorized. I would be cautious about using the word comprehensive, as the identification depends on many aspects, including the completeness of the annotated proteome used to map the MassSpec spectra against. Even if their bioID experiments always converge on the same set of proteins, factors can still be missing due to annotation issues. In addition, certain components might be refractory for detection by MassSpec due to their amino acid composition. Other digestion methods, other than trypsin, could, however, identify those.

We agree that this term overstates completeness. We will revise wording to reflect that our identification is extensive but dependent on proteome annotation and mass spectrometry detectability.

Figure 4: I guess the result is somewhat expected given the previous inability to identify these components computationally. I guess the distribution of the non-tetrahymena components might be skewed towards lower sequence divergence, since they do not include orthologs that require experimental approaches for identification. If the authors agree, this could be added as a discussion.

We agree with the reviewer that Figure 4 merely showcases why we could not detect these kinetochore orthologs in the first place. In our present analysis we did not include orthologs of species with previously shown ‘difficult-to-detect’ orthologs. We will add discussion acknowledging that detectable homologs in other species may be biased toward less divergent sequences and that experimental identification may reveal additional highly diverged components elsewhere.

The telophase-specific localization of TTHERM_00932010 is interesting. Although the paper focuses on the structural composition of kinetochores, it would be useful if the authors included more details about this protein.

We will expand the description of TTHERM_00932010 to provide additional contextual information regarding domain architecture, expression timing, and potential functional implications. Off note, for this protein we cannot detect any orthologs outside Tetrahymena spp.

What is the function of kinesin-6, known roles with respect to chromosome segregation in other species?

We already discuss the role of kinesin-6 in chromosome segregation in other species in the discussion section at L355-356 (bioRxiv v1). We will expand this section and add two more sentences on diverse functions of this family in eukaryotes.

Perhaps MadBub localization is more apparent in the presence of unattached kinetochores? In that scenario, it would be useful if the authors knock down KiTT12 and test whether they can localize MadBub.

We agree this is an interesting possibility. However, systematic spindle perturbation experiments fall outside the primary scope of this structural study. We will clarify this limitation and discuss it as a direction for future work.

Minor comments It would be useful if the authors added either the expression of all genes or known constitutive genes as a background profile to Figure 2E, in order for the reader to be able to evaluate the G2/M specific increase in expression of bioID hits.

The data has been taken from [Bertagna et al. 2025, Bioinformatics], and the expression profiles of all the other proteins are provided for inspection by the reviewer/reader (see Table S3). The data representation asked for by the reviewer can thus be found in Bertagna et al. 2025. To provide further overview, we will add a supplementary figure including expression profile for protein with peaks in each of the cell cycle phases, including an overview of those peaking in G2/M.

What is TTHERM_0046753? One of the identified unknown hits? It is also not part of Figure 2E unless this is a typo and the correct identifier should be 00467535?

The reviewer is correct that this is a typo on our end, for which we apologise. The correct identifier should be 00467535.

Why are 29 expressions shown in 2E but only 27 mentioned in the text (23 bioID hits as well as the four Ndc80 complex components)? Or did the authors instead identify 25 specific bioID hits that were further classified into the different categories? A rewrite on this section would likely help the reader to better understand the analyses of the PCA data.

We agree this section can do with some optimization. We will clarify the number of proteins included in PCA and expression analyses and revise the relevant section for clarity.

Significance (Required)

This study highlights the importance of non-model organisms, such as ciliates, in understanding the evolution of the chromosome segregation machinery. Studies on such organisms would shed light on the evolutionary aspects of kinetochore biology.

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

Kinetochores are protein complexes essential for chromosome segregation in all eukaryotes. Unexpectedly, despite their crucial function, many kinetochore components evolve rapidly, which can hinder their identification based solely on sequence comparisons. In this study, the authors combine experimental and computational analyses to provide insights into the composition of the kinetochore protein complex in the ciliate Tetrahymena thermophila. This study makes an important contribution because kinetochore components in Tetrahymena have not previously been investigated experimentally, and the composition of the Tetrahymena complex was largely unknown. Starting with previously identified orthologs of the outer kinetochore proteins Ndc80 and Nuf2, the authors computationally identified the two additional members of the Ndc80 complex, Spc24 and Spc25. All four components were subjected to BioID analyses, leading to the identification of 23 additional candidates, some of which are factors known to be associated with centromeric chromatin in other eukaryotes (condensin, etc.). Focusing on a subset of unknown components, the authors provide experimental support for their kinetochore participation using microscopy and confirm distant homology with several known kinetochore components in other eukaryotes. Four components referred to as KiTT10-13, however, lack detectable orthology to known kinetochore components. Relative localization analyses using super-resolution microscopy revealed that KiTT10, 11, and 13 are more proximal to the inner kinetochore component CENP-C, while KiTT12 localizes closer to outer kinetochore components. Remote homology and phylogenetic analyses identify divergent WD40 or SANT domains in KiTT10 and 11, as well as a kinesin motor domain for the outer-kinetochore proximal KiTT12. Finally, RNAi-mediated depletion of KiTT12 demonstrated its requirement for accurate chromosome segregation and Ndc80 localization. Overall, I think this manuscript is interesting and makes an important contribution to the field of kinetochore biology. The results of this study, particularly regarding the novel kinetochore components identified, will likely also spark follow-up studies. My major comment concerns the discussion and presentation of the data:

Major Comments

At times, the explanation of homology search appears very technical and would not be accessible to non-experts. Moreover, the authors could include more details about their analysis of TurboID data to improve clarity. I was initially confused what does "not in original proteome" mean in the figure before understanding that two different proteome versions were used. I think it would be less confusing for the reader if the authors simply map their bioID data to the most recent version of the Tetrahymena proteome, which includes both Nnf1 and Csm1. Is it possible that this might also reveal the presence of other components in addition to the two that were specifically targeted?<br /> The data presentation in Figure 2 is confusing and requires clarification of the analyses performed. The Figure legend for panel 2C is incomplete. For example, there is no mapping for the character "*" in the legend. The legend can be revised for better clarity. Also, more than 23 proteins are shown in the 2D inset; were those not enriched in the other BioID experiments? It would be helpful to include a legend for these hits as well. I would be cautious about using the word comprehensive, as the identification depends on many aspects, including the completeness of the annotated proteome used to map the MassSpec spectra against. Even if their bioID experiments always converge on the same set of proteins, factors can still be missing due to annotation issues. In addition, certain components might be refractory for detection by MassSpec due to their amino acid composition. Other digestion methods, other than trypsin, could, however, identify those.<br /> Figure 4: I guess the result is somewhat expected given the previous inability to identify these components computationally. I guess the distribution of the non-tetrahymena components might be skewed towards lower sequence divergence, since they do not include orthologs that require experimental approaches for identification. If the authors agree, this could be added as a discussion.<br /> The telophase-specific localization of TTHERM_00932010 is interesting. Although the paper focuses on the structural composition of kinetochores, it would be useful if the authors included more details about this protein. What is the function of kinesin-6, known roles with respect to chromosome segregation in other species? Perhaps MadBub localization is more apparent in the presence of unattached kinetochores? In that scenario, it would be useful if the authors knock down KiTT12 and test whether they can localize MadBub.

Minor comments

It would be useful if the authors added either the expression of all genes or known constitutive genes as a background profile to Figure 2E, in order for the reader to be able to evaluate the G2/M specific increase in expression of bioID hits What is TTHERM_0046753? One of the identified unknown hits? It is also not part of Figure 2E unless this is a typo and the correct identifier should be 00467535? Why are 29 expressions shown in 2E but only 27 mentioned in the text (23 bioID hits as well as the four Ndc80 complex components)? Or did the authors instead identify 25 specific bioID hits that were further classified into the different categories? A rewrite on this section would likely help the reader to better understand the analyses of the PCA data.

Significance

This study highlights the importance of non-model organisms, such as ciliates, in understanding the evolution of the chromosome segregation machinery. Studies on such organisms would shed light on the evolutionary aspects of kinetochore biology.

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

Summary

Ali, Raas et al. provide a comprehensive molecular characterization of the kinetochore in the ciliate Tetrahymena thermophila. By integrating proximity proteomics (TurboID) with structure-based "deep" homology detection, they identify 16 kinetochore proteins (KiTT1-16), including nine highly diverged "cryptic" orthologs of conserved LECA components and four lineage-specific proteins. Their results demonstrate that while the Tetrahymena kinetochore lacks a conventional CCAN complex, it maintains a recognizable outer kinetochore structure supplemented by novel proteins essential for faithful chromosome segregation.

Major comments

1. Representation of known kinetochore diversity
   • Since this manuscript wants to highlight that it is important to characterize kinetochore components in different eukaryotic clades, it would be good to highlight the known diversity from the literature in Figure 1, e.g. indicating species/clades for which components have been experimentally validated vs. only computationally inferred.
   • It would be good to specifically highlight this on the figure for the clade closest to Tetrahymena in which KT components have been experimentally validated (Apicomplexa?).
   • L58-64: the sentences 'we have a limited understanding about kinetochore composition and function from other branches of the eukaryotic tree of life' and 'these surveys also uncovered a surprisingly extensive diversity of kinetochore composition across eukaryotes' seem to contradict each other. Instead of/in addition to the literature described in the introduction, as suggested above, having known diversity indicated on a figure would therefore be helpful. This could be done quite roughly, just mentioning the number of verified KT components and the number of species for which this was done.
   • L46-L56: when explaining the structure of the KT, it would be good to already refer to a figure, like the diagram of a human KT in 1B. As it is now, the introduction first explains the general structure, and then goes into diversity. This is fine, but it would be easier to understand if the figure panels followed this order.
2. The data can sometimes be represented in a more straightforward manner:
   • L120-...: After reading through the whole text, I understand why the authors choose to talk about Spc24 and Spc25 first (since Spc25 is also used in the TurboID experiment). However, the presented pipeline for these two proteins is much less convincing than for the other proteins. Spc24/25: 'Some homology > slight structure similarity > right localization in immunostaining' vs. the pipeline for the other proteins: 'TurboID > confirmation using homology + immunostaining' (what is depicted in Fig. 2C). The latter is very convincing, but by starting off with the less convincing pipeline, the reader starts off on the wrong track. Since Spc24 is not used in the end for the first TurboID results, is Spc25 necessary at this point or can this come later?
   • It is very good and thorough that the authors noticed that some of the KT proteins were simply missed because they were not part of the original predicted proteome. However, why weren't the TurboID analyses simply redone with the new proteome? The authors could still note that it was important to use the most recent version, but it would be much more straightforward for readers to immediately have the most up to date analysis.
3. Figure 4 and accompanying paragraph: this is an interesting analysis, but impossible to interpret without comparing with the branch length of other Tetrahymena proteins or Tetrahymena as a species (if I interpreted the analysis correctly). L251: 'this underscores the high rates of evolution of kinetochore proteins'. This could be true, but this isn't proven here because there is no comparison with the evolutionary rate of other proteins in Tetrahymena.
4. Figure 5: For further validation and to better show the layered structure of the Tetrahymena kinetochore it would be nice to have a couple of images here with increased resolution by using expansion microscopy.

Minor comments

• Abstract: if you are going to call out individual components, maybe also point out the few that were already known (KiTT1-2 and 14). Otherwise the reader might be confused about the missing numbers.
• L37: is 'cryptic ortholog' an official term? Doesn't this just depend on the starting point of the homology search and the number of experimentally verified hits you have in certain parts of the tree? Just wondering.
• For future submissions, it would be useful to have the figure numbers indicated on the figures, because now it was sometimes difficult to keep track.
• L51: mentioning the SAC might make it a bit too complicated for people not 100% familiar with all the complexes. Either leave it out until later, or have a short sentence explaining what the SAC is.
• Figure 1A: the identity of the black 'nuclei' is not explained for the Ciliophora and Apicomplexa in the figure or figure legend.
• In Figure 1B, instead of saying 'absent', wouldn't it be more correct to say something like 'not found/detected/identified'? Figure 1C. During interphase, sometimes homologous chromosomes seem to cluster at the centromeres (5 foci - example on the left), but sometimes they don't (10 foci - example on the right). Is this something you observe a lot? Is it strain-dependent?
• Figure 1C (and later in Fig. 5): centromeres don't seem to align during metaphase. Is this true, or are these examples showing late metaphase/early anaphase?
• Why was STU2 included in the kinetochore? Wouldn't it be better classified as a MAP as in Fig. 3A? I saw this is actually discussed in the discussion, but maybe this explanation should come earlier.
• Figure 2A: 'strong similarity'. For a TM score of 0.4 and 0.54, I am not sure I would say 'strong similarity'. Visually, they also look different. TM is also not explained in the legend.
• Fig. 2D: why not PC2? Please explain this somewhere.
• Fig. 3C-D: 'striking similarity', again, it is hard to evaluate whether this is true from the figures and TM values alone (all are >0.5). Either change the phrasing, or explain how much similarity one would expect between homologs.
• How certain are you that these are all diverged homologs? For example, for KNL1, could another RWD domain-containing protein have evolved to become a kinetochore protein?
• Fig. 5: why wasn't CNA1 used as a marker of the inner kinetochore or tested?
• Fig. 8: There is a time axis below, but I'm not sure what is indicated on this axis. Are the events above mapped on this axis?
• L347-349: 'convergent evolution'. Is the loss of the CCAN convergent evolution, or was it already lost in the SAR common ancestor?

Significance

General Assessment: The study is robust, thorough, and well-written. The analyses are technically sound, and the authors avoid overstating their conclusions. Key strengths include the successful identification of diverged components using a "deep homology" pipeline and the functional validation of novel subunits. To improve the study, the data representation could be made more straightforward, and the manuscript structure could be condensed to better highlight the most convincing results. Finally, the claims on the speed of evolution of the kinetochore components need to be better supported.

Advance: The study provides the first molecular map of a ciliate kinetochore. By uncovering "cryptic" orthologs that escaped previous detection, the work demonstrates that many "missing" complexes in diverse eukaryotes are likely present but highly diverged.

Audience: This work will interest evolutionary cell biologists studying mitosis and kinetochores (especially those interested in eukaryotic diversity), as well as the ciliate research community. It also serves as a methodological roadmap for researchers using structural homology to identify divergent proteins in other non-model organisms.

Expertise: My field of expertise includes evolutionary cell biology, kinetochores, centromeres, microbiology, microscopy and phylogenetics.

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Referee #1

Evidence, reproducibility and clarity

Ali et al investigate the composition of putative kinetochore subcomplexes in the unicellular eukaryote Tetrahymena thermophila. Up to the point of this study, only a CENP-A ortholog and two subunits of the microtubule-binding Ndc80 complex had been clearly identified. This left open the question, whether Tetrahmena kinetochores follow the conventional organization found in common model systems such as yeast or human cells, or contain many unconventional proteins. The authors combine proximity biotinylation coupled to mass spectrometry with deep homology searches and structure predictions. Extensive bioinformatic analysis of the T. thermophila genome allows the authors to annotate 16 genes as kinetochore genes (KiTT). Using sequence comparisons with known kinetochore proteins, they were able to relate their novel KiTT proteins to the conserved kinetochore components Cenp A, Cenp C, the KMN network, as well as auxiliary proteins. In particular, the authors were able to complete the organization of the Ndc80 complex and identify subunits of the Mtw1/Mis12 complex and a Knl1 ortholog. This characterizes a KMN network as the centerpiece of the Tetrahymena kinetochore architecture. The CCAN seems to be represented solely by CENP-C, with key binding interfaces to KMN and CENP-A being preserved. An interesting aspect is that neither a Dam1-, nor a Ska homolog seems to support the Ndc80 complex. Instead, the authors identify a Kinesin-6 homolog that may potentially compensate for the absence of these factors. The study is well-designed, the results are thoughtfully discussed and the expertly conducted experiments highlight the power of combining experimental identification (BioID) with bioinformatic analyses.

Major comments

The functional validation of the newly identified subunits using RNAi feels somewhat limited in this study. I understand there a technical limitations in this system, but whenever possible, I would at least expect the authors to explore differential effects on different parts of the kinetochore using the reagents they have at hand. In the particular, the authors show the effects of depleting KiTT12 (the kinesin-6 homolog) on Ndc80 kinetochore localization. It would be important to check effects also on CENP-A (using the anti-CNA1 antibody), or on other subunits. Given the available reagents, this should be readily possible. The organization of the Knl1 ortholog and the question of whether a mitotic checkpoint is present, deserves some additional discussion. Interestingly, the positional organization of a PP1 binding motif at the N-terminus of a long disordered domain seems conserved. On the other hand, MELT motifs appear to be absent. The authors should discuss the implications of this some more. Is there an Mps1 homolog? What about the error correction machinery including Aurora B and the CPC? The putative MadBub homolog does not seem to localize to kinetochores, but maybe this is not detectable, unless the respective conditions (unattached kinetochores) are generated. Is it known, how the system reacts to spindle depolymerization?

Minor comments

Introduction: When introducing the Tetrahymena kinetochore, please add some sentences on microtubule/spindle organization in the MIC. What is known about the kinetochore-microtubule attachment site in Tetrahymena?

Line 128: putative homology to Spc24 (E=13), comment on why this was considered, what cutoffs were applied etc..

Line 135: briefly mention and discuss conservation of the RWD folds in the Spc24-25 orthologs

Line 194: Maybe replace "show" with "suggest", given there is no experimental data behind the CENP-C identification

Figure 7B: please add the information for the RNAi target directly to the Figure

Figures in the combined pdf: please add the respective Figure number or Supplementary Figure number directly on the Figure.

Significance

While functional studies are often conducted in very few model organisms, exploring the evolutionary variations of kinetochore architecture can help to understand the design principles of kinetochores. I also helps to assign functions to specific subcomplexes and can reveal how adaptations of a core machinery occurs. Tetrahymena is historically an important experimental system that has had a great impact on the understanding of multiple aspects of nuclear biology. Deciphering the organization of the chromosome segregation machinery in this organism is therefore of great interest to researchers interested in mitosis and genome stability.

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Reply to the reviewers

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

The study by Hemberg et al investigated whether the critical adaptor protein MAVS is required for IFN induction and viral resistance in primary human respiratory epithelial cells infected with influenza A virus (IAV). Specifically, air-liquid interface pulmonary bronchial epithelial cells (ALI-PBECs) are engineered with CRISPR/Cas9 to knockout MAVS (or AAVS1 as a control), followed by IAV infection and subsequent monitoring of the 1) IFN/ISG response and 2) viral replication. The study is thoroughly conducted, the methodology and the results are clearly described, and the study is written in a clear and transparent manner. No overstatements are made and limitations of the study are clearly indicated. I therefore only have a few minor comments:

We would like to thank Reviewer 1 for their assessment of our manuscript. We are pleased with the overall positive comments, especially that the study was considered thoroughly conducted. However, this reviewer also raised some concerns that we will address in the point-to-point review below.

• In the Discussion the following sentence should be nuanced: "However, most studies report no observable effect of MAVS KO on antiviral protection18,20". Please indicate that this refers to the context of IAV infection. I would also clarify that in this sentence you are referring to antiviral protection rather than IFN/ISG induction. (For example: While MAVS is important for IFN/ISG induction upon IAV infection, some studies in MAVS-deficient mice showed that this did not necessarily translate to increased antiviral protection). I would also advice to stay away from 'most studies report no observable effect' when you only reference two publications.

This is a very valid point. We have addressed the comment by adjusting the sentence accordingly:

“The importance of MAVS in IAV infections has only been investigated in few studies using MAVS-deficient mice. While these studies show that MAVS is essential for the induction of IFNs and ISGs upon IAV infection, supporting the findings of the current study, these findings did not translate to increased antiviral protection in the mice18,20.” in the revised version of our manuscript (page 4, line 34-37).

• Fig. 2A and 2B (and 2C and 2D): please indicate the time points in the graphs to better reflect (visually) the difference between the panels.

We agree with this comment by the reviewer. Figure 2A-D have been adjusted to include the infectious time points.

Reviewer #1 (Significance (Required)):

While the results of the study are not surprising (reduced IFN/ISG responses and increased IAV replication in MAVS KO cells), the scientific advance in this study is largely of a methodological nature: the role of MAVS in IAV infection has not been previously studied in this advanced culture model system. The study is of relevance to researchers that are in the immediate research field (virologists, RNA sensing). The study provides a useful example of CRISRP/Cas9 engineering in a complex model system to investigate the role of a particular gene in antiviral innate responses, which could easily be extrapolated to other genes.

We are thankful, that Reviewer 1 appreciates the significance and potential of the complex model used in this study.

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

Review of manuscript RC-2025-03340:

The authors of the manuscript "MAVS is Important for Antiviral Defense Against Influenza A Virus in a Human Respiratory Epithelium Model" present their recent work evaluating innate immune responses in a human cell line. Specifically, they infect primary human respiratory epithelial cells with influenza A virus and use CRISPR-Cas9 to knockout MAVS and demonstrate the importance of this adaptor molecule on type I and type III IFN induction. Their work shows that MAVS is important for restricting viral replication and they conclude that it is a non-redundant protector of human respiratory epithelial cells. Below are comments that the authors should consider during revision of this manuscript.

We thank Reviewer 2 for their careful review of our manuscript. Reviewer 2 provided several valuable suggestions for improvements, which we will address below.

1. The authors use the IAV A/PR/8/34, which is a good, laboratory strain for initial characterization. However, since this model strives to evaluate human cell interactions the authors are encouraged to use a relevant primary human influenza virus isolate in their model. This is important as the host:pathogen interactions may differ significantly when using a human isolate.

This is an important point. We agree that stain-specific differences might affect host-pathogen interactions. Although IAV A/PR/8/34 is well-characterized and easily reproducible in mechanistic studies, it is a laboratory adapted strain. Therefore, we have now added a statement in Discussion acknowledging this limitation:

“An important consideration of this study is the use of the laboratory-adapted influenza A/PR/8/34 (H1N1) strain. While this strain was selected due to its widespread use and ability to provide a robust and reproducible infection model, it has undergone extensive laboratory adaption. Consequently, the host-pathogen interactions observed in this study might differ from those elicited by primary clinical isolates. Validation of these results using contemporary human influenza stains will be important to determine their broader applicability.” (page 5, line 22-27).

1. It was unclear why the authors used SeV for a control.

We thank the reviewer for this important comment. Sendai virus (SeV) was used as a positive control due to its well-established ability to effectively activate RIG-I-dependent antiviral signaling. SeV is widely used as a potent inducer of RIG-I-mediated innate immune responses and provide a strong and reproducible stimulus independent of influenza-specific evasion mechanisms. To clarify this rationale, we have expanded the motivation for using SeV in the manuscript as indicated below:

“To validate disruption of MAVS-dependent signaling, MAVS KO HAE-ALI cultures were infected with Sendai virus (SeV). SeV is a well characterized activator of the RIG-I pathway and is widely used as a positive control in studies of antiviral innate immunity. Infection with SeV induces a strong and reproducible activation of downstream signaling, thereby allowing validation of pathway integrity.” (page 2, line 44-46 and page 3, line 1-2).

Reviewer #2 (Significance (Required)):

Strengths of this study are the model developed and the evaluation of the MAVS component within primary human epithelial cells. Limitations include the use of a lab strain of influenza that is mouse-adapted (minimizes potential interaction with human host intracellular machinery), lack of a uniform knockout, and the inclusion of SeV without indicating the benefit of using this virus as a control. The advance in this publication is modest as it uses a non-uniform knockout model to demonstrate that an already-appreciated mechanism is involved in host:pathogen interactions. Also, without the use of a human virus isolate it is unclear if this is applicable beyond the lab setting.

We would like to thank Reviewer 2 for their time and helpful comments. We have addressed their concerns to the best of our ability. We are pleased that the reviewer recognized the strength of our model in assessing the role of MAVS in primary respiratory epithelium.

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

The manuscript "MAVS is Important for Antiviral Defense Against Influenza A Virus in a Human Respiratory Epithelium Model" by Hemberg et al. demonstrates that reduction of MAVS expression in human respiratory epithelium leads to diminished induction of the type I IFN gene IFNB1, the type III IFN gene IFNL1, and multiple interferon-stimulated genes in response to IAV infection. They further show increased viral replication at 48 hours post-infection in MAVS-reduced epithelial cultures, as evidenced by elevated viral gene (NP, M2, NS1) transcripts and viral protein (NS1) levels.

We would like to thank Reviewer 3 for their assessment of our manuscript. That reviewer raised some major and minor concerns that we will address in the point-to-point review below.

Major comments: The authors convincingly show reduced MAVS expression in their CRISPR-Cas9 KO epithelial cultures compared to AAVS1 KO controls. However, residual MAVS expression remains detectable by western blot (Fig. 1C). No data is provided regarding cell-type specificity of the gene knockdown, although immunostaining and transcript analyses confirm the presence of both ciliated and secretory cells in MAVS KO and control cultures (Fig. 1H-I). Given that IAV exhibits strain-dependent cellular tropism and replication kinetics (e.g., Roach et al., PNAS 2024; https://doi.org/10.1073/pnas.2320303121), demonstrating unbiased gene editing across cell populations would strengthen the conclusions. While technically challenging (requiring scRNA-seq or RNA-scope), acknowledging this limitation in the discussion would be sufficient.

We appreciate the reviewer’s comment regarding residual MAVS expression and the lack of cell-type–specific gene editing. We agree that while western blot analysis demonstrates substantial reduction of MAVS, low levels of MAVS expression remain detectable. As noted by the reviewer, we did not directly assess editing efficiency across individual epithelial cell subtypes. Although we confirm the presence of ciliated and secretory populations in both KO and control cultures, unbiased quantification of gene disruption at single-cell resolution was beyond the scope of the present study. We agree that such analyses would further strengthen conclusions regarding cell-type–specific effects and have now acknowledged this as a limitation in the Discussion section.

“While MAVS protein levels were markedly reduced in the MAVS KO cultures, low residual expression remained detectable by western blot. HAE-ALI cultures are heterogeneous, and electroporation may not affect all cells, making complete MAVS elimination challenging. Nonetheless, MAVS protein levels were consistently reduced in KO cultures from both donors compared to controls, allowing investigation of the role of MAVS in this respiratory epithelium model. An important limitation of this study is that, although both ciliated and secretory epithelial populations were confirmed in KO and control cultures, gene editing efficiency was not assessed at single-cell resolution. Given that influenza A virus can exhibit strain-dependent cellular tropism, editing efficiency may vary across epithelial subtypes. Future studies employing single-cell transcriptomic approaches will be valuable in determining the extent of MAVS disruption within distinct epithelial populations.” (page 5, line 6-15).

The claim that MAVS is critical for restricting viral replication is somewhat less compelling. While increased viral gene transcripts and reduced NS1 protein by western blot support this, the immunofluorescence images in Fig. 3E-F are difficult to interpret at the current magnification and resolution. Co-staining for secretory and ciliated cells would help assess tropism and epithelial integrity qualitatively. Additionally, although the data indicate increased viral replication, the most rigorous confirmatory assay would be a plaque-forming assay. Inclusion of discussion acknowledging this limitation would address concerns regarding replication kinetics without PFU measurement.

We thank the reviewer for their comment regarding the assessment of viral replication. We agree that plaque-forming assays provide the most direct quantification of infectious viral particles. In the present study, increased viral gene transcripts together with altered NS1 protein levels were used as indicators of enhanced viral burden in MAVS KO cultures. While this support increased viral replication, we acknowledge that infectious viral titers were not directly measured. We have now added a statement to the Discussion recognizing this limitation.

Regarding the immunofluorescence images, we agree that higher magnification and co-staining for epithelial subtypes would provide additional insight into cellular tropism and epithelial integrity. This has been noted as a limitation and an area for future investigation.

“Although increased viral transcripts and altered viral protein levels in MAVS KO cultures support enhanced viral burden, infectious viral titers were not directly quantified by plaque-forming assay, which remains the gold standard for measuring replication kinetics. Therefore, while our data indicate increased viral gene expression in the absence of MAVS, the extent to which this corresponds to increased production of infectious virions warrants further investigation. In addition, higher-resolution imaging with co-staining of epithelial subtypes would provide greater insight into potential strain-dependent tropism and epithelial integrity following infection.” (page 4, line 44-46 and page 5, line 1-4).

Minor comments:

Increase legibility of the scale bar in Fig. 3E.

The size of the scale bars in all images of Fig. 3E has been increased to increase readability.

Typographical corrections:

"some HAE-ALI cell that wasn't affected by the KO" → "some HAE-ALI cells weren't affected by the KO"

"ProLong Glas Antifade" → "ProLong Glass Antifade"

All minor comments were adjusted in our manuscript.

Reviewer #3 (Significance (Required)):

The core strength and novelty of this study lies in the use of CRISPR-Cas9-mediated knockdown of a gene of interest in a human epithelial system. The authors demonstrate effective gene editing across multiple donors to interrogate a specific pathway. Although the results are limited to the innate responses of the respiratory epithelium-unlike prior studies using murine models, which capture a broader range of cell types and immune responses-the paper provides valuable mechanistic insight into the role of MAVS in the respiratory epithelium, the first line of defense against viral pathogens.

We sincerely appreciate the thoughtful evaluation of our work by Reviewer 3 and their recognition of its strengths. We are particularly pleased that the reviewer highlighted the novelty of the CRISPR-Cas9–mediated gene editing approach in primary human epithelium and acknowledged the value of validating the model across multiple donors. We also appreciate their recognition that, despite the focused scope on epithelial innate responses, the study provides meaningful mechanistic insight into the role of MAVS at the respiratory barrier.

In addition to revising the manuscript in response to reviewer’s comments, we have also made minor grammatical changes, which are listed below:

1. On the → and their (page 1, line 12)
2. Molecule → protein (page 1, line 13)
3. Test → assess (page 1, line 13)
4. Has → is various experiments have (page 2, line 16)
5. However, there are discrepancies regarding the extent to which MAVS contributes to antiviral defense → However, discrepancies regarding the extent to which MAVS contributes to antiviral defense are still present. (page 2, line 18)
6. Moved this sentence from line 23 to line 21 on page 2: “Only a few studies have examined the importance of MAVS in the antiviral defense against IAV, and these studies report no consistent phenotype 9,16,18,20.”.
7. RNA virus infections → IAV infection (page 2, line 23)
8. Deleted “then” (page 2, line 40).
9. Infection with SeV induced C-X-C Motif Chemokine Ligand 10 (CXCL-10) and Interferon Stimulated Gene 15 (ISG-15), measured by ELISA and qPCR, however this induction was decreased in the MAVS KO cultures compared to the control (Fig. 1D, E) → Infection with SeV increased production of C-X-C Motif Chemokine Ligand 10 (CXCL-10) and Interferon Stimulated Gene 15 (ISG-15), measured by ELISA and qPCR. However, this induction was decreased in the MAVS KO cultures compared to the control (Fig. 1D, E), (page 3, line 2-5).
10. Deleted “generated” (page 3, line 12).
11. However → but (page 3, line 16)
12. Was → were (page 3, line 31)
13. Deleted “by qPCR” (page 3, line 32).
14. To examine this, viral RNA corresponding to the segments NP, M2, and NS1 of IAV from infected AAVS1 or MAVS KO HAE-ALI was quantified by qPCR. → To examine this, viral RNA corresponding to the Nucleoprotein (NP), Matrix protein 2 (M2), and Non-structural protein 1 (NS1) of IAV from infected AAVS1 or MAVS KO HAE-ALI was quantified by qPCR. (page 4, line 3-5)
15. Added “the” (page 4, line 25)
16. The current study only includes two same sex donors → A limitation of the current study is the inclusion of only two same-sex donors (page 5, line 16-17)
17. The HAE-ALI model only includes respiratory epithelial cells, and therefore it does not... → Another limitation is, that the HAE-ALI model only includes respiratory epithelial cells. Therefore, it does not … (page 5, line 18-19)
18. Role → importance (page 5, line 20)
19. Importance → role (page 5, line 21)
20. Deleted “the” (page 5, line 21)
21. An important strength of this study is, that it was conducted on primary human respiratory epithelium cells, making the results transferable to humans. → Despite these limitations, an important strength of this study is, that it was conducted on primary human respiratory epithelium cells, making the results applicable to humans. (page 5, line 27-28).
22. Added “Although further research, is needed, this study demonstrates that MAVS KO significantly impairs IFN and ISG induction in a human respiratory epithelial model infected with IAV. Given the physiological relevance of this system, these results support an important role for MAVS in antiviral responses in the human respiratory epithelium.” (page 5, line 34-37).
23. Figure texts: IAV (diluted 1:20 in DMEM) → IAV (MOI 0.5).

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Referee #3

Evidence, reproducibility and clarity

The manuscript "MAVS is Important for Antiviral Defense Against Influenza A Virus in a Human Respiratory Epithelium Model" by Hemberg et al. demonstrates that reduction of MAVS expression in human respiratory epithelium leads to diminished induction of the type I IFN gene IFNB1, the type III IFN gene IFNL1, and multiple interferon-stimulated genes in response to IAV infection. They further show increased viral replication at 48 hours post-infection in MAVS-reduced epithelial cultures, as evidenced by elevated viral gene (NP, M2, NS1) transcripts and viral protein (NS1) levels.

Major comments:

The authors convincingly show reduced MAVS expression in their CRISPR-Cas9 KO epithelial cultures compared to AAVS1 KO controls. However, residual MAVS expression remains detectable by western blot (Fig. 1C). No data is provided regarding cell-type specificity of the gene knockdown, although immunostaining and transcript analyses confirm the presence of both ciliated and secretory cells in MAVS KO and control cultures (Fig. 1H-I). Given that IAV exhibits strain-dependent cellular tropism and replication kinetics (e.g., Roach et al., PNAS 2024; https://doi.org/10.1073/pnas.2320303121 ), demonstrating unbiased gene editing across cell populations would strengthen the conclusions. While technically challenging (requiring scRNA-seq or RNA-scope), acknowledging this limitation in the discussion would be sufficient.

The claim that MAVS is critical for restricting viral replication is somewhat less compelling. While increased viral gene transcripts and reduced NS1 protein by western blot support this, the immunofluorescence images in Fig. 3E-F are difficult to interpret at the current magnification and resolution. Co-staining for secretory and ciliated cells would help assess tropism and epithelial integrity qualitatively. Additionally, although the data indicate increased viral replication, the most rigorous confirmatory assay would be a plaque-forming assay. Inclusion of discussion acknowledging this limitation would address concerns regarding replication kinetics without PFU measurement.

Minor comments:

Increase legibility of the scale bar in Fig. 3E.

Typographical corrections:

"some HAE-ALI cell that wasn't affected by the KO" → "some HAE-ALI cells weren't affected by the KO"

"ProLong Glas Antifade" → "ProLong Glass Antifade"

Significance

The core strength and novelty of this study lies in the use of CRISPR-Cas9-mediated knockdown of a gene of interest in a human epithelial system. The authors demonstrate effective gene editing across multiple donors to interrogate a specific pathway. Although the results are limited to the innate responses of the respiratory epithelium-unlike prior studies using murine models, which capture a broader range of cell types and immune responses-the paper provides valuable mechanistic insight into the role of MAVS in the respiratory epithelium, the first line of defense against viral pathogens.

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Referee #2

Evidence, reproducibility and clarity

The authors of the manuscript "MAVS is Important for Antiviral Defense Against Influenza A Virus in a Human Respiratory Epithelium Model" present their recent work evaluating innate immune responses in a human cell line. Specifically, they infect primary human respiratory epithelial cells with influenza A virus and use CRISPR-Cas9 to knockout MAVS and demonstrate the importance of this adaptor molecule on type I and type III IFN induction. Their work shows that MAVS is important for restricting viral replication and they conclude that it is a non-redundant protector of human respiratory epithelial cells. Below are comments that the authors should consider during revision of this manuscript.

1. The authors use the IAV A/PR/8/34, which is a good, laboratory strain for initial characterization. However, since this model strives to evaluate human cell interactions the authors are encouraged to use a relevant primary human influenza virus isolate in their model. This is important as the host:pathogen interactions may differ significantly when using a human isolate.
2. It was unclear why the authors used SeV for a control.

Significance

A. Strengths of this study are the model developed and the evaluation of the MAVS component within primary human epithelial cells. Limitations include the use of a lab strain of influenza that is mouse-adapted (minimizes potential interaction with human host intracellular machinery), lack of a uniform knockout, and the inclusion of SeV without indicating the benefit of using this virus as a control.

B. The advance in this publication is modest as it uses a non-uniform knockout model to demonstrate that an already-appreciated mechanism is involved in host:pathogen interactions. Also, without the use of a human virus isolate it is unclear if this is applicable beyond the lab setting.

C. The audience for this is basic research.

D. I am a basic science researcher who studies host:pathogen interactions using influenza models of vaccination, virus pathogenesis, and secondary bacterial infections.

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Referee #1

Evidence, reproducibility and clarity

The study by Hemberg et al investigated whether the critical adaptor protein MAVS is required for IFN induction and viral resistance in primary human respiratory epithelial cells infected with influenza A virus (IAV). Specifically, air-liquid interface pulmonary bronchial epithelial cells (ALI-PBECs) are engineered with CRISPR/Cas9 to knockout MAVS (or AAVS1 as a control), followed by IAV infection and subsequent monitoring of the 1) IFN/ISG response and 2) viral replication. The study is thoroughly conducted, the methodology and the results are clearly described, and the study is written in a clear and transparent manner. No overstatements are made and limitations of the study are clearly indicated. I therefore only have a few minor comments:

• In the Discussion the following sentence should be nuanced: "However, most studies report no observable effect of MAVS KO on antiviral protection18,20". Please indicate that this refers to the context of IAV infection. I would also clarify that in this sentence you are referring to antiviral protection rather than IFN/ISG induction. (For example: While MAVS is important for IFN/ISG induction upon IAV infection, some studies in MAVS-deficient mice showed that this did not necessarily translate to increased antiviral protection). I would also advice to stay away from 'most studies report no observable effect' when you only reference two publications.
• Fig. 2A and 2B (and 2C and 2D): please indicate the time points in the graphs to better reflect (visually) the difference between the panels.

Significance

While the results of the study are not surprising (reduced IFN/ISG responses and increased IAV replication in MAVS KO cells), the scientific advance in this study is largely of a methodological nature: the role of MAVS in IAV infection has not been previously studied in this advanced culture model system. The study is of relevance to researchers that are in the immediate research field (virologists, RNA sensing). The study provides a useful example of CRISRP/Cas9 engineering in a complex model system to investigate the role of a particular gene in antiviral innate responses, which could easily be extrapolated to other genes.

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Reply to the reviewers

We appreciate the time and effort the reviewers have invested in providing constructive feedback on our manuscript. Below, we’ve detailed additional work, corrections, and improvements that we will complete during the revision process.

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

Summary

Folding is a major morphogenetic process that shapes tissues and organs in three dimensions. The mechanisms underlying tissue folding have been extensively explored and are often driven by actomyosin-based apical constriction. Here, the authors describe changes in cell geometry and mechanics during mouse neural tube formation. They build on quantitative fixed imaging and live junction ablation to extract cell geometry and junctional tension. These analyses are performed at different developmental stages and in both male and female embryos to propose a mechanical mechanism for neural tube elevation in the brain.

Major comments

The authors report quantitative data on cell geometry and junctional tension inferred from laser ablation. Overall, there are numerous statements that require stronger support from the experimental data. To substantiate several of their claims, the authors need to provide a larger number of data points-or at least comparable numbers across experimental conditions-for the tension measurements. Additional statistical analyses are required throughout to support the conclusions.

Figure 1

1. Does the projection algorithm account for tissue curvature when computing cell geometrical parameters such as area and anisotropy? At present, our projection algorithm does not correct for tissue curvature. Curvature in the tissue can make larger cells appear smaller in projections, skew the angle of cell orientations, and change aspect ratios. The largest curvature in the midbrain neural tube samples that we analyze is found in the transition region from the midline and lateral regions (~10-30% of tissue width) of 5 ss and 8ss embryos. The regions at the midline and more laterally are relatively flat. Therefore, distortion from curvature will not dramatically alter our key conclusions. We will apply a curvature correction using existing tools (Herbert S., et al (2021) BMC Biology) to sample images and determine if there are substantial differences in curvature-sensitive cells shape metrics. These will be included in a supplement to Figure 1. If there is a significant difference, we will expand the correction to all images that we analyze and update our analysis.

The authors should provide information on the accuracy and reliability of the cell segmentation.

We can provide a supplement to Figure 1 to demonstrate the accuracy of the segmentation. We have used F-Actin to segment cells in our images, which is enriched along the cell junctions but can also form medial cables that cross the cell surface. Junctional actomyosin is notably brighter than medial cables, and segmentation with our trained CellPose model is consistently able to distinguish the junctions. We also checked segmentation and performed manual corrections to ensure accuracy. To demonstrate this for our readers, we will prepare samples stained with both F-actin and ZO-1, a tight junction component that is localized to cell junctions. We will then segment the image twice in CellPose, once using the F-actin signal and once using the ZO-1 signal. The resulting cell outlines will then be digitally superimposed to show how much the signals overlap, and we will plot out the cell frequency as a function of area to determine if F-actin segmentations can segment with the same fidelity as ZO-1. Recent work by a co-author has shown excellent corroboration of neuroepithelial apical cell areas segmented using F-Actin and ZO-1 (Ampartzidis I., et al. eLife 2026). We are confident that our data will show a similar result.

The authors indicate that the rate of apical constriction differs between male and female embryos. However, apical sizes differ only at specific positions along the ML axis (Fig. 2H, I).

In Figure 2H, we show that at 5 ss males have larger apical areas than females at the midline, adjacent lateral cells, and at the surface ectoderm-neural epithelium border. By 8ss (Figure 2I), cells at the midline are smaller in males than females, while cells in more lateral regions are now equivalent between sexes. This change in apical area over time suggests that males have faster rates of constriction than females at the midline and adjacent lateral region where male cells become smaller or equivalent in size to female cells, respectively. We will perform statistical analysis (see comment #4) to determine if there are regions with significant differences in rate and amend our language to clarify that these differences are region specific as appropriate.

The authors should provide statistical analyses for the rates shown in Fig. 2J. Are these rates significantly different between males and females, and between medial and lateral regions?

Currently we calculate our rates using the difference in population averages of apical area at each stage shown in Figure 2H and 2I for each sex, and dividing by the number of somite stages, 3. As a result, there is only one rate value at each midline-lateral bin for each sex which is not amenable to statistical analysis. To correct this, we will calculate rates by subtracting the average apical area of each embryo at 8 ss from the population average of embryos at 5 ss. This will create 5 rates for both females and males at each 10% midline-lateral bin. We plan to perform a two-way ANOVA to determine if there are statistical differences in rates between males and females at each bin position and between medial and lateral regions. We will also add a section describing these calculations to the “Statistical Analysis” portion of the methods.

Please clearly state the main novelty of this study relative to the work published by Brooks et al.

Our study builds on the work of Brooks ER, et al. (2020) eLife. Brooks demonstrates that cells in a region of the lateral neural folds undergo apical constriction (Figure 1) and that cells at the midline do not (Figure 2). We expand and improve upon this work in the following ways:

1. A) As required by our funding sources at the NIH (NOT-OD-15-102) we have collected, analyzed, and reported on sex as a biological variable of interest. In doing so, we have shown that there are clear sex differences in apical area in the neural tube that were not previously shown. We also show that there is apical constriction within the neural tube midline in a sex dependent manner. Brooks et al do not address sex in their work.
2. B) We have provided more complete and spatially precise information on midline-lateral patterns of apical area and apical constriction. To show changes in apical area of lateral cells, Brooks selects a 100 x 100 µm region of interest in the midbrain (Figure 1E-F, Figure 2A) but does not specify the midline-lateral or rostral-caudal location of this region of interest or standardize it between embryos of different ages and dimensions. In our study, we’ve standardized our measurements to a 100 µm wide band across the midbrain adjacent to the midbrain/hindbrain boundary (Figure 2A-C). We also standardize positions as a percent distance from midline to account for differences in width between embryos and ages. This allows us to consistently compare similar populations of cells along the midline-lateral axis and determine changes in apical area over time.
3. C) We connect patterns of apical area and constriction to F-actin and Myosin-IIB density. Though Brooks et al report some analysis of F-actin in lateral cells (Figure 6), they do not analyze the midline cells or explore the relationship between cell shape and actomyosin.
4. D) Finally, we tested the mechanical properties of the tissue through laser ablation in living mouse embryos. From these ablations we’ve found that tension at the midline is less than in more lateral regions. Work in the neural tubes of frog (Haigo S., et al. (2003) Current Biology, Baldwin AT., et al. (2022) eLife, Matsuda M., et al. (2023) Nature Communications) and chicken (Kinoshita N., (2008) * Cell, Nishimura T., et al. (2012) Cell) embryos has conclusively shown that enriched midline actomyosin promotes apical contractility and drives hinge formation. It was therefore largely believed that a similar contractile hinge was employed in mammals (Copp AJ. and Green NDE. (2010) J. Pathol, Nikolopoulo E., et al. (2017) Development). Collectively, our work is the first to demonstrate that such a contractile hinge is not present in the mammalian brain neural tube. Figure 3*

The authors need to provide statistical support for the claim that large midline cells exhibit reduced F-actin and Myosin IIB levels.

We will conduct a two-way ANOVA to determine if there are statistical differences in F-actin and Myosin IIB density at the midline and more lateral regions in both males and females. We will update our language in the text and plots as appropriate from these results.

F-actin and Myosin IIB intensities should be plotted as a function of cell area to support the proposed anticorrelation between apical area and actomyosin levels.

We will make plots of cell areas vs. F-actin or Myosin IIB density for cells in each embryo. We will then fit a line to determine the R value for each embryo to determine if there is a negative correlation between cell area and actomyosin intensity. We will also adjust our language in the text as appropriate based on the results of these tests.

Statistical analyses are missing to substantiate the increase in F-actin levels between stages ss5 and ss8.

We will perform an F-test to determine homogeneity of variance between F-actin at 5 ss and 8 ss followed by the appropriate t-test to determine if there is a statistical increase in F-actin over time. We will also amend our language in the text to reflect the results of this test.

Figure S3 should be supported by plots showing Myosin II and F-actin intensity as a function of position along the ML axis, together with appropriate statistics.

In Figure 3A-D, we show representative images of F-Actin and Myosin IIB density in female embryos. These are plotted as the purple lines in Figure 3 E-H. Figure 3 Supplement 1 shows representative images of F-actin and Myosin IIB density in male embryos. These are plotted as the green lines in Figure 3 E-H. We will add a line in the caption of Figure 3 Supplement 1 indicating that these samples are represented and plotted in Figure 3. We also noted a typo in the respective captions, incorrectly indicating male or females were shown in the figure. We will correct these typos as well. Additionally, we will perform the statistical tests indicated under comment #6.

Figure 4

The authors state that lateral tension in male embryos is not different from midline tension, yet the number of data points is much lower than in females. To support this claim, the number of ablations should be comparable across sexes.

As part of this study we performed 270 ablations in the neural tubes of 83 mouse embryos: an exceptional scale of ablations that is the first of its kind in early embryos. We conducted our initial recoil velocity analysis blinded to information on sex. Male embryos were statistically underrepresented in our data set because male embryos develop faster than their female littermates (Seller MJ. and Perkins-Cole KJ. (1987) J. Reprod. Fert.). As such, the neural folds of male embryos were too elevated to ablate. At present we do not have the resources or justification to perform laser ablations on additional animals to obtain the number of male embryos needed to supplement the already exceptionally large data set. We will instead perform a power analysis to determine if: 1) we have a sample size large enough to detect a biologically-meaningful difference with suitable power, 2) the sample size required to detect the observed difference is so large that the difference would not be biologically meaningful, or 3) we do not have a sample size large enough to detect a difference confidently. With the results of this analysis, we will amend our language in the text to reflect the most accurate claims that can be made.

Is lateral tension different between males and females?

In Figure 4G we show that females have statistically different tension between the lateral and midline regions, while males do not. However, we do not test if the lateral or midline tension is different between females and males. We will perform an F-test and t-test to determine if there are statistical differences between males and females in this region.

Similarly, the data in Fig. S4 used to claim no change in tension over time are not supported by sufficient data points.

As discussed in comment #10, the scale of ablations is already substantial, and the initial recoil velocities were analyzed blinded to information on embryo age. We will calculate a best fit line for these plots to demonstrate if there is a trend in recoil velocity over time. We will then adjust our language in the text as appropriate with this added information.

Would the medial and lateral tensions reported in Fig. 4G remain unchanged if the authors perform statistical analyses on 10-15 ablations per condition?

We do not have a justification for removal or exclusion of any of the laser ablations analyzed in this study. We will instead perform a power analysis, as indicated in comment # 10, and adjust the language in the text as appropriate given the results of that analysis.

Figure 5

The number of data points in Fig. 5J and L is insufficient to support claims of no difference. The only detectable difference arises in the comparison with much higher sample size (Fig. 5L, ML vs RC).

In Figure 5J we disaggregate ablations performed at the midline by directionality (midline-lateral or rostral-caudal). We were unable to detect a statistically significant difference based on the direction of initial recoil velocity in either sex, though N’s for all categories are comparable. As discussed in comments #10 and #12, the scale of ablations conducted in this study is uniquely substantial. We will perform a power analysis for our anisotropy measurements in the lateral region of the tissue to determine if we have a sample size large enough to have detect a biologically-relevant difference with high confidence or if the sample size required to detect the observed difference is so large that the difference would not be biologically meaningful. Given the results of this analysis, we will amend our language in the text to reflect the most accurate claims that can be made.

The authors conclude that males have higher ML tension than RC tension, but given the limited data this conclusion should be amended to "no detectable difference."

In Figure 5L, we disaggregate ablations performed in the lateral regions, by directionality (midline-lateral or rostral-caudal). We find a statistical difference in the directionality of initial recoil velocity in females. In males, though we can observe a difference in the initial recoil velocity means, we are unable to detect a statistical difference, likely due to the smaller male sample size. As discussed in comments #10 and #12, the scale of ablations conducted in this study is uniquely substantial and was conducted blinded to embryo sex. Given that males develop faster than their female littermates (Seller MJ. and Perkins-Cole KJ. (1987) J. Reprod. Fert.) we were unable to obtain more males in our data set. We will perform a power analysis for our anisotropy measurements in the lateral region of the tissue to determine if: 1) we have a sample size large enough to detect a biologically-meaningful difference with suitable power, 2) the sample size required to detect the observed difference is so large that the difference would not be biologically meaningful, or 3) we do not have a sample size large enough to detect a difference confidently. With the results of this analysis, we will amend our language in the text to reflect the most accurate claims that can be made.

Code availability

The authors should provide access to the code used to generate the projections.

We are committed to ensuring open access to all code used as part of this study, including components of the projection workflow, data analysis, and figure creation. We are in the process of assembling a GitHub repository containing these files as well as documentation to allow for use by other members of the research community and public. We will publicly publish this documentary upon completion of the repository or at time of publication, whichever comes first.

Reviewer #1 (Significance (Required)):

The authors propose a mechanical model for neural tube elevation based on analyses of cell geometry and tension at two developmental stages. The reported differences in cell geometry or actomyosin levels do not appear to explain the differences in geometry or tension suggested between male and female embryos. This raises questions about the relationship between these measurements and their relevance for understanding the mechanisms of neural tube elevation.

If the major concerns outlined above are rigorously addressed, the manuscript will offer a valuable descriptive characterization of neural tube cell geometry and mechanical stress during morphogenesis. Such datasets could form a foundation for future studies investigating the mechanisms driving neural tube elevation.

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

The manuscript investigates the role of apical constriction and actomyosin organization in shaping the mouse brain neural epithelium during neural tube elevation, with particular emphasis on sex-specific differences. The authors develop an imaging and analysis pipeline to reconstruct the apical surface of the neural plate in three dimensions and perform quantitative measurements of apical cell area, actin, and myosin IIB distributions. Targeted laser ablation experiments are used to infer regional tissue tension.

The main findings can be summarized as follows. First, the authors identify a mediolateral gradient in apical cell area, with larger cells at the midline and smaller cells on the lateral neural folds, which inversely correlates with actomyosin density. Laser ablation experiments suggest that apical tension is lower and isotropic at the midline, whereas it is higher and anisotropic on the lateral folds, particularly in females. Second, sex-dependent differences in apical cell area, constriction rates, and actomyosin levels are reported at early somite stages, preceding previously described sex biases in neural tube defects.

The experimental work is technically solid, and the imaging and quantification pipeline represents a useful advance for analyzing large, curved epithelial surfaces. However, the study feels incomplete in its current form. Despite addressing neural tube elevation, the manuscript does not provide a comprehensive analysis of the folding process itself. Key aspects such as three-dimensional tissue morphology, curvature evolution, or global shape changes of the neural folds are not quantified. In addition, other potentially relevant cellular behaviors, such as proliferation, cell rearrangements, or contributions from neighboring tissues, are not examined, nor are they compared systematically between sexes.

Conceptually, the study focuses narrowly on correlations between apical cell area, actomyosin density, and inferred tension. While these measurements are carefully performed, the relationship between differential actomyosin contractility and three-dimensional tissue folding remains largely descriptive. No mechanical model or simulation framework is provided to link changes in actomyosin organization and cell shape to the emergence of neural folds and hinge formation. As a result, it is difficult to assess whether the measured differences in tension (on the order of ~40%) are sufficient to account for the proposed mechanical behavior of the tissue.

The central hypothesis advanced by the authors is that a relatively "soft" midline, flanked by stiffer, tension-bearing lateral folds, facilitates hinge formation during brain neurulation. However, this hypothesis is not directly tested by perturbation. For example, experimentally increasing contractility or stiffness at the midline (e.g., via optogenetic activation of apical constriction machinery) would provide a more direct test of causality. As it stands, the data demonstrate correlation rather than necessity or sufficiency.

Relatedly, alternative interpretations are not fully addressed. Large apical cell areas and low actomyosin levels at the midline could arise as a consequence of tissue geometry, contact with underlying structures such as the notochord, or extrinsic mechanical constraints, rather than being the primary cause of hinge formation. Similarly, anisotropic stresses generated at the tissue or embryo scale could align cells and actomyosin cables, producing the observed patterns without requiring locally specified apical tension differences as the initiating mechanism. The manuscript does not clearly distinguish whether apical tension asymmetries are a driver of folding or an emergent outcome of folding dynamics.

Finally, while the identification of sex differences is intriguing, it remains unclear what mechanistic insight is gained beyond establishing that such differences exist. The functional consequences of these differences for neural tube closure, robustness, or failure are not explored, nor is it clear how they integrate into the proposed lateral tension model.

In summary, this study provides high-quality measurements of apical cell geometry, actomyosin organization, and inferred tension in the mouse neural epithelium. However, the lack of direct perturbations, mechanical modeling, and quantitative analysis of three-dimensional tissue deformation limits the strength of the mechanistic conclusions. Addressing these gaps would substantially strengthen the manuscript and clarify the causal role of apical tension patterns in neural fold formation.

__ __The reviewer makes an excellent point, that direct perturbation of the system would enable us to test our hypothesis and inform whether the reduced contractility at the midline is essential for neural tube elevation. However, at present the technology needed to conduct an optogenetic experiment like that described by the reviewer does not exist. As with the laser ablations, an optogenetic experiment requires access to live and healthy embryos. Currently, mouse embryos can be cultured for several days in roller culture, where they are continuously rotated, or for several hours in static culture (Aguilera-Castrejon A. and Hanna JH. (2021) J. Vis. Exp.). Both techniques require that the yolk and amniotic sacs remain intact around the embryo. To access the apical surface of the brain neural tube for imaging, both sacs must be breached, after which the embryo has about 30 minutes before it begins to exhibit altered cellular morphology and tissue integrity and ultimate embryo death.

The neural tube elevates over several hours and closes fully after more than a day (Jacobson AG. and Tam PPL. (1982) The Anatomical Record). Even if we did acquire mice expressing photoactivatable constructs, the support membranes of the embryos would need to be breached to activate protein interactions. The embryos would die before any meaningful progress in neural tube elevation could be evaluated. Conducting an experiment like this would greatly advance our understanding of the system, and we hope that the needed technologies are developed to enable future work of this nature. The Galea lab previously purchased a photo-activatable Cre line, but was unable to induce deletion of a protein of interest using this allele before closure of the neural tube was completed (and the blue light needed to activate the cre was photo-toxic).

At present, there is some experimental evidence to suggest that lack of apical constriction at the midline if important for proper neural tube closure. Brooks ER, et al. (2020) eLife shows that a truncated Ift122 mutant, leads to abnormal constriction of the midline cells but does not disrupt lateral cell apical constriction, leading to a failure in brain neural tube closure in these embryos. Ift122 regulates trafficking and signaling proteins in cilia, which in turn regulates Sonic hedgehog signaling which Brooks ER, et al. also demonstrates regulates apical constriction. While this disruption is clearly multifaceted and nuanced, it provides some genetic support for the lack of apical constriction at the midline being important for neural tube closure.

Major Comments

Figure quality. Figure 1 contains very low-resolution images, which makes it difficult to evaluate the segmentation quality and tissue morphology. Higher-resolution versions should be provided.

In Figure 1, we outline the conceptual strategy and approach used to create and analyze shell projections of the curved neural tube. As much of our analysis builds from segmentation of cells in the projections, being able to assess segmentation quality from high resolution images is critical to evaluating the quality of the data shown. As discussed in comment #2, we will create a supplement to Figure 1 to demonstrate the accuracy of the segmentation. This will include high resolution images of both the label used to segment and the resulting segmentation, with corresponding overlays.

Cell segmentation strategy and validation. The authors segment cell areas using Myosin II and F-actin signals. This approach may introduce inaccuracies, as actomyosin cables can traverse the apical surface of individual cells and do not always coincide with cell boundaries. Segmentation based on junctional markers such as ZO-1 may be more appropriate. At minimum, the authors should provide a quantitative validation of segmentation accuracy, for example by overlaying segmentation results on raw images together with a nuclear marker (e.g., DAPI or H2B-GFP), to demonstrate that the number of segmented cells corresponds to the number of nuclei.

We will provide a supplement to Figure 1 to demonstrate the accuracy of the segmentation. We have used F-Actin to segment cells in our images. F-actin is enriched along junctions but cells can also have medial pools and F-actin cables, which might lead to errors. Though we understand the reviewer’s logic in asking to align segmentations with marked nuclei, the morphology of the neural epithelium makes this approach infeasible. The neural epithelium is pseudostratified, and nuclear position varies along the apical-basal axis depending on the cell cycle phase of each cell. As a result, an apical shell projection of nuclei would not capture all nuclei and a maximum intensity projection in Z of all nuclei would be uninterpretable as there would be substantial XY overlap between nuclei. Instead, we will create a supplement to Figure 1 to demonstrate the accuracy of the segmentation as discussed in comment #2. We will segment samples stained for both F-Actin and junctional markers like ZO-1. We will then create overlays of the resulting cell outlines and a cell area frequency plot for both segmentations to evaluate if F-actin based segmentation deviates from tight junction-based segmentation.

Lack of cross-sectional views of neural tube morphology. The manuscript would benefit from the inclusion of cross-sectional images of the neural tissue at different developmental stages. This would serve two purposes: (i) to demonstrate that the authors have a comprehensive understanding of the full three-dimensional folding process during neural tube closure, including medial and lateral hinge formation, and (ii) to allow readers to visualize the tissue geometry corresponding to the analyzed projection datasets (e.g., at 5 ss and 8 ss).

A key component of our model states that the changes in cell-level morphology and features correspond to changes in tissue level morphology (Figure 6). Specifically, that lateral apical constriction coincides with the flattening and elevation of the dorsal bulges on the lateral neural folds. We agree that it is beneficial to include additional visuals of tissue morphology. We plan to add an additional figure at the start of manuscript that details both the dorsal and relevant cross-sectional views of the somite stages analyzed. These visuals will take the form of graphical illustrations along with 3D confocal microscopy images and optical reconstructions of samples.

Sex-specific differences in overall neural plate morphology. The authors report that at 5 ss, males consistently have larger apical cell areas than females. It is unclear whether this difference reflects a global difference in neural plate morphology. Showing representative images of female and male neural plates would help readers directly assess whether there are overt morphological differences beyond those revealed by quantitative analysis.

If one sex has larger cells than the other, it would be reasonable to expect that the neural folds may be wider as well. In Figure 2B-C, we show representative images of male embryos at 5 and 8 ss. As part of the additions we indicated in comment #19, we will also include dorsal and cross-sectional views of both male and female embryos at the stages analyzed. If there is a difference in tissue morphology between sexes, we will also quantify these differences in tissue size, curvature, etc.

Cell number analysis. The authors state, based on prior literature, that cell numbers do not change between 5 and 8 ss. Given that the tissue is already segmented in the current study, this claim should be directly verified using the authors' own data. This analysis should be straightforward and would strengthen the conclusions.

We agree and will determine the number of cells analyzed for each embryo to test if there are changes in cell numbers at different stages and between sexes, along with appropriate statistical tests.

Relation between tissue curvature and cellular properties. It would be highly informative to extract the three-dimensional morphology of the neural plate, in particular its curvature, and examine how curvature correlates with two-dimensional cell anisotropy, apical area, and F-actin/Myosin intensity. For example, at 8 ss the authors report a U-shaped dependence of cell area along the mediolateral axis. How does this pattern relate to local tissue curvature?

We agree with this assessment and will create optical reslices in the midbrain adjacent to but excluding the midbrain hindbrain boundary. We will then divide the apical surface into 10% bins and fit a circle to the apical surface of the neural epithelium in each to calculate the local radius of curvature, which is the reciprocal of curvature for the surface. We can then correlate these values with two-dimensional cell shape and actomyosin density metrics.

Visualization of sex differences in medial actin levels (Figure 3). In Figure 3, the reported female-male difference in medial actin levels would benefit from visualization of the raw data. A zoomed-in inset of the midline region, shown separately for females and males, would help substantiate this claim.

In Figure 3, we demonstrate patterns of the whole-cell apical F-actin (Fig. 3A, B) and Myosin IIB (Fig. 3C, D) density. We find that there is no difference in F-Actin density between males and females (Fig. 3E, F), but a significant difference in midline Myosin IIB density at 5 ss that is mostly absent by 8 ss (Fig. 3G, H). We currently provide representative images for female and male myosin IIB expression across the midline-lateral axis in Figure 3C, D, and Figure 3-Supplement 1C and D. We can provide a close-up image of Myosin IIB in the midline region for both sexes as part of Figure 3, with additional annotations on existing representative image to indicate their origin.

Typographical error. Line 143: please correct "cell are" to "cell area".

We thank the reviewer for pointing out this error and will correct this typo and perform additional editing to correct any other typos present in the manuscript.

Quantitative correlation analysis between cell area and actomyosin. The authors qualitatively discuss the relationship between cell area dynamics and actomyosin levels. It would strengthen the analysis to directly compute and report correlations between these variables, and to explicitly test whether actin and myosin levels are anti-correlated with apical cell area.

As discussed in comment #6, we will plot cell area vs. F-actin or Myosin IIB density for each embryo and fit a line to calculate their correlation coefficient. From there, we will determine if there is a negative correlation between cell area and actomyosin intensity.

Interpretation of anti-correlation and contractile hinge mechanism. In lines 143-157, the authors state that the observed anti-correlation between actomyosin and cell area argues against a contractile hinge mechanism. However, this anti-correlation could also suggest that apical cell area is determined by local mechanical or geometric constraints rather than by local actomyosin contractility. The authors should clarify and discuss this alternative interpretation.

Within the neural epithelium of mice and other vertebrates, F-actin and myosin-IIB are enriched on the apical surface relative to other regions of the cell (Sadler TW, et al. (1982) Science, Matsuda M., et al. (2023), Nat. Communication, Röper, K. (2013) BioArchitecture). This poises the actomyosin network to be able to selectively constrict the apical surface relative to the basal side of the cells. Apical constriction is observed to actively facilitate the formation of hinges in folding tissues (Chanet S, et al. (2017), Nature Communications, Nishimura T., et al. (2012) Cell, Chistrodoulou N., et al. (2015) Cell Reports) in what we term the contractile hinge model of tissue folding. Tissues that employ this model of folding are expected to have small apical areas and apical enrichment of contractile actomyosin at the hinge point during folding. We observe large apical areas, low apical actomyosin density, and low apical tension at the midline hinge of the mouse midbrain neural tube, which are all inconsistent with a contractile hinge mechanism being employed in this tissue folding process. We agree with the reviewer that “cell shape does not always match [acto]myosin contractility levels, because cell shape depends on extrinsic, as well as intrinsic forces” (Line 147-149). We also agree that anticorrelation of actomyosin density and apical cell area does not per se argue against the contractile hinge model and will amend our language to be clearer. We will also further elaborate on potential extrinsic factors that may lead to the observed cell behaviors at the midline in the discussion.

Statistical robustness of laser ablation results (Figure 4). The differences in recoil velocity between regions appear small, with substantial overlap between the distributions. In addition, the sample sizes for lateral versus midline ablations appear unequal (with visibly more data points in the lateral condition). These factors raise concerns about the robustness and statistical significance of the reported differences, which should be addressed more carefully.

In Figure 4E, we show initial recoil velocities binned only by region: lateral vs. midline and report a 3.03 μm/s vs. 2.40 μm/s, or 26% difference between the two regions. We then show in Figure 4G that by considering another relevant variable, sex, we find initial recoil to be 3.15 μm/s vs. 2.30 μm/s, or 37% difference in females and 2.68 μm/s vs. 2.57 μm/s, or 4% difference in males. We go on to show In Figure 5L that within the lateral region that recoils also vary by direction, with a 38% difference. Ultimately the final conclusions that we draw regarding tissue tension that we present in our model are derived from the most finely disaggregated data in Figure 5. Our goal in presenting a stepwise disaggregation of the data was to demonstrate which variables had the greatest impact on the variance within our data set. We agree with the reviewer that a more precise statistical analysis of this data set is warranted that accounts for the complexity and multitude of variables that can influence our conclusions. In addition to the power analysis described in comment #10, we plan to conduct a mixed-effect model analysis of our data that considers factors including sex, age, cut direction, cut region, cut number, and embryos to determine which factors explain the most variance in the population. We will add this analysis as a supplement to Figure 4 alongside a description of the tests performed in the Statistical Analysis section of the methods. We will also adjust our language in the text to clearly state the limitations of the data as presented and qualify conclusions as appropriate.

Speculative statement regarding anisotropic tension in males. Line 278: "We believe that both sexes demonstrate anisotropic tension, given that males have cell aspect ratios and orientations in the lateral neural folds similar to females." This statement is speculative. Either anisotropic tension in males should be directly measured and reported, or this statement should be removed.

As discussed in comment # 15, in Figure 5L, though we can observe a difference in the initial recoil velocity means, we are unable to detect a statistical difference. Ablations were conducted blinded to embryo sex, but fewer male embryos were suitable for ablation because males develop faster than their female littermates (Seller MJ. and Perkins-Cole KJ. (1987) J. Reprod. Fert.). We were therefore unable to obtain more males in our data set. At present we do not have the resources to perform additional laser ablations to supplement the existing data set. We will instead perform a power analysis for our anisotropy measurements in the lateral region of the tissue to determine if: 1) we have a sample size large enough to detect a biologically-meaningful difference with suitable power, 2) the sample size required to detect the observed difference is so large that the difference would not be biologically meaningful, or 3) we do not have a sample size large enough to detect a difference confidently. With the results of this analysis, we will amend our language in the text to reflect the most accurate claims that can be made.

Reviewer #2 (Significance (Required)):

This study provides high-quality measurements of apical cell geometry, actomyosin organization, and inferred tension in the mouse neural epithelium. However, the lack of direct perturbations, mechanical modeling, and quantitative analysis of three-dimensional tissue deformation limits the strength of the mechanistic conclusions. Addressing these gaps would substantially strengthen the manuscript and clarify the causal role of apical tension patterns in neural fold formation. At the end of the day, the authors suggest an hypothesis that is not well support by their data, which is of high quality.

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

Summary

This manuscript by De La O et al addresses a long-standing question of how actomyosin contributes mechanically to cranial neural tube elevation in the mouse, a system in which classical midline contractile hinge models appear insufficient. The authors develop an image-processing and analysis pipeline that enables reconstruction and quantitative analysis of the apical actomyosin network across the large, curved dorsal surface of the mouse brain neuroepithelium. Using this approach, combined with laser ablation-based tension measurements in live embryos, they report a medio-lateral gradient of apical cell area and an inverse gradient of actomyosin density. Contrary to contractile hinge models described in frog, chick and invertebrate systems, they find that the midline exhibits low, isotropic tension, while the lateral neural folds show higher anisotropic apical tension, consistent with their proposal of a "lateral tension" mechanism for neural tube elevation.

The work provides an important reframing of actomyosin function in mammalian cranial neurulation, supported by extensive quantitative imaging and mechanical measurements. The finding that lateral, rather than midline, actomyosin networks dominate tissue tension is compelling and helps reconcile previous observations that midline hinge formation in mouse can proceed despite actomyosin perturbation. The study is technically sophisticated and addresses a biologically important process with clear relevance to neural tube defect etiology. However, several aspects of the statistical treatment, interpretation of laser ablation data, and mechanistic framing require clarification or tempering to fully support the authors' conclusions.

Major comments

Statistical unit and pseudo-replication in cell-based analyses (Figures 2-3)

In Figures 2 and 3, it is unclear whether statistical comparisons were performed at the level of individual cells or embryos. Because cells are nested within embryos, treating cells as independent observations raises concerns about pseudo-replication and inflated statistical significance, particularly for sex-dependent effects. While the color-coded maps are visually compelling, they may overstate confidence in differences between conditions if embryo-to-embryo variability is not explicitly accounted for.

Clarification is needed as to whether statistical testing was performed on embryo-level summary values (e.g., one value per embryo per positional bin), or whether hierarchical or mixed-effects models were used with embryo treated as a random effect. Providing embryo-level summary plots would also help readers assess inter-embryo variability. Addressing this point is important for confidence in both the reported medio-lateral gradients and the sex differences.

We agree with the reviewer that it is inappropriate to calculate statistics based on measurements of individual cells. As indicated under the ‘Statistical Analysis and Figure Assembly’ section of our methods “For fixed images, cell shape and protein intensity analysis (Figure 2H-J, Figure 3E-H, Figure 5E-H), N = 5 embryos for all conditions and n, or the number of cells in each 10% bin, is ≥ 150 cells for each embryo” (Line 556 – 558). The average and SD between embryos are shown in these plots and is calculated at the embryo level, not the cell level. We chose to consolidate this information in the methods section as the same data set is used across the three figures. We will add a line to the figure captions that N values for all experiments can be found in this section of the methods. We will also provide supplementary plots showing the bin averages for each individual embryo, color coded by embryo to show the distribution of the data set.

Interpretation of actomyosin density as a proxy for contractility (Figure 3)

The descriptive correlation between apical cell area and actomyosin density is clear and consistent. However, actomyosin abundance alone does not necessarily equate to force generation, particularly in the absence of measurements of myosin activation state (e.g., pMLC), actomyosin dynamics, or direct perturbations linking actomyosin levels to mechanical output. Although the authors appropriately note that cell shape does not always reflect intrinsic contractility, actomyosin density is nevertheless used to argue against a contractile hinge mechanism.

While the subsequent laser ablation experiments address tissue tension more directly, the mechanistic conclusions drawn from actomyosin density measurements alone would benefit from more careful qualification. Tempering language that equates actomyosin enrichment with contractile output, or explicitly acknowledging these limitations, would strengthen the interpretation.

It is largely believed that apical pools of actomyosin are active and that apical localization of actomyosin is dependent on activation. Shroom3, an actin-binding protein, is localized to the apical adherens junctions in the neural tube (Haigo SL., et al. (2003) Curr. Biol., Hildebrand JD. and Soriano P. (1999) Cell), where it can recruit Rho kinases (ROCKs) that in turn phosphorylate and activate Myosin IIB (Nishimura T. and Takeichi M. (2008) Dev.). Mutations in Shroom3 lead to neural tube close defects and its overexpression in the neural tube can induce apical constriction and increased apical accumulation of Myosin II tube (Haigo SL., et al. (2003) Curr. Biol., Hildebrand JD. (2005) J. Cell Sci.). In the mouse neural tube, Myosin IIB intensity is greater in cells that can apically constrict than in those that cannot constrict (Galea GL., et al. (2021) Nat Commun). Additionally, inhibition of ROCK reduces apical tension, presumably by reduction of activated Myosin II (Butler MB., et al. (2019) J. Cell Sci.). We agree with the reviewer’s assessment that to definitively state that the apical pools of Myosin IIB and F-actin are promoting apical contractility, a demonstration of the phosphorylation state of the Myosin II regulatory light chain (pMLC) or observations/perturbations in live embryos is necessary. We will adjust our language to reflect this limitation. We will also provide information on the relationship between apically localized actomyosin and contractility.

Statistical and biological independence of laser ablation measurements (Figures 4-5)

The Methods indicate that 155 laser ablations were analyzed across 71 embryos, implying that multiple ablations were performed per embryo. It would be helpful to clarify how this hierarchical data structure was handled statistically. Specifically, were recoil velocities averaged per embryo, paired with embryos for ML vs. RC comparisons, or analyzed using hierarchical/mixed-effects models?

Our laser ablation data set captures variables including embryo sex, age, cut location, cut direction, and cut number. Therefore, we did not feel it appropriate to average recoils within the same embryo as these cuts were intentionally in different regions (lateral vs midline) or in different orientations (i.e. a rostral-caudal cut and midline-lateral cut on opposite lateral folds), which our analysis has shown would lead to averaging out potential differences. Ablations were far apart from each other, and we had checked that ablation order did not predict changes in recoil. However, we agree with the reviewer that a more precise statistical analysis of this data set is warranted that accounts for the complexity of variables potentially influencing initial recoil velocities. As discussed in comment #27, we plan to conduct a mixed-effect model analysis of our data that considers the above and add this analysis as a supplement to figure 4. We will include a description of this in the methods and our language in the text to clearly state the limitations of the data as presented and qualify conclusions as appropriate.

In addition, embryos were subjected up to 5 ablations within a short time window. Because laser ablation disrupts tissue integrity and can induce rapid cytoskeletal remodeling, it is unclear whether later ablations represent independent measurements of the native tension state. Clarification is needed regarding whether the authors tested for effects of ablation order (e.g., first vs. later cuts), ensured sufficient spatial separation between ablation sites, or verified that repeated ablations did not systematically alter recoil measurements. Demonstrating that initial recoil velocity is independent of cut number would substantially strengthen confidence in the mechanical conclusions.

We agree with the reviewer that laser ablations cause disruptions to tissue, and these disruptions can impact the results of additional ablations performed near the site of prior ablations. The average embryo in our data set has three ablations: one on either neural fold and one at the midline, with hundreds of µm distances from each other. In embryos that had more than 3 ablations made far away from each other (additional ablations were performed in the hindbrain rhombomeres, rhombomere boundaries, at the neuroepithelium and surface ectoderm boundary, or at the zipper point, but n numbers of these are insufficient for analysis). We will supplement the methods text describing the laser ablations to clarify this for readers. Additionally, after an ablation, displacement is not detectable further than 3-5 cell lengths away from the cut even after several seconds post ablation. We will provide visual examples of these cuts after ablation to demonstrate this phenomenon. As discussed in comment #27 and #32, we will also perform mixed-effect modeling to determine if cut number impacts observed initial recoil velocities. We will also provide plots demonstrating relevant examples of these comparisons (e.g. sequential lateral cuts made in the same direction).

Interpretation of sex-dependent tension differences (Figures 4-5)

Figure 4 shows a clear lateral-greater-than-midline tension difference in females, whereas this pattern is not detected in males under initial analysis. Later, Figure 5 reveals directional anisotropy in the lateral neural folds of both sexes. As currently framed, this creates some ambiguity regarding whether the proposed lateral tension mechanism is sex-specific, sex-biased in magnitude, or sex-general but masked by directional averaging in males.

Clarifying this distinction, both in figure presentation and in the text, would strengthen the mechanistic interpretation and prevent confusion. In particular, it would be helpful to more clearly explain how directional anisotropy reconciles the apparent absence of regional tension differences in males in Figure 4.

We appreciate the reviewer taking the time to indicate this point of confusion. We ultimately conclude that the lateral tension model of neural tube elevation is agnostic of sex. Though there are nuanced differences in some of the details regarding Myosin IIB density, midline apical constriction and tension anisotropy, we do not believe these differences would fundamentally change the mechanical model used between sexes. With specific regards to masking of the lateral neural fold tension in males, we briefly address this in the discussion: “The averaging of [Rostra-Caudal] and [Midline-Lateral] [Initial Recoil Velocities] likely masked tension differences between the midline hinge and lateral neural folds, creating the false impression that males did not have high tension on the lateral neural folds” (Line 280-282). We will adjust the text in the results and discussion section to clearly indicate that are lateral tension model applies to both sexes, though some differences in specific details exist, and that averaging may have led to the result in Figure 4G.

Causal overreach in mechanistic interpretation of anisotropic tension

While the laser ablation data convincingly demonstrates spatial and directional differences in recoil consistent with patterned mechanical anisotropy, the manuscript frequently treats anisotropic apical tension as a mechanistic explanation for neural tube elevation. The presented experiments do not directly test whether anisotropic apical tension is necessary or sufficient for tissue bending, nor whether isotropic tension at the midline plays a causal role. Initial recoil velocity reflects not only pre-existing tension but also tissue geometry and viscoelastic properties, which may differ between midline and lateral regions.

As such, statements suggesting that anisotropic lateral tension "explains" neural fold elevation should be tempered or reframed. The data strongly support spatial patterning of mechanical properties but do not yet establish causal primacy. Recasting the model as a mechanically consistent framework rather than a definitive mechanism would better align conclusions with the data.

Our lateral tension model proposes that a regionalized difference in tension, with high tension in the lateral neural folds and low tension at the midline, is needed to enable neural tube elevation and ultimate closure. We agree with the reviewer, our work demonstrates that the results of our laser ablation experiments, along with measurements of cell shapes and protein density, are consistent with the lateral tension model that we propose. Our model is also supported by past work that shows that perturbations that disrupt actomyosin contractility leads to defects in brain neural tube elevation and closure but not midline hinge formation. For example, chemical perturbation of actin polymerization with Cytochalasin D (Ybot-Gonzalez P. and Copp AJ. (1999) Dev. Dyn), and genetic perturbations of Shroom 3, which apically localizes actomyosin (Hildebrand JD. And Soriano P. (1999) Cell) or Fhod3, which promotes actin polymerization (Sulistomo HW, et al. (2019) J. Biol. Chem.) all have brain neural tube closure defects but form a midline hinge. However, since we do not directly perturb tension, we have only demonstrated consistency rather than causality or sufficiency. We will adjust and temper our language accordingly in the relevant sections of the results and discussion.

Minor comments

Manuscript length and clarity

The manuscript is longer and more complex than necessary for its central message. Several sections of the Results, particularly methodological validation and somite-stage stratification, could be streamlined.

We agree with the reviewer and will continue editing the manuscript, prioritizing clarity, brevity, and precision of language so that readers are able to quickly understand the key points of the manuscript.

Sex differences section

The section on sex differences is interesting but somewhat tangential. Clarifying whether these findings are intended as mechanistic insight or observational motivation for future work could improve focus.

  We intended this section to offer up perspectives that inform and motivate future work to continue to track, analyze, and report on sex difference during development. We will edit this section of the discussion to improve clarity and brevity so that the reader can easily acquire this takeaway. Sex differences in the penetrance of exencephaly is an active area of research and our manuscript provides the first cell-level measurements which will guide the field in disaggregating future analyses by embryo sex.

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript by De La O et al addresses a long-standing question of how actomyosin contributes mechanically to cranial neural tube elevation in the mouse, a system in which classical midline contractile hinge models appear insufficient. The authors develop an image-processing and analysis pipeline that enables reconstruction and quantitative analysis of the apical actomyosin network across the large, curved dorsal surface of the mouse brain neuroepithelium. Using this approach, combined with laser ablation-based tension measurements in live embryos, they report a medio-lateral gradient of apical cell area and an inverse gradient of actomyosin density. Contrary to contractile hinge models described in frog, chick and invertebrate systems, they find that the midline exhibits low, isotropic tension, while the lateral neural folds show higher anisotropic apical tension, consistent with their proposal of a "lateral tension" mechanism for neural tube elevation.

The work provides an important reframing of actomyosin function in mammalian cranial neurulation, supported by extensive quantitative imaging and mechanical measurements. The finding that lateral, rather than midline, actomyosin networks dominate tissue tension is compelling and helps reconcile previous observations that midline hinge formation in mouse can proceed despite actomyosin perturbation. The study is technically sophisticated and addresses a biologically important process with clear relevance to neural tube defect etiology. However, several aspects of the statistical treatment, interpretation of laser ablation data, and mechanistic framing require clarification or tempering to fully support the authors' conclusions.

Major comments

1. Statistical unit and pseudo-replication in cell-based analyses (Figures 2-3) In Figures 2 and 3, it is unclear whether statistical comparisons were performed at the level of individual cells or embryos. Because cells are nested within embryos, treating cells as independent observations raises concerns about pseudo-replication and inflated statistical significance, particularly for sex-dependent effects. While the color-coded maps are visually compelling, they may overstate confidence in differences between conditions if embryo-to-embryo variability is not explicitly accounted for.

Clarification is needed as to whether statistical testing was performed on embryo-level summary values (e.g., one value per embryo per positional bin), or whether hierarchical or mixed-effects models were used with embryo treated as a random effect. Providing embryo-level summary plots would also help readers assess inter-embryo variability. Addressing this point is important for confidence in both the reported medio-lateral gradients and the sex differences. 2. Interpretation of actomyosin density as a proxy for contractility (Figure 3) The descriptive correlation between apical cell area and actomyosin density is clear and consistent. However, actomyosin abundance alone does not necessarily equate to force generation, particularly in the absence of measurements of myosin activation state (e.g., pMLC), actomyosin dynamics, or direct perturbations linking actomyosin levels to mechanical output. Although the authors appropriately note that cell shape does not always reflect intrinsic contractility, actomyosin density is nevertheless used to argue against a contractile hinge mechanism.

While the subsequent laser ablation experiments address tissue tension more directly, the mechanistic conclusions drawn from actomyosin density measurements alone would benefit from more careful qualification. Tempering language that equates actomyosin enrichment with contractile output, or explicitly acknowledging these limitations, would strengthen the interpretation. 3. Statistical and biological independence of laser ablation measurements (Figures 4-5) The Methods indicate that 155 laser ablations were analyzed across 71 embryos, implying that multiple ablations were performed per embryo. It would be helpful to clarify how this hierarchical data structure was handled statistically. Specifically, were recoil velocities averaged per embryo, paired with embryos for ML vs. RC comparisons, or analyzed using hierarchical/mixed-effects models?

In addition, embryos were subjected up to 5 ablations within a short time window. Because laser ablation disrupts tissue integrity and can induce rapid cytoskeletal remodeling, it is unclear whether later ablations represent independent measurements of the native tension state. Clarification is needed regarding whether the authors tested for effects of ablation order (e.g., first vs. later cuts), ensured sufficient spatial separation between ablation sites, or verified that repeated ablations did not systematically alter recoil measurements. Demonstrating that initial recoil velocity is independent of cut number would substantially strengthen confidence in the mechanical conclusions. 4. Interpretation of sex-dependent tension differences (Figures 4-5) Figure 4 shows a clear lateral-greater-than-midline tension difference in females, whereas this pattern is not detected in males under initial analysis. Later, Figure 5 reveals directional anisotropy in the lateral neural folds of both sexes. As currently framed, this creates some ambiguity regarding whether the proposed lateral tension mechanism is sex-specific, sex-biased in magnitude, or sex-general but masked by directional averaging in males.

Clarifying this distinction, both in figure presentation and in the text, would strengthen the mechanistic interpretation and prevent confusion. In particular, it would be helpful to more clearly explain how directional anisotropy reconciles the apparent absence of regional tension differences in males in Figure 4. 5. Causal overreach in mechanistic interpretation of anisotropic tension While the laser ablation data convincingly demonstrates spatial and directional differences in recoil consistent with patterned mechanical anisotropy, the manuscript frequently treats anisotropic apical tension as a mechanistic explanation for neural tube elevation. The presented experiments do not directly test whether anisotropic apical tension is necessary or sufficient for tissue bending, nor whether isotropic tension at the midline plays a causal role. Initial recoil velocity reflects not only pre-existing tension but also tissue geometry and viscoelastic properties, which may differ between midline and lateral regions.

As such, statements suggesting that anisotropic lateral tension "explains" neural fold elevation should be tempered or reframed. The data strongly support spatial patterning of mechanical properties but do not yet establish causal primacy. Recasting the model as a mechanically consistent framework rather than a definitive mechanism would better align conclusions with the data.

Minor comments

1. Manuscript length and clarity The manuscript is longer and more complex than necessary for its central message. Several sections of the Results, particularly methodological validation and somite-stage stratification, could be streamlined.
2. Sex differences section The section on sex differences is interesting but somewhat tangential. Clarifying whether these findings are intended as mechanistic insight or observational motivation for future work could improve focus.

Significance

General assessment.

This study provides a technically sophisticated and carefully executed analysis of the mechanical organization of the mouse cranial neural epithelium during neural tube elevation. Its principal strengths lie in the development of a large-scale apical imaging and reconstruction pipeline, the quantitative mapping of medio-lateral gradients in cell shape and actomyosin organization, and the use of laser ablation to directly probe regional and directional tissue tension in live embryos. Together, these approaches allow the authors to address a long-standing discrepancy between classical contractile hinge models and prior observations in mouse neurulation. The main limitations of the study relate not to data quality, but to interpretation: several conclusions rely on correlational relationships between actomyosin enrichment, cell shape anisotropy, and tissue tension, and the mechanistic language at times exceeds what is directly tested. Clarification of statistical structure and tempering of causal claims would substantially strengthen the work.

Advance.

Relative to prior studies of neural tube closure in frog, chick, and invertebrate systems, this work advances the field by providing direct, spatially resolved measurements of tissue tension in the mouse cranial neural tube. The identification of low, largely isotropic tension at the midline and higher, anisotropic tension in the lateral neural folds represents a conceptual advance that reframes how actomyosin contributes to mammalian neurulation. While the study does not establish causality between anisotropic apical tension and tissue bending, it offers a mechanically consistent alternative to contractile hinge models and provides a valuable framework for interpreting species-specific differences in neural tube morphogenesis. The advance is therefore primarily conceptual and technical, rather than mechanistic in the strict causal sense.

Audience.

This work will be of strong interest to a specialized but broad audience spanning developmental biology, epithelial mechanics, morphogenesis, and neural tube defect research. The imaging and analytical approaches are likely to be useful beyond neurulation, particularly for investigators studying force patterning in large, curved epithelial tissues. With appropriate framing, the study should also be of interest to researchers investigating the biomechanical basis of congenital defects, even if its immediate implications are primarily basic rather than translational.

Field of expertise.

My expertise lies in epithelial morphogenesis, tissue mechanics, actomyosin-based force generation, and quantitative imaging in developmental systems. I do not have specific expertise in clinical aspects of neural tube defect diagnosis or treatment.

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Referee #2

Evidence, reproducibility and clarity

The manuscript investigates the role of apical constriction and actomyosin organization in shaping the mouse brain neural epithelium during neural tube elevation, with particular emphasis on sex-specific differences. The authors develop an imaging and analysis pipeline to reconstruct the apical surface of the neural plate in three dimensions and perform quantitative measurements of apical cell area, actin, and myosin IIB distributions. Targeted laser ablation experiments are used to infer regional tissue tension.

The main findings can be summarized as follows. First, the authors identify a mediolateral gradient in apical cell area, with larger cells at the midline and smaller cells on the lateral neural folds, which inversely correlates with actomyosin density. Laser ablation experiments suggest that apical tension is lower and isotropic at the midline, whereas it is higher and anisotropic on the lateral folds, particularly in females. Second, sex-dependent differences in apical cell area, constriction rates, and actomyosin levels are reported at early somite stages, preceding previously described sex biases in neural tube defects.

The experimental work is technically solid, and the imaging and quantification pipeline represents a useful advance for analyzing large, curved epithelial surfaces. However, the study feels incomplete in its current form. Despite addressing neural tube elevation, the manuscript does not provide a comprehensive analysis of the folding process itself. Key aspects such as three-dimensional tissue morphology, curvature evolution, or global shape changes of the neural folds are not quantified. In addition, other potentially relevant cellular behaviors, such as proliferation, cell rearrangements, or contributions from neighboring tissues, are not examined, nor are they compared systematically between sexes.

Conceptually, the study focuses narrowly on correlations between apical cell area, actomyosin density, and inferred tension. While these measurements are carefully performed, the relationship between differential actomyosin contractility and three-dimensional tissue folding remains largely descriptive. No mechanical model or simulation framework is provided to link changes in actomyosin organization and cell shape to the emergence of neural folds and hinge formation. As a result, it is difficult to assess whether the measured differences in tension (on the order of ~40%) are sufficient to account for the proposed mechanical behavior of the tissue.

The central hypothesis advanced by the authors is that a relatively "soft" midline, flanked by stiffer, tension-bearing lateral folds, facilitates hinge formation during brain neurulation. However, this hypothesis is not directly tested by perturbation. For example, experimentally increasing contractility or stiffness at the midline (e.g., via optogenetic activation of apical constriction machinery) would provide a more direct test of causality. As it stands, the data demonstrate correlation rather than necessity or sufficiency.

Relatedly, alternative interpretations are not fully addressed. Large apical cell areas and low actomyosin levels at the midline could arise as a consequence of tissue geometry, contact with underlying structures such as the notochord, or extrinsic mechanical constraints, rather than being the primary cause of hinge formation. Similarly, anisotropic stresses generated at the tissue or embryo scale could align cells and actomyosin cables, producing the observed patterns without requiring locally specified apical tension differences as the initiating mechanism. The manuscript does not clearly distinguish whether apical tension asymmetries are a driver of folding or an emergent outcome of folding dynamics.

Finally, while the identification of sex differences is intriguing, it remains unclear what mechanistic insight is gained beyond establishing that such differences exist. The functional consequences of these differences for neural tube closure, robustness, or failure are not explored, nor is it clear how they integrate into the proposed lateral tension model.

In summary, this study provides high-quality measurements of apical cell geometry, actomyosin organization, and inferred tension in the mouse neural epithelium. However, the lack of direct perturbations, mechanical modeling, and quantitative analysis of three-dimensional tissue deformation limits the strength of the mechanistic conclusions. Addressing these gaps would substantially strengthen the manuscript and clarify the causal role of apical tension patterns in neural fold formation.

Major Comments

1. Figure quality. Figure 1 contains very low-resolution images, which makes it difficult to evaluate the segmentation quality and tissue morphology. Higher-resolution versions should be provided.
2. Cell segmentation strategy and validation. The authors segment cell areas using Myosin II and F-actin signals. This approach may introduce inaccuracies, as actomyosin cables can traverse the apical surface of individual cells and do not always coincide with cell boundaries. Segmentation based on junctional markers such as ZO-1 may be more appropriate. At minimum, the authors should provide a quantitative validation of segmentation accuracy, for example by overlaying segmentation results on raw images together with a nuclear marker (e.g., DAPI or H2B-GFP), to demonstrate that the number of segmented cells corresponds to the number of nuclei.
3. Lack of cross-sectional views of neural tube morphology. The manuscript would benefit from the inclusion of cross-sectional images of the neural tissue at different developmental stages. This would serve two purposes: (i) to demonstrate that the authors have a comprehensive understanding of the full three-dimensional folding process during neural tube closure, including medial and lateral hinge formation, and (ii) to allow readers to visualize the tissue geometry corresponding to the analyzed projection datasets (e.g., at 5 ss and 8 ss).
4. Sex-specific differences in overall neural plate morphology. The authors report that at 5 ss, males consistently have larger apical cell areas than females. It is unclear whether this difference reflects a global difference in neural plate morphology. Showing representative images of female and male neural plates would help readers directly assess whether there are overt morphological differences beyond those revealed by quantitative analysis.
5. Cell number analysis. The authors state, based on prior literature, that cell numbers do not change between 5 and 8 ss. Given that the tissue is already segmented in the current study, this claim should be directly verified using the authors' own data. This analysis should be straightforward and would strengthen the conclusions.
6. Relation between tissue curvature and cellular properties. It would be highly informative to extract the three-dimensional morphology of the neural plate, in particular its curvature, and examine how curvature correlates with two-dimensional cell anisotropy, apical area, and F-actin/Myosin intensity. For example, at 8 ss the authors report a U-shaped dependence of cell area along the mediolateral axis. How does this pattern relate to local tissue curvature?
7. Visualization of sex differences in medial actin levels (Figure 3). In Figure 3, the reported female-male difference in medial actin levels would benefit from visualization of the raw data. A zoomed-in inset of the midline region, shown separately for females and males, would help substantiate this claim.
8. Typographical error. Line 143: please correct "cell are" to "cell area".
9. Quantitative correlation analysis between cell area and actomyosin. The authors qualitatively discuss the relationship between cell area dynamics and actomyosin levels. It would strengthen the analysis to directly compute and report correlations between these variables, and to explicitly test whether actin and myosin levels are anti-correlated with apical cell area.
10. Interpretation of anti-correlation and contractile hinge mechanism. In lines 143-157, the authors state that the observed anti-correlation between actomyosin and cell area argues against a contractile hinge mechanism. However, this anti-correlation could also suggest that apical cell area is determined by local mechanical or geometric constraints rather than by local actomyosin contractility. The authors should clarify and discuss this alternative interpretation.
11. Statistical robustness of laser ablation results (Figure 4). The differences in recoil velocity between regions appear small, with substantial overlap between the distributions. In addition, the sample sizes for lateral versus midline ablations appear unequal (with visibly more data points in the lateral condition). These factors raise concerns about the robustness and statistical significance of the reported differences, which should be addressed more carefully.
12. Speculative statement regarding anisotropic tension in males. Line 278: "We believe that both sexes demonstrate anisotropic tension, given that males have cell aspect ratios and orientations in the lateral neural folds similar to females." This statement is speculative. Either anisotropic tension in males should be directly measured and reported, or this statement should be removed.

Significance

This study provides high-quality measurements of apical cell geometry, actomyosin organization, and inferred tension in the mouse neural epithelium. However, the lack of direct perturbations, mechanical modeling, and quantitative analysis of three-dimensional tissue deformation limits the strength of the mechanistic conclusions. Addressing these gaps would substantially strengthen the manuscript and clarify the causal role of apical tension patterns in neural fold formation. At the end of the day, the authors suggest an hypothesis that is not well support by their data, which is of high quality.

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Referee #1

Evidence, reproducibility and clarity

Summary

Folding is a major morphogenetic process that shapes tissues and organs in three dimensions. The mechanisms underlying tissue folding have been extensively explored and are often driven by actomyosin-based apical constriction. Here, the authors describe changes in cell geometry and mechanics during mouse neural tube formation. They build on quantitative fixed imaging and live junction ablation to extract cell geometry and junctional tension. These analyses are performed at different developmental stages and in both male and female embryos to propose a mechanical mechanism for neural tube elevation in the brain.

Major comments

The authors report quantitative data on cell geometry and junctional tension inferred from laser ablation. Overall, there are numerous statements that require stronger support from the experimental data. To substantiate several of their claims, the authors need to provide a larger number of data points-or at least comparable numbers across experimental conditions-for the tension measurements. Additional statistical analyses are required throughout to support the conclusions.

Figure 1

• Does the projection algorithm account for tissue curvature when computing cell geometrical parameters such as area and anisotropy?
• The authors should provide information on the accuracy and reliability of the cell segmentation.

Figure 2

• The authors indicate that the rate of apical constriction differs between male and female embryos. However, apical sizes differ only at specific positions along the ML axis (Fig. 2H, I). The authors should provide statistical analyses for the rates shown in Fig. 2J. Are these rates significantly different between males and females, and between medial and lateral regions?
• Please clearly state the main novelty of this study relative to the work published by Brooks et al.

Figure 3

• The authors need to provide statistical support for the claim that large midline cells exhibit reduced F-actin and Myosin IIB levels.
• F-actin and Myosin IIB intensities should be plotted as a function of cell area to support the proposed anticorrelation between apical area and actomyosin levels.
• Statistical analyses are missing to substantiate the increase in F-actin levels between stages ss5 and ss8.
• Figure S3 should be supported by plots showing Myosin II and F-actin intensity as a function of position along the ML axis, together with appropriate statistics.

Figure 4

• The authors state that lateral tension in male embryos is not different from midline tension, yet the number of data points is much lower than in females. To support this claim, the number of ablations should be comparable across sexes. Is lateral tension different between males and females?
• Similarly, the data in Fig. S4 used to claim no change in tension over time are not supported by sufficient data points. Would the medial and lateral tensions reported in Fig. 4G remain unchanged if the authors perform statistical analyses on 10-15 ablations per condition?

Figure 5

• The number of data points in Fig. 5J and L is insufficient to support claims of no difference. The only detectable difference arises in the comparison with much higher sample size (Fig. 5L, ML vs RC). The authors conclude that males have higher ML tension than RC tension, but given the limited data this conclusion should be amended to "no detectable difference."

Code availability

The authors should provide access to the code used to generate the projections.

Significance

The authors propose a mechanical model for neural tube elevation based on analyses of cell geometry and tension at two developmental stages. The reported differences in cell geometry or actomyosin levels do not appear to explain the differences in geometry or tension suggested between male and female embryos. This raises questions about the relationship between these measurements and their relevance for understanding the mechanisms of neural tube elevation.

If the major concerns outlined above are rigorously addressed, the manuscript will offer a valuable descriptive characterization of neural tube cell geometry and mechanical stress during morphogenesis. Such datasets could form a foundation for future studies investigating the mechanisms driving neural tube elevation.

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Reply to the reviewers

Review Commons Refereed Preprint #RC-2022-01348

Response to Reviewers

Dear Editor,

Thank you for allowing us to submit a revised draft of the manuscript "Nrf2 promotes thyroid development and hormone synthesis" to Review Commons. We appreciate and are grateful for the time and effort you and the reviewers dedicated to providing feedback on our manuscript. The insightful comments were very valuable in improving the quality of our paper.

We apologize for the delay in submitting this revised version. Addressing the reviewers' insightful comments required substantial additional experimental work, including new in vivo analyses, chromatin accessibility profiling, and functional pathway interrogation. During the revision process, the PhD student who led this project completed her training and left the laboratory, requiring a reorganization of responsibilities and experimental efforts within the team to ensure rigorous completion of the requested studies. We appreciate your patience during this period and believe that the additional data have significantly strengthened the manuscript. In addition, a list of new data and experiments performed is shown below. Please see, in italics, the point-by-point response to the reviewers' comments and concerns. All figures, lines, and page numbers refer to the revised manuscript file.

List of experiments performed following the reviewers' comments:

• Tg staining in zebrafish wt and nrf2aΔ5 embryos - 6dpf (Supplementary Figure 4).
• Immunostaining for Phalloidin in mESC-derived organoids.
• ATAC sequencing for mESC-derived organoids (WT and Nrf2 KO; day 22).
• AP-1 pathway inhibition and gene/protein expression assessments __Reviewer #1 __

(Evidence, reproducibility and clarity (Required)):

This paper deals with the role of the transcription factor Nrf2 in the thyroid gland of zebrafish and in a thyroid organoid model. The subject if of relevance since Nrf2 is known to control the cellular response to oxidative stress and the thyroid is an organ where protection of oxidative stress is of major relevance, given the production of reactive oxygen species during thyroid hormone biosynthesis.

The main result is that in Zebrafish (ZF) thyroid Nrf2 appears to be important for thyroid hormone formation since late stages ZF embryos deprived of NRF2 the levels of the thyroid hormone T4 and of its precursor, iodinated thyroglobulin(Tg), are very much decreased. However, there is no significant decrease of Thyroglobulin mRNA, albeit an impairment in the up-regulation of Tg by TSH could be observed. No effect is seen on the structure of the thyroid follicles and no developmental defect is observed, in contrast with the title of the paper.

Conversely, in the mouse thyroid organoid model the absence of Nrf2 results in an impressive decrease of Tg mRNA and in impaired formation of thyroid follicles.

The study is in most part elegant and technically impeccable. The data are well presented and organised as far as figure is concerned. However, much remains to be done on the interpretation and presentation of results. In addition, the text that has been put together sloppily, with many typing and punctuation mistakes and difficult to interpret sentences. A revision of typing and syntax is absolutely needed.

1. • Dear reviewer, we appreciate your positive and constructive comments (addressed below) on our manuscript and we apologize for the text clarity and typos. The grammar and text structure were improved following the comments while additional experiments were performed aiming to answer the open questions.* Main concerns:

2. The title of the paper needs to be changed. There is no evidence that there is a problem with thyroid development in ZF. The thyroid appears to be enlarged at the end of development, most likely as a consequence of increased TSH stimulation, but there is no developmental defect!

3. • Dear reviewer, thank you for pointing it out. Indeed, the initial title did not represent the phenotype observed in both the Zebrafish and murine thyroid organoid models. So, in this revised version the title has been updated to reflect the effect of Nrf2/nrf2a on maturation rather than development. The new title is "The role of Nrf2/nrf2a in thyroid maturation and hormone synthesis in mammalian and non-mammalian models".*
4. There is an evident contradiction, in ZF, between the marginal, if any, decrease of Tg mRNA and the impressive decrease in T4 and iodinated Tg. This, in my opinion, very interesting discrepancy, is never discussed. Perhaps the authors should look at the level of Tg protein. It it possible that there is an increased degradation or some negative translational control in absence of Nrf2? Alternatively, is it possible that there is a defect, yet unidentified, in the organification process? Certainly, to conclude, as the authors do in page 11, lines 236-237, that the defect in hormonogenesis depends on thyroglobulin production is, with the data presented, an unproven statement.
5. • Dear reviewer, thank you for raising this question and suggesting experimental ways to tackle it. Following your comment, we performed Tg staining in zebrafish embryos. We could observe similar levels of Tg protein in nrf2a ko vs. nrf2a heterozygous and WT. Data have been added as Supplementary Figure 4 and the text has been updated (L. 175-179). This data ruled out our previous hypothesis that TH-impairment would happen in response to lower Tg levels. Since the phenotype observed in nrf2a KO is similar to the one previously demonstrated by our team with the duox KO (Giusti et al., 2020), we hypothesize that duox could be implicated in dyshormonogenesis. Since duox enzymes are known for tightly controlling H2O2 production, an essential factor for T.H. synthesis (Carvalho and Dupuy, 2017), duox dysregulation could further induce oxidative stress, and lead to hypothyroidism (L. 357-365). To access the duox expression in zebrafish we performed qPCR in pool of embryos and we did not observe any clear change in duox levels in nrf2a KO compared to WT (results included in Fig. 2S). Since duox is not exclusively expressed in the thyroid, we also performed in situ hybridization, however, we never managed to have convincing results using this technique. Finally, despite the observation that tpo and duox genes are expressed in nrf2a KO embryos, we cannot rule out that the activity of those enzymes is preserved and that the T.H. machinery is functional (L. 192-195). Due to the limitations of performing functional assays in zebrafish, the mechanism behind the dyshormonogenesis phenotype is an open question.*

6. *

7. The data on transcriptional effect of NRrf2 in the mouse ES cell system do not really add much. Their major effect is to contribute to a lengthy discussion that would really benefit of a substantial reduction.

8. • Dear reviewer, for this revised version of the manuscript we included new ATACseq data and combined it with the previously shown transcriptomic to explore the molecular mechanisms by which Nrf2 loss drives such maturation phenotype in mESC-derived thyroid organoids (L. 298-340; figure 6A-H). Using such approach we demonstrate that Nrf2 causes significant changes in chromatin accessibility which is strongly correlated with changes in gene expression profile. We also could demonstrate that Tg expression is indeed impaired by a reduction in chromatin accessibility under the lack of Nrf2, while we identified key pathways/TFs regulated by Nrf2 that could play a role in driving the phenotype. More specifically we identified increased mRNA expression and chromatin accessibility of genes associated with AP-1 pathway activation, such as Fos, Jun-b, and Stats (L. 322-334; Figure 6 and Supplementary Figure 6). * Interestingly, studies have shown that Nrf2 and AP-1-proteins significantly overlap regulating each other at several levels, including transcriptionally. Also, despite Nrf2 being known for binding to ARE and AP-1 to TRE site, they often overlap with AP-1 being embedded into ARE. These tight relations suggest shared feed-forward and feed-back circuits between NRF2 and AP-1 factors contributing to their functioning. To further investigate if AP-1 overexpression in Nrf2 KO-derived thyroid organoids has a compensatory effect or if it contributes to the phenotype observed, we performed AP-1 inhibition during the thyroid differentiation protocol. Nrf2 KO cells differentiated with the SR11302 inhibitor (from day 7 to 22) partially reduced the Tg mRNA at higher doses (10m*M) while Tg protein and Tg-I production are not clearly distinct from the control (L. 334-340; Supplementary Figure 7A-B). This suggests that AP-1 upregulation upon loss of Nrf2 might work as a compensatory mechanism, however, due to the lack of Tg expression, which is under a direct effect of Nrf2, the functionality is not recovered. *

9. *

10. More time should be devoted to explain the substantial differences between the three systems studied (two in this paper, one in a previous published by partly same authors), keeping in mind that studies in mice could be largely influenced by the genetic background.

11. Following the suggestion of the reviewer, we added a table (Table 7) summarizing the differences and similarities between the two models used in this study and the in vivo model from Ziros, et al. 2018. We also better discussed the 3 models in the discussion and added subtitles to make it clearer.*

Reviewer #1 (Significance (Required)):

This paper is largely confirmatory of previous results obtained in a mouse Nrf2 KO model, whose main authors are also part of this study (Ziros et al., 2018). A clarification of the molecular defect in hormone production in ZF could add the novelty that this study might need.

1. • Dear reviewer, indeed our study reinforces the effect of Nrf2 in regulating of Tg expression in mice (not conserved in zebrafish). In addition, we demonstrate the transcriptional and chromatin accessibility changes promoted by the loss of Nrf2 in mouse thyroid cells. Also, the fact that Nrf2 KO ES cells do not efficiently form follicles in vitro is a very interesting and unexpected observation that reinforces the hypothesis that Tg secretion plays a role during early folliculogenesis. In zebrafish, despite the normal expression of the main thyroid markers, the defect in function could be explained by disruptions in duox and tpo activity which would impair Tg iodination. Unfortunately, the limitation of zebrafish for functional studies keeps this question open. * Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary

In this manuscript Gillotay et al investigate and further establish a role for Nrf2 in thyroid physiology. Importantly, a role of Nrf2 in thyroid development is investigated in the Tg(tg:nlsEGFP) zebrafish model system developed by this group. This permits detailed and also live tracking of zebrafish thyroid development. By a Crispr/Cas9 approach the authors establish a functional role for nrf2a in zebrafish thyroid development. Nrf2a loss-of-function in zebrafish leads to a hypothyroid phenotype that seems to recapitulate aspects of dyshormonogenesis with a slightly enlarged gland, increased tshb, strongly reduced T4 and iodinated TG (TG-I). Morover, Tg synthesis is perturbed, only slightly during control conditions but pronouncedly during PTU challenge. By restoring nrf2a specifically in the zebrafish thyroid, the authors prove the phenotype to be cell autonomous to the thyroid.

The authors then turn to the model system of functional thyroid follicular maturation from mESC that they have previously described. In this system Nrf2a KO leads to loss of TG expression and what the authors describe as an inability to form follicular units. Even though Nis is expressed, iodine organification is impaired, likely due to defective Tg production.

Evidence, reproducibility and clarity

Major comments

This is a nicely written manuscript with mostly convincing results. The authors demonstrate laudable scientific rigor by verifying that the genetic modifications indeed have the expected effect (that nrf2 in the model systems that they create is indeed non-functional) and by using a rescue strain for the zebrafish model. In my opinion the data and the methods are presented in such a way that they can be reproduced. Generally, the conclusions are well supported by the results presented.

The authors make a rather strong point of Nrf2 thyroid function as an evolutionary conserved mechanism and this might need some further underpinning.

1. • Dear reviewer, we appreciate your positive comments on our manuscript. Concerning the evolutionary conserved mechanisms driven by Nrf2, we better discuss this aspect in this new version. Even if the lack of nrf2/nrf2a drives the same phenotypical outcome in both models, we discuss the possible distinct mechanisms by which it drives such phenotype. While in mESC-derived thyroid organoids, we confirm the repressive effect of Nrf2 loss on Tg expression and consequently on folliculogenesis and TH production, in zebrafish our new data suggest another mechanism. As suggested by reviewer 1, Tg staining was performed under "physiological" conditions and we did not observe any change in Tg protein in nrf2 KO compared to WT embryos (Supplementary Figure 4). This ruled out the hypothesis of a conserved mechanism involving tg expression. However, as discussed in the new version, this phenotype could be related to dysfunctions in the activity of enzymes associated with tg iodinations, like tpo and duox. However, due to the challenges in performing functional and activity studies in zebrafish, this hypothesis could not be validated.* Line 368. The authors state that their findings "...reinforce a recently published report on the role of Nrf2 in adult mouse thyroid physiology (Ziros et al., 2018)" and continue: "Although we did not analysed (sic!) the thyroid gland of adult nrf2a KO zebrafish"...".

Why were not adult zebrafish investigated? As some key results of Ziros et al on adult Nrf2 KO mice differ from those of the manuscript (e.g. TG iodination under non stressed conditions seems to be increased in mice but decreased in zebrafish) it would be highly desirable to know if the zebrafish phenotype is more similar to that of mice in later adulthood.

1. • Dear reviewer, indeed assessing TH status in adult zebrafish would tell us if there is a later compensatory effect occurring, what might be the case in mice. However, despite our will to test it in adults, we faced several challenges: a. A big proportion of the nrf2a homozygous embryos die around 10dpf, which could be a consequence of the absence of THs. b. The few adults that managed to survive have shown much lower ability to produce eggs (20 eggs instead of hundreds), a reduction in fertility. Considering that the complete lack of TH would be detrimental to survival, we could expect that the minority of nrf2a KO embryos able to reach adulthood are the selected ones producing a sufficient amount of T4 to keep them alive. c. Thyroid tissue analysis in adult zebrafish is technically similar to mice, where the tissue dissection and processing is quite challenging since the thyroid is very small and difficult to dissect. Taking into account these limiting aspects, unfortunately, we were not able to provide the TH production assessment for this manuscript. * As I will elaborate on later on, to me a key finding seems to be that nrf2a might have unexpected "non-canonical functions" that do not immediately seem to pertain to its presumed major function as a key regulator of defense to oxidative stress. One of these is to be an impact on Tg production. The other one seems to be a possible role in folliculogenesis, even though this might in some way be related to the impact on Tg production. I do understand that the authors want to leverage from the elegant in vitro model of mESC-derived follicles that they have developed. However, the rationale of using the model system in this context is not entirely clear to me. In Ziros et al the effect of Nrf2 deficiency was studied in a murine global knockout model, in a thyroid specific knockout (even though it might be argued that by using a Pax8 Cre-driver Nrf2 was likely knocked out also in the kidneys and in some regions of the CNS) as well as in cultured rat thyroid cells. Is it the fact that the Pax8 Cre-driver is not entirely thyroid specific that prompted the authors to turn to the mESC-model, the possibility of studying thyroid cell autonomous mechanisms of folliculogenesis (without the possible impact of other tissues and the HPT-axis) by turning to this reductionistic model or other considerations? Even though the results from the mESC model certainly are of interest, the rationale needs to be better explained and the real potential of this model is perhaps not fully exploited. Specifically, the effect on folliculogenesis in the mESC system needs to be more carefully presented:
2. • Dear reviewer, indeed, the rationale behind the choice of using mESC-derived thyroid organoids to study Nrf2 loss was not clearly presented in the first version of our manuscript. The text has been modified in the updated version to better explain our choice of using the mESC-derived thyroid model. In fact, the first goal of using this system was to be able to compare the effect of Nrf2 KO during thyroid development in a mammalian system. Compared to in vivo mouse models, assessing/tracking changes (mRNA expression and live imaging) during early development is challenging due to the need for many animals to study each stage of development. In addition, we aimed to use the derived cells to perform omics and understand the mechanisms behind the phenotype. These experiments would be challenging to perform in zebrafish due to the small number of thyroid cells at 6dpf and the number of cells necessary for RNA and ATAC sequencing. Such assessments were also not performed in the Ziros, 2018 previous study. * To us, in Ziros, 2018 paper, the fact that Pax8 is expressed in the kidney was not a main drawback. In our system, the folliculogenesis phenotype was also not expected, and it is highlighted as an unexpected and novel finding during development, rather than as the rationale for this work. Our new Fig. 5B shows that even if less frequently, smaller follicles are formed. Taking this into account, we cannot exclude that this phenotype could be transitory during early stages of development and that upon Tg accumulation overtime, follicles could be formed and Tg iodinated since the iodine machinery is highly preserved. This hypothesis would fit with the findings from Ziros (2018) that show thyroid follicular organization and function in adult mice lacking Nrf2 expression. Another possible explanation is that during thyroid in vitro differentiation a higher level of stress is expected compared to an in vivo system and in the case of Nrf2 lack it would exacerbate the effect, as previously demonstrated in vivo by the overload of iodine in adult mice (Ziros, 2018).

Line 294. Even though they might be discernible, it is difficult to really appreciate the occurrence of follicular lumina in Fig 4E WT structures. The authors consider this as a main finding (see discussion: "The most striking difference we observed between the two models was the absence of follicular organisation in Nrf2 KO thyroid cells..."). I think this would be clearer if staining for an apical marker such as ezrin or MUC1 are shown and I would also like to see some kind of quantification of follicular organization (e.g. number per area, size) between the WT and KO conditions. I think that would strengthen the notion of abolished follicular organization in Nrf2 KO cells.

1. • Dear reviewer, following your comment we performed phalloidin staining to get a better view of the follicular organization in Nrf2 WT and KO-derived thyroid organoids (Fig. 5B). Also, using this staining we could observe that visually fewer and smaller follicle-like structures are formed upon Nrf2 absence. This could indicate that folliculogenesis is not completely abrogated but not fully and properly occurring in this case, mostly likely due to the low accumulation of Tg in the lumen. This reinforces the hypothesis that in mice, overtime accumulation of Tg, even if less produced, could compensate for the folliculogenesis phenotype and finally produce functional follicles (as in Ziros's paper).* Fig 5A. Also in this image it is difficult to appreciate any genuine "follicular organization" of the WT cells. Again, staining for an apical marker would be desirable. It rather seems like microlumina between two or three cells. Also a close up might be illustrative.
2. • Dear reviewer, to show more clearly the follicular organization, phalloidin staining has been added to Fig. 5 (B).* In my opinion, these suggestions seem realistic in terms of time and resources, as this group has established, have access to and are proficient in using both the zebrafish lines as well as the mESC differentiation protocol towards follicular thyroid units.

It is difficult to tell if and how mechanistic insights into the role of Nrf2 in folliculogenesis in the mESC system might be obtained. That might require opening up new lines of experimentation (that I certainly do not require), but I leave it to the authors to judge if some realistic and feasible additional experiments would possibly contribute to more mechanistically oriented understanding. It would be nice to see the authors leverage even more from their beautiful mESC model of thyroid folliculogenesis and I believe that this model might indeed provide important mechanistic insight into this issue.

1. • Dear reviewer, we fully agree that the unexpected role of Nrf2 in folliculogenesis is something to be better explored in our organoid system. Even though, we are not sure if there is a direct effect of this TF in regulating this process or if it is just a consequence of Tg downregulation. As a future perspective, we aim to keep the Nrf2 KO organoids in culture for longer periods (to be established) and assess if the overtime accumulation of Tg is enough to form bigger and functional follicles.* It is known from previous literature that Tg production is diminished in nrf2 KO mice and that AREs are present in murine Tg enhancer regions (Ziros et al 2018). In the current manuscript the authors do not identify such elements in the vicinity of the zebrafish tg gene. To me, this comparison of AREs in enhancer elements is an important observation that might explain some of the differences to results in Ziros et al and warrants to be included in the results section with a figure, and not only mentioned in the discussion section by referring to a supplementary figure.
2. • Dear reviewer, this aspect was further discussed in the text and the comparison figure was added as part of a main figure (Fig. 6C). In addition, in this updated version we also included new ATAC sequencing data (L. 298-340; Fig. 6) that reinforces the results previously shown by Ziros (2018) in which Nrf2 regulates Tg by binding to the ARE sites in its promoter. * It would be desirable if the authors elaborate a bit more and clearly on how they envision nrf2a impacts on Tg production in the zebrafish.
3. • Dear reviewer, as suggested by reviewer 1, we performed immunostaining to evaluate the levels of Tg protein and we did not observe any difference in protein among nrf2a KO and WT embryos (Supplementary Fig. 4). This together with the lack of ARE sites at zebrafish Tg promoted ruled out an effect of nrf2 on its expression in zebrafish under physiological conditions.* In Fig 2L it seems like T4 expression is completely lacking in KO embryos, whereas Fig 2R suggests that a signal that can be quantified is indeed present. Moreover, in Fig 3J a T4 signal, albeit reduced, is seen. Is Fig 2L really representative?
4. • Dear reviewer, the displayed pictures are representative of the main phenotype obtained (majority of the embryos). Fluorescent quantification was done using Leica software (described below). The software quantifies the fluorescence based on grayscale images which means that fluorescence slightly higher than the background, thus barely visible, will be quantified which can lead to a value different than zero despite no "visible" staining. This reflects the apparent discordance between the Figures 2L and 2R. Concerning Fig 3J, this is an example that a few nrf2a KO embryos can produce T4 though in lower levels than WT. This range of phenotypes is now highlighted within the text and is reflected in the Fig. 2R and 3Q quantification data.* In Fig 3Q the decrease of T4 signal seems much less pronounced than in Fig. 2R, even though it seems like the comparisons are between the same genotypes. Can the authors comment on this?
5. • Dear reviewer, Fig. 2R represents embryos from F2 while Fig. 3Q are from F3 and both were performed independently. Despite the possible differences between the generations, other technical factors could be involved such as: sample fixation, staining duration of antibody, post-processing of the samples, etc. Although we tried to perform both experiments as similarly as possible, we can not rule out small differences between both experiments.* Fig 6B. What do the two columns in WT and KO represent? Has the experiment been conducted on only two biological replicates?
6. • Dear reviewer, indeed, the experiments, bulk RNA and ATAC sequencing, we performed using two biological replicates. For each replicated, we pooled together at least 4 organoid wells that were not previously selected, aiming to represent a possible variability in differentiation.* Minor comments

Fig 2S - Do the bars of this graph show the ratio of expression in KO vs WT? What is the black bar furthest to the left (labelled "WT") that seems to be some kind of normalizer? Which transcript does it represent? The same question goes also for 2T-V and 4B and C.

1. • Dear reviewer, we apologize for the lack of clarity. All data displays the fold change compared to their respective control (WT). The black bar shows the control (WT=1) for each gene on the figure panel. A dashed line has been added to better visualize the differences in gene expression levels respective to the control. Figure legends have been updated for clarity. * Fig 2U - In the results section it it stated that "Upon PTU treatment, tsh-β and slc5a5a expression were increased in both WT and nrf2aΔ5 186 homozygous mutants...". In the figure it seems like there is no significant change of slc5a5 in PTU treated homozygous mutants.
2. • Dear reviewer, we apologize for the mistake, the sentence was corrected accordingly.* Line 52. "...the thyroid enables the production of growth hormones...". This is not clear to me. To the authors mean GH or do they more loosely refer to T3/T4 as "growth hormones"?
3. • Dear reviewer, we agree with the comment and modified the sentence accordingly to precise that the action of the thyroid on growth hormone production is mediated by the thyroid hormones.* Line 60. "... If left untreated, C.H. will cause severe mental and growth retardation in patient among other physiological consequences...". I would consider these consequences as "pathological" rather than "physiological".
4. • Dear reviewer, indeed, using pathological is more appropriate, the sentence has been updated.* Line 151 A.U - if the units are arbitrary, why use such a cumbersome order of magnitude where the numbers are in the order of 10e5 and 10e6?
5. • Dear reviewer, we are performing the fluorescence quantification using the quantification module of the "Leica, LAS X" software. Briefly, we delimitate region of interest for which the software will give us the value of fluorescence for each pixel with this region of interest. Although we are correcting the value of each of these pixels in the region of interest by the average fluorescent value of the pixels in the background area, the amount of pixels in each region is bringing the value to this extent. We decided to keep the raw fluorescence values to better express the differences in magnitude among the groups.* Line 246. "Based on these results, we hypothesized that adult Nrf2 KO mice might develop body-wide resistance to the effects of Nrf2 defficiency (sic!) which in turn, might reduce the visible effects on thyroid development and physiology". The concept of a putative "body-wide resistance" is a bit nebulous to me. It would be great if the authors could be a bit more precise, or at least speculate on, the putative mechanisms of such a "body-wide resistance".
6. • Dear reviewer, indeed this is a speculation and we have removed this statement to improve the clarity of the manuscript. In addition, we included in the updated text a hypothesis that the overtime accumulation of Tg from early development (as seen in our in vitro system) to adulthood could lead to the proper formation of thyroid follicles and consequently T.H. synthesis. Even if not included in this manuscript, we plan to improve our in vitro model for long-term culture to assess this hypothesis.* Line 297. It is very difficult to appreciate from these images that "the percentage of Nkx2-1 cells was higher compared with the control cell line". In WT it seems that all nuclei are positive for Nkx2-1 but rather that the expression level is lower than in the KO cell line. I would like the authors to elaborate on this. Is really the percentage of "Nkx2-1 cells" (I think the authors mean Nkx2-1 positive cells) lower in WT than in the KO or it is rather a matter of staining intensities?

7. Dear reviewer, we apologize for the lack of clarity. Rather than referring to the IF images at Fig. 4E we refer to a higher percentage of Nkx2.1+ cells in Nrf2 KO organoids when using Flow cytometry quantification (Fig. 4D). The flow cytometer graphs show the gating for Nkx2.1-stained cells and highlight that upon the absence of Nrf2 65.3% of the cells are Nkx2.1+ compared to 27.1% in the WT controls. We updated the text to avoid misunderstandings and immunostainings are mainly used to show visually the cell organization and protein expression rather than with quantitative purposes.*

Line 309. Is it really a "lower portion of cells" that are "able to promote ioidide organification"? Do the authors consider some KO cells to be organification competent whereas other cells not? Is it not rather a globally diminished ability to organify iodine?

1. • Dear reviewer, we consider that the lower ability of Nrf2 KO cells to produce Tg and consequently self-organize into follicles is the primary cause of the global reduction in iodine organification. Even though, iodine uptake is not impaired, a lower amount of cells can produce Tg-I, thus displaying the ability to organify iodine. Very likely this is limited by the number of Tg-expressing cells and/or the amount of Tg in each cell derived from Nrf2 KO mESCs.* Line 316. "...KO derived thyroid follicles". This seems contradictory to the previous notion that KO cells do not form follicles. I suggest that "follicles" is replaced by "thyrocytes" if follicular structures are indeed completely lacking. However, the phrasing "KO derived thyroid follicles" suggest that such are indeed present and might be possible to quantify as suggested above.
2. • Dear reviewer, thank you for pointing it out. Indeed, the term nrf2 KO-derived thyroid follicles is not appropriate and has been changed in the text. Also, since our Phalloidin staining shows that we have small follicles formed we updated our data description and discussion for the fact that follicles seem to form, however a clear delay in size is observed among Nrf2 KO organoids. This is very likely linked to a lower expression of Tg in those organoids.* Line 327 "...among NRF2 WT cells, we detected upregulation...". What do the authors mean by "upregulation" in the context of WT cells? As compared to what? If "upregulated" means as compared to KO cell that does not seem completely appropriate. Even though this might seem like semantics, it is not intuitive to me to describe something as "upregulated" in WT cells, that would rather constitute a baseline condition. Would it rather not be considered as a "downregulation" in KO cells?
3. • Dear reviewer, the statement was indeed not appropriate and we modified the text accordingly.* Line 337. "... important downregulation" seems a little unorthodox to write in a results section. The downregulation might be significant or not. If it is important or not is a different matter (of subjective biological interpretation, i.e. how biological meaning is appreciated) and more suited to be put into context in the discussion section.
4. • Dear reviewer, following your comments, transcriptomic results and discussion have been updated for clarity. A more factual description has been kept in the result section while the interpretation was moved down to the discussion.* There are scattered typos and grammatical errors that make reading less pleasant and need to be corrected, preferably by a native English speaker.
5. • Dear reviewer, we apologize for the text clarity and typos. The grammar and text structure were improved following the comments.* Reviewer #2 (Significance (Required)):

Significance

This is to the best of my knowledge the first study of a putative role for Nrf2 in thyroid development. However, a role of Nrf2 in thyroid physiology and pathology has previously been rather firmly established.

Even though the manuscript is a very nice piece of work, it is perhaps difficult to claim that it in its present form signifies a major conceptual advance of the field, as it provides only limited mechanistic insight, especially with respect to possible "non-canonical" functions of nrf2 (mechanisms of impact on Tg production and folliculogenesis). If such insights could be obtained it would clearly increase the significance of this contribution.

1. • Dear reviewer, for this revised version of the manuscript we included a new set of ATACseq data and combined it with the previously shown transcriptomic to further explore the molecular mechanisms by which Nrf2 loss drives such maturation phenotype in developing mESC-derived thyroid organoids (L. 304-340; figure 6A-H). Using such an approach we demonstrate that Nrf2 causes significant changes in chromatin accessibility which is strongly correlated with changes in gene expression profile. We also could demonstrate that Tg expression is indeed impaired by a reduction in chromatin accessibility under the lack of Nrf2, while we identified key pathways/TFs regulated by Nrf2 that could play a role in driving the phenotype or as compensatory mechanisms. More specifically we identified increased mRNA expression and chromatin accessibility of genes associated with AP-1 pathway activation, such as Fos, Jun-b, and Stats (L. 298-333; Figure 6 and Supplementary Figure 6). * Interestingly, studies have shown that Nrf2 and AP-1-proteins significantly overlap regulating each other at several levels, including transcriptionally. Also, despite Nrf2 being known for binding to ARE and AP-1 to the TRE sites, they often overlap with AP-1 being embedded into ARE. These tight relations suggest shared feed-forward and feed-back circuits between NRF2 and AP-1 factors contributing to their functioning. To further investigate if AP-1 overexpression in Nrf2 KO-derived thyroid organoids has a compensatory effect or if it contributes to the phenotype observed, we performed AP-1 inhibition during the thyroid differentiation protocol. Nrf2 KO cells differentiated with the SR11302 inhibitor (from day 7 to 22) partially reduced the Tg mRNA at higher doses (10m*M) while Tg protein and Tg-I production are not visually different from the control (L. 334-340; Supplementary Figure 7A-B). This sugge that AP-1 upregulation upon loss of Nrf2 might work as a compensatory mechanism, however, due to the lack of Tg expression, which is under a direct effect of Nrf2, the functionality is not recovered. *

The main strength of the study is that it investigates Nrf2 function in the context of embryonic development.

Even though the manuscript makes a point of evolutionary conserved mechanisms, I do not really see that that the discrepancies to results obtained from in vivo studies in higher vertebrates are sufficiently discussed and elaborated on.

1. • Dear reviewer, following your and reviewer 1 suggestions we have updated our discussion to better highlight the similarities and differences between both models while comparing our mouse in vitro model to the in vivo model previously published.* Line 240. It feels a bit presumptuous to comment on the contents of an excellent paper that one of the authors of the current manuscript is the senior author of (Ziros et al 2018) and of course knows much better than I do.

However, the present manuscript states (about Ziros et al 2018) that "In this study, the authors described how loss of Nrf2 function causes a thyroid phenotype only under stress conditions such as iodine overload. However, in the same study, the authors described that the loss of Nrf2 function causes a reduction of the thyroglobulin expression in PCCL3 rat thyroid follicular cell culture". In my recollection of Ziros et al there is a thyroid phenotype in KO mice not only under stress conditions, but also under normal conditions with reduced TG and increased TG-I? I would like the authors to comment on this.

1. • Dear reviewer, indeed, in Ziros' (2018) paper it is shown that lack of Nrf2 does not cause hypothyroidism in physiological conditions, however, Tg expression is reduced (regulation mechanisms were also shown) but the Tg-I/Tg iodination rate was increased. Only under iodine overload, they could see an inhibitory effect on thyroid hormone production. We were not clear in our statement in the previous version which is now improved in the revised version. In addition, we also better discuss our findings in organoids and raise the hypothesis that long-term Tg accumulation could "restore" folliculogenesis and thyroid hormone synthesis. * The authors seem to emphasize the aspect of evolutionary conservation. However, even though I consider the possible effect on folliculogenesis in the mESC model as a very interesting finding, it is difficult to understsand if it is a phenomenon that is specific to the mESC model system or of more general importance. As the authors demonstrate, follicles indeed seem to develop in nrf2a deficient zebrafish. In Ziros et al 2018 no images of thyroid morphology are provided, but as KO mice are euthyroid it seems likely that follicular organization is not grossly perturbed. The authors need to elaborate on this. Even if the effect might be more or less specific to the mESC system, that does not necessarily make it less relevant. It might provide fundamental insights into the process of folliculogenesis, but for greater significance more mechanistic insight would be desirable.
2. • Dear reviewer, as mentioned above, we used new tools to better analyze the "folliculogenesis impairment" previously suggested to be occurring in our organoid system. A careful assessment of the morphology of our Nrf2 KO-derived organoids using Phalloidin (Fig. 5B) staining evidenced that in fact folliculogenesis process might be undergoing in our organoids, however, the follicular-like structures are less frequently observed (difficult to quantify due to the 3D aspect of the follicular organization) while the size seems to be smaller than in WT organoids. Here we believe that due to the lower levels of Tg expressed and secreted into the lumen the size is smaller. This proposed hypothesis fits with the previous studies suggesting that Tg has a role in folliculogenesis. In addition, we cannot rule out that in vivo this same phenotype happens during early development and that overtime accumulation of Tg could lead to proper follicular formation and consequently to normal thyroid function. Interestingly, Ziros' paper shows that even in Tg downregulation conditions, T.H. production is not impaired, with a higher ratio of iodinated Tg compared to WT mice, suggesting a compensatory mechanism to overcome the lower levels of Tg. This new aspect is now further discussed in the manuscript. *

**Referees cross-commenting**

I largely agree with the comments of referee #1, particularly the comment that the title (and some of the discussion) of the paper needs to be changed as pointed out by referee #1 ("...there is no evidence that there is a problem with thyroid development in ZF. The thyroid appears to be enlarged at the end of development, most likely as a consequence of increased TSH stimulation, but there is no developmental defect!").

1. • Dear reviewer, following both reviewer's suggestions, we modified the title of the paper to better reflect the results presented. The new title is "The role of Nrf2/nrf2a in thyroid maturation and hormone synthesis in mammalian and non-mammalian models". * In humans, developmental defects such as congenital hypothyroidism can be divided into two main categories: 1. Dyshormonogenesis, when the tissue is properly developed but thyroid function is impaired and 2. Dysgenesis, when the tissue (organogenesis is impaired) is not properly formed or not at all, resulting in hypothyroidism. The phenotype observed in nrf2a KO zebrafish corresponds to the dishormonogenesis in humans and despite that folliculogenesis seems to be preserved, the bigger size of the thyroid is not considered as a defect in organogenesis but a consequence of higher TSH stimulation. Still, it would be classified as a developmental defect. However, to avoid misinterpretation, we updated the text and highlighted that in zebrafish the lack of nrf2a results in hyperplastic non-functional thyroid tissue.

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Referee #3

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Referee #2

Evidence, reproducibility and clarity

Summary

In this manuscript Gillotay et al investigate and further establish a role for Nrf2 in thyroid physiology. Importantly, a role of Nrf2 in thyroid development is investigated in the Tg(tg:nlsEGFP) zebrafish model system developed by this group. This permits detailed and also live tracking of zebrafish thyroid development. By a Crispr/Cas9 approach the authors establish a functional role for nrf2a in zebrafish thyroid development. Nrf2a loss-of-function in zebrafish leads to a hypothyroid phenotype that seems to recapitulate aspects of dyshormonogenesis with a slightly enlarged gland, increased tshb, strongly reduced T4 and iodinated TG (TG-I). Morover, Tg synthesis is perturbed, only slightly during control conditions but pronouncedly during PTU challenge. By restoring nrf2a specifically in the zebrafish thyroid, the authors prove the phenotype to be cell autonomous to the thyroid. The authors then turn to the model system of functional thyroid follicular maturation from mESC that they have previously described. In this system Nrf2a KO leads to loss of TG expression and what the authors describe as an inability to form follicular units. Even though Nis is expressed, iodine organification is impaired, likely due to defective Tg production.

Major comments

This is a nicely written manuscript with mostly convincing results. The authors demonstrate laudable scientific rigor by verifying that the genetic modifications indeed have the expected effect (that nrf2 in the model systems that they create is indeed non-functional) and by using a rescue strain for the zebrafish model. In my opinion the data and the methods are presented in such a way that they can be reproduced. Generally, the conclusions are well supported by the results presented.

The authors make a rather strong point of Nrf2 thyroid function as an evolutionary conserved mechanism and this might need some further underpinning.

Line 368. The authors state that their findings "...reinforce a recently published report on the role of Nrf2 in adult mouse thyroid physiology (Ziros et al., 2018)" and continue: "Although we did not analysed (sic!) the thyroid gland of adult nrf2a KO zebrafish"...". Why were not adult zebrafish investigated? As some key results of Ziros et al on adult Nrf2 KO mice differ from those of the manuscript (e.g. TG iodination under non stressed conditions seems to be increased in mice but decreased in zebrafish) it would be highly desirable to know if the zebrafish phenotype is more similar to that of mice in later adulthood.

As I will elaborate on later on, to me a key finding seems to be that nrf2a might have unexpected "non-canonical functions" that do not immediately seem to pertain to its presumed major function as a key regulator of defense to oxidative stress. One of these is to be an impact on Tg production. The other one seems to be a possible role in folliculogenesis, even though this might in some way be related to the impact on Tg production. I do understand that the authors want to leverage from the elegant in vitro model of mESC-derived follicles that they have developed. However, the rationale of using the model system in this context is not entirely clear to me. In Ziros et al the effect of Nrf2 deficiency was studied in a murine global knockout model, in a thyroid specific knockout (even though it might be argued that by using a Pax8 Cre-driver Nrf2 was likely knocked out also in the kidneys and in some regions of the CNS) as well as in cultured rat thyroid cells. Is it the fact that the Pax8 Cre-driver is not entirely thyroid specific that prompted the authors to turn to the mESC-model, the possibility of studying thyroid cell autonomous mechanisms of folliculogenesis (without the possible impact of other tissues and the HPT-axis) by turning to this reductionistic model or other considerations? Even though the results from the mESC model certainly are of interest, the rationale needs to be better explained and the real potential of this model is perhaps not fully exploited. Specifically, the effect on folliculogenesis in the mESC system needs to be more carefully presented:

Line 294. Even though they might be discernible, it is difficult to really appreciate the occurrence of follicular lumina in Fig 4E WT structures. The authors consider this as a main finding (see discussion: "The most striking difference we observed between the two models was the absence of follicular organisation in Nrf2 KO thyroid cells..."). I think this would be clearer if staining for an apical marker such as ezrin or MUC1 are shown and I would also like to see some kind of quantification of follicular organization (e.g. number per area, size) between the WT and KO conditions. I think that would strengthen the notion of abolished follicular organization in Nrf2 KO cells.

Fig 5A. Also in this image it is difficult to appreciate any genuine "follicular organization" of the WT cells. Again, staining for an apical marker would be desirable. It rather seems like microlumina between two or three cells. Also a close up might be illustrative.

In my opinion, these suggestions seem realistic in terms of time and resources, as this group has established, have access to and are proficient in using both the zebrafish lines as well as the mESC differentiation protocol towards follicular thyroid units. It is difficult to tell if and how mechanistic insights into the role of Nrf2 in folliculogenesis in the mESC system might be obtained. That might require opening up new lines of experimentation (that I certainly do not require), but I leave it to the authors to judge if some realistic and feasible additional experiments would possibly contribute to more mechanistically oriented understanding. It would be nice to see the authors leverage even more from their beautiful mESC model of thyroid folliculogenesis and I believe that this model might indeed provide important mechanistic insight into this issue.

It is known from previous literature that Tg production is diminished in nrf2 KO mice and that AREs are present in murine Tg enhancer regions (Ziros et al 2018). In the current manuscript the authors do not identify such elements in the vicinity of the zebrafish tg gene. To me, this comparison of AREs in enhancer elements is an important observation that might explain some of the differences to results in Ziros et al and warrants to be included in the results section with a figure, and not only mentioned in the discussion section by referring to a supplementary figure. It would be desirable if the authors elaborate a bit more and clearly on how they envision nrf2a impacts on Tg production in the zebrafish.

In Fig 2L it seems like T4 expression is completely lacking in KO embryos, whereas Fig 2R suggests that a signal that can be quantified is indeed present. Moreover, in Fig 3J a T4 signal, albeit reduced, is seen. Is Fig 2L really representative?

In Fig 3Q the decrease of T4 signal seems much less pronounced than in Fig. 2R, even though it seems like the comparisons are between the same genotypes. Can the authors comment on this?

Fig 6B. What do the two columns in WT and KO represent? Has the experiment been conducted on only two biological replicates?

Minor comments

Fig 2S - Do the bars of this graph show the ratio of expression in KO vs WT? What is the black bar furthest to the left (labelled "WT") that seems to be some kind of normalizer? Which transcript does it represent? The same question goes also for 2T-V and 4B and C.

Fig 2U - In the results section it it stated that "Upon PTU treatment, tsh-β and slc5a5a expression were increased in both WT and nrf2aΔ5 186 homozygous mutants...". In the figure it seems like there is no significant change of slc5a5 in PTU treated homozygous mutants.

Line 52. "...the thyroid enables the production of growth hormones...". This is not clear to me. To the authors mean GH or do they more loosely refer to T3/T4 as "growth hormones"?

Line 60. "... If left untreated, C.H. will cause severe mental and growth retardation in patient among other physiological consequences...". I would consider these consequences as "pathological" rather than "physiological".

Line 151 A.U - if the units are arbitrary, why use such a cumbersome order of magnitude where the numbers are in the order of 10e5 and 10e6?

Line 246. "Based on these results, we hypothesized that adult Nrf2 KO mice might develop body-wide resistance to the effects of Nrf2 defficiency (sic!) which in turn, might reduce the visible effects on thyroid development and physiology". The concept of a putative "body-wide resistance" is a bit nebulous to me. It would be great if the authors could be a bit more precise, or at least speculate on, the putative mechanisms of such a "body-wide resistance".

Line 297. It is very difficult to appreciate from these images that "the percentage of Nkx2-1 cells was higher compared with the control cell line". In WT it seems that all nuclei are positive for Nkx2-1 but rather that the expression level is lower than in the KO cell line. I would like the authors to elaborate on this. Is really the percentage of "Nkx2-1 cells" (I think the authors mean Nkx2-1 positive cells) lower in WT than in the KO or it is rather a matter of staining intensities?

Line 309. Is it really a "lower portion of cells" that are "able to promote ioidide organification"? Do the authors consider some KO cells to be organification competent whereas other cells not? Is it not rather a globally diminished ability to organify ioidie?

Line 316. "...KO derived thyroid follicles". This seems contradictory to the previous notion that KO cells do not form follicles. I suggest that "follicles" is replaced by "thyrocytes" if follicular structures are indeed completely lacking. However, the phrasing "KO derived thyroid follicles" suggest that such are indeed present and might be possible to quantify as suggested above.

Line 327 "...among NRF2 WT cells, we detected upregulation...". What do the authors mean by "upregulation" in the context of WT cells? As compared to what? If "upregulated" means as compared to KO cell that does not seem completely appropriate. Even though this might seem like semantics, it is not intuitive to me to describe something as "upregulated" in WT cells, that would rather constitute a baseline condition. Would it rather not be considered as a "downregulation" in KO cells?

Line 337. "... important downregulation" seems a little unorthodox to write in a results section. The downregulation might be significant or not. If it is important or not is a different matter (of subjective biological interpretation, i.e. how biological meaning is appreciated) and more suited to be put into context in the discussion section.

There are scattered typos and grammatical errors that make reading less pleasant and need to be corrected, preferably by a native English speaker.

Significance

This is to the best of my knowledge the first study of a putative role for Nrf2 in thyroid development. However, a role of Nrf2 in thyroid physiology and pathology has previously been rather firmly established. Even though the manuscript is a very nice piece of work, it is perhaps difficult to claim that it in its present form signifies a major conceptual advance of the field, as it provides only limited mechanistic insight, especially with respect to possible "non-canonical" functions of nrf2 (mechanisms of impact on Tg production and folliculogenesis). If such insights could be obtained it would clearly increase the significance of this contribution.

The main strength of the study is that it investigates Nrf2 function in the context of embryonic development. Even though the manuscript makes a point of evolutionary conserved mechanisms, I do not really see that that the discrepancies to results obtained from in vivo studies in higher vertebrates are sufficiently discussed and elaborated on.

Line 240. It feels a bit presumptuous to comment on the contents of an excellent paper that one of the authors of the current manuscript is the senior author of (Ziros et al 2018) and of course knows much better than I do. However, the present manuscript states (about Ziros et al 2018) that "In this study, the authors described how loss of Nrf2 function causes a thyroid phenotype only under stress conditions such as iodine overload. However, in the same study, the authors described that the loss of Nrf2 function causes a reduction of the thyroglobulin expression in PCCL3 rat thyroid follicular cell culture". In my recollection of Ziros et al there is a thyroid phenotype in KO mice not only under stress conditions, but also under normal conditions with reduced TG and increased TG-I? I would like the authors to comment on this.

The authors seem to emphasize the aspect of evolutionary conservation. However, even though I consider the possible effect on folliculogenesis in the mESC model as a very interesting finding, it is difficult to understsand if it is a phenomenon that is specific to the mESC model system or of more general importance. As the authors demonstrate, follicles indeed seem to develop in nrf2a deficient zebrafish. In Ziros et al 2018 no images of thyroid morphology are provided, but as KO mice are euthyroid it seems likely that follicular organization is not grossly perturbed. The authors need to elaborate on this. Even if the effect might be more or less specific to the mESC system, that does not necessarily make it less relevant. It might provide fundamental insights into the process of folliculogenesis, but for greater significance more mechanistic insight would be desirable.

Referees cross-commenting

I largely agree with the comments of referee #1, particularly the comment that the title (and some of the discussion) of the paper needs to be changed as pointed out by referee #1 ("...there is no evidence that there is a problem with thyroid development in ZF. The thyroid appears to be enlarged at the end of development, most likely as a consequence of increased TSH stimulation, but there is no developmental defect!").

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Referee #1

Evidence, reproducibility and clarity

This paper deals with the role of the transcription factor Nrf2 in the thyroid gland of zebrafish and in a thyroid organoid model. The subject if of relevance since Nrf2 is known to control the cellular response to oxidative stress and the thyroid is an organ where protection of oxidative stress is of major relevance, given the production of reactive oxygen species during thyroid hormone biosynthesis. The main result is that in Zebrafish (ZF) thyroid Nrf2 appears to be important for thyroid hormone formation since late stages ZF embryos deprived of NRF2 the levels of the thyroid hormone T4 and of its precursor, iodinated thyroglobulin(Tg), are very much decreased. However, there is no significant decrease of Thyroglobulin mRNA, albeit an impairment in the up-regulation of Tg by TSH could be observed. No effect is seen on the structure of the thyroid follicles and no developmental defect is observed, in contrast with the title of the paper. Conversely, in the mouse thyroid organoid model the absence of Nrf2 results in an impressive decrease of Tg mRNA and in impaired formation of thyroid follicles. The study is in most part elegant and technically impeccable. The data are well presented and organised as far as figure is concerned. However, much remains to be done on the interpretation and presentation of results. In addition, the text that has been put together sloppily, with many typing and punctuation mistakes and difficult to interpret sentences. A revision of typing and syntax is absolutely needed.

Main concerns:

1. The title of the paper needs to be changed. There is no evidence that there is a problem with thyroid development in ZF. The thyroid appears to be enlarged at the end of development, most likely as a consequence of increased TSH stimulation, but there is no developmental defect!
2. There is an evident contradiction, in ZF, between the marginal, if any, decrease of Tg mRNA and the impressive decrease in T4 and iodinated Tg. This, in my opinion, very interesting discrepancy, is never discussed. Perhaps the authors should look at the level of Tg protein. It it possible that there is an increased degradation or some negative translational control in absence of Nrf2? Alternatively, is it possible that there is a defect, yet unidentified, in the organification process? Certainly, to conclude, as the authors do in page 11, lines 236-237, that the defect in hormonogenesis depends on thyroglobulin production is, with the data presented, an unproven statement.
3. The data on transcriptional effect of NRrf2 in the mouse ES cell system do not really add much. Their major effect is to contribute to a lengthy discussion that would really benefit of a substantial reduction.
4. More time should be devoted to explain the substantial differences between the three systems studied (two in this paper, one in a previous published by partly same authors), keeping in mind that studies in mice could be largely influenced by the genetic background.

Significance

This paper is largely confirmatory of previous results obtained in a mouse Nrf2 KO model, whose main authors are also part of this study (Ziros et al. , 2018). A clarification of the molecular defect in hormone production in ZF could add the novelty that this study might need.

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Reply to the reviewers

Ruby Ponnudurai

Scientific Editor

Review Commons

February 16th, 2026

Dear Dr. Ponnudurai,

Please see below for a detailed response to reviewers for manuscript #RC-2025-03108: "Short chain fatty acids regulate the chromatin landscape and distinct gene expression changes in human colorectal cancer cells".

__Authors' Summary: __We thank all the reviewers for the constructive and immensely helpful reviews of our manuscript. We have revised the manuscript addressing the reviewers' comments, which we feel has substantially strengthened our paper. Please see below for our point-by-point responses to the comments, which are all indicated in blue text. All changes in the manuscript are also indicated in blue text.

Reviewer #1 Evidence, reproducibility and clarity

In this manuscript, Kabir et al. explore the impact of microbiota-derived short-chain fatty acids (SCFAs) on chromatin structure and gene expression in human cells. They show that SCFAs, particularly butyrate, contribute to specific histone modifications such as butyrylation at H3K27, detectable in human colon tissue. Additional modifications like acetylation, butyrylation, and propionylation at H3K9 and H3K27 respond to SCFA levels and are enriched at active regulatory regions in colorectal cancer cells. Treatment with individual or combined SCFAs mimicking gut conditions alters gene expression patterns, with butyrate playing a dominant regulatory role. Butyrate's effects on gene expression are claimed to be independent of HDAC inhibition and instead rely on the p300/CBP complex through histone butyrylation. These findings underscore SCFAs as crucial modulators of epigenetic regulation in the human colon and highlight butyrate's dominant role in shaping chromatin and gene regulation beyond its known metabolic functions.

The authors used two human cell lines and an in vivo murine model paired with RNA and ChIP sequencing approaches to identify target genes and chromatin modifications in response to SCFAs.

While the findings are interesting and could provide important insights into the epigenetic influence of SCFAs in human cells, the study would benefit from additional experiments to strengthen the conclusions. Comments and suggestions are listed below:

Response: We sincerely thank the reviewer for their thoughtful and constructive comments. In addition, we appreciate the recognition of the potential impact of our findings. We have addressed all comments below.

1. Figure 1: The H3K27bu expression in human biopsies highlights the clinical significance of the current study. However, the authors need to provide more information on the human colon samples, e.g., how many total patients were analyzed, and what were the age and/or sex. Only the methods mention the use of benign TMA; this should also be clarified in the figure legends. It would also be helpful to show histone butyrylation levels in normal vs. cancer human tissues.

Response: We completely agree that analysis of additional patient samples is important. In light of this comment, we have expanded our analysis of human colon samples. In the original manuscript, we showed IF images from patient intestinal sections. Patient demographic information (age and sex) is now included in the figure legend. While we analyzed two patients by IF, we realized that images from only one patient are shown. We also felt it was important to add additional rigor to our patient analysis. Therefore, we have incorporated additional patient samples and performed H3K27bu staining using IHC across normal and colon cancer sections obtained from 40 different patients. This is now included as Supplemental Figure 1. In addition, we have included information about age, sex, staging, and grading in Supplemental Figure 1C. Interestingly, we observed that adenocarcinoma patients have significantly decreased levels of H3K27bu compared to normal colon or normal adjacent tissues (Supplemental Figure 1B). We speculate that this may be due to alterations with the microbiota composition and dysbiosis associated with colorectal cancer (PMIDs: 26515465, 25758642, 25699023). Very interestingly, this is in contrast to reports of elevated H3K27ac in colon cancer samples (PMID: 24994966). We are excited to explore this further, and this is something we plan to follow-up on in future studies.

1. Figure 1: In addition, given that the butyrate level descends towards the base of the colonic crypt (with the highest at the top of the crypt where mature intestinal epithelial cells reside) (Kaiko et al., 2016), it is important to show how the H3K27bu signature is distributed along the crypt. This data would further emphasize the clinical relevance of this study, given that most colorectal cancers (CRCs) arise from stem and progenitor cells.

Response: We agree that this is an important question and recognize the elegant study by Kaiko et al. However, our human samples are obtained from commercially available tissue microarrays and the sectioning is not consistent across samples, resulting in a minimal amount of samples that we could analyze for staining patterns from crypt to villi (please see Supplemental Figure 1A for example sections). This unfortunately prevents us from completing rigorous image analysis. In future studies, we plan to perform this analysis after we obtain an IRB protocol that will allow us to answer this question in the most rigorous way possible.

Throughout the manuscript: The rationale for selecting the two CRC cell lines (HCT 116 and Caco2) should be explained. While commonly used, providing background on their genetic differences (e.g., driver mutations) is important, as this could greatly influence the PTM landscape.

Response: We chose to use both HCT-116 and Caco-2 cancer cell lines throughout our studies, since as noted these cells are the most commonly used lines in the literature. In addition, having consistent results across distinct genetic backgrounds strengthens our results: using both cell lines tells us whether observed PTM patterns are conserved across genetically diverse CRC contexts, as HCT-116 is characterized by mutations in KRAS and PIK3CA, while Caco-2 has mutations in APC and TP53 (PMIDs: 17088437, 24755471, and 16418264). We have added this information into the text in lines 106-107.

The study lacks additional controls, such as a normal colon epithelial cell line and a non-colonic cell type. Including these would help determine whether the observed butyrate effects are tissue- or disease-specific. This data would also help assess whether SCFA effects, and specifically butyrate's effects, on histone acylation and gene expression are systemic or local.

Response: Thank you for this insightful comment. We have now included additional data using normal colon cells in the form of mouse colon organoids and a distinct non-intestinal cell line, the embryonic kidney cell line HEK 293T. Importantly, we observe similar changes to chromatin after treatments with different SCFAs in both colon organoids and HEK 293T cells as shown in the cancer cell lines (Figure 1E, 1F). Interestingly, we also observe that the colon cancer cell lines have visible signal of histone butyrylation without treatment, while we only observe these modifications in HEK 293T cells following treatment.