Dear Dr Foley,

Thank you for submitting your manuscript entitled "Estrogen impacts NOD2-dependent regulation of intestinal homeostasis" for consideration as a Research Article by PLOS Biology.

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Kind regards,

Ines

--

Ines Alvarez-Garcia, PhD

Senior Editor

PLOS Biology

ialvarez-garcia@plos.org

Dear Dr Foley,

Thank you for your patience while your manuscript entitled "Estrogen impacts NOD2-dependent regulation of intestinal homeostasis" was peer-reviewed at PLOS Biology. Please also accept again my apologies for the delay in sending you our decision. The manuscript has now been evaluated by the PLOS Biology editors, an Academic Editor with relevant expertise, and by three independent reviewers.

The reviews are attached below. As you will see, the reviewers find the conclusions interesting and worth pursuing for publication, but they also raise several issues that will need to be addressed. Reviewer 1 asks for deeper histological analyses to show the regional effects, misses quantification in some of the experiments, and requests an analysis of the individual scRNAseq animals by male/female to confirm the 3 females to 2 males split in the dataset. Similarly, Reviewer 2 would like to know if sex is controlled for and thinks that some of the data should be presented according to sex. This reviewer also asks for a better presentation of the data to see animal-level and tissue-/cell-level variability and more mechanistic details on how estrogen signalling is achieved, among other issues. Reviewer 3 also requests clarifications on the methods and thinks that some of the results should be better discussed.

In light of the reviews, we would like to invite you to revise the work to thoroughly address the reviewers' reports. Given the extent of revision needed, we cannot make a decision about publication until we have seen the revised manuscript and your response to the reviewers' comments. Your revised manuscript is likely to be sent for further evaluation by all or a subset of the reviewers.

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Thank you again for your submission to our journal. We hope that our editorial process has been constructive thus far, and we welcome your feedback at any time. Please don't hesitate to contact us if you have any questions or comments.

Sincerely,

Ines

--

Ines Alvarez-Garcia, PhD

Senior Editor

PLOS Biology

ialvarez-garcia@plos.org

------------------------------------

Reviewers' comments

Rev. 1: Stefan Oehlers – please note that this reviewer has signed the review.

Eklund & Foley use a novel zebrafish nod2 mutant allele to investigate the role of Nod2 in intestinal homeostasis, response to injury, and interaction with estrogen signalling. The manuscript's most novel finding is the interaction with estrogen signalling whereby Nod2 and E2/tamoxifen-regulated signalling appear to oppose each other. The discussion and limitation sections are quite clear about additional mechanistic experiments that *could* be performed to strengthen the manuscript's argument (such as use of genetics to target ER, additional small molecule probes). I am happy that sufficient experimental evidence is provided, most importantly in the form of a genetic tool combined with opposing small molecule probes with well characterised biological activity) to support the claims made in the manuscript and my comments are limited to deeper analysis of existing datasets and clarification points.

Specific comments

Some of the histological analyses would benefit from deeper analyses. The regional effects, while not essential to the narrative of the Nod2 story, are useful to advance the comparative intestinal biology field.

Figure 1BC: there is an intestinal fold height difference in the later figures (Fig 3I, S1. Maybe not so strong in 2IJ) that should be described early in the story here.

Figure 2K could be quantified to comment on the apical vs basal/LP location of leukocytes. From the example images it appears the increase in leukocyte density is driven by leukocytes at the base of the intestinal folds. It might be difficult to prove, but this would correlate with stroma>IEC expression of chemoattractant/adhesion genes in NOD2-/-.

Fig S5 and 3F: please be more clear about the location (along the intestinal bulb-cloaca axis) of tissue shown as examples and enumerated. I think the right edge of the S5 images are the cloaca but the framing of the 3F images is not immediately obvious.

Figure 3H: Can the authors explain why they switched to a flow cytometry methodology here? The whole mount imaging approach would allow detection of spatial patterns to NOD2/MDP-dependent proliferation that are missed by the analysis of dissociated cells.

Figure 4IJ text "the absolute barrier size" does not appear to be related to the presented analysis. Additionally the area of analysis outlined in Fig 4I and the methods suggests pneumatic duct-derived lumen mucins would be included in the quantification. I think the most pertinent measure would be goblet cell number/density rather than total mucins, which would be more variable from peristalsis and handling.

Figure 5: the qPCR data in 5HI suggest the vtg signal in panels A-G was driven by the 3 females to 2 males split in the scRNAseq dataset. Can the authors subanalyse the individual scRNAseq animals by male/female split to confirm this?

Conclusion/Discussion text

The second clause in the final results paragraph is a bit overstated, the authors did not explore the effect of E2 exposure on cell death phenotype, admittedly this was only explored in adult mutants so there is the *in zebrafish larvae caveat here.

Would the final clause "...key modifier of the disruptions..." be clearer as "estrogen and NOD2 oppose each other"?

Discussion paragraph beginning "Further supporting a mechanistic link": this would be an appropriate place to discuss the zebrafish paper using tamoxifen vs M. marinum infection (PMID 36475748).

Rev. 2:

This is an interesting manuscript that demonstrates a new role for estradiol and NOD2 signaling in intestinal cell homeostasis. The integration of scRNAseq and phenotypic characterization provides a multifaceted view of intestinal homeostasis, and the exploration of estrogen receptor involvement (even without discovering which estrogen receptors are involved) adds valuable mechanistic insight. The claims are novel and the conclusions are generally supported by the data.

However, there are several limitations and areas where it is not clear whether the conclusions are supported by the data. The manuscript does not consistently control for sex across experiments, which may confound interpretation of sex-dependent effects. Key findings, such as those related to cell proliferation in adult intestine, would benefit from stratification or explicit reporting by sex. Some data presentations, including quantification of immune and proliferative cell populations, would be more rigorous if shown as super plots to illustrate animal-level and tissue-/cell-level variability. Finally, further clarity on mechanism of estrogen signaling could be achieved by including additional pharmacologic controls and exploring the roles of both nuclear and membrane estrogen receptors using specific agonists/antagonists.

Note that I do not have the expertise to analyze the scRNAseq data in detail. GSE299263 is deposited on NCBI (scheduled for public release in March 2026) but I was not given a reviewer token to access it.

Specific comments:

1. Is sex being controlled for? In some cases it is not mentioned (eg Fig 1B), in other cases it is purposely confounded (eg scRNAseq experiments on 2M, 3F, with results pooled/not controlled for sex, Fig 2). Are there any sex-dependent effects of either NOD2 mutant phenotypes or estrogen exposure phenotypes in the gut? If the authors are focused on NOD2 effects in common to both sexes, or that occur in either sex (without regards to potential sex differences), then please make this clear for each and every experiment.

2. Related, NOD2-deficiency increased the estrogen response (vtg gene expression) in adult females but not in males (Fig 5). Does this suggest that NOD2 functions to regulate intestinal homeostasis in females but not in males? How is this result reconciled with previous results from the manuscript (eg PCNA-pos cells) in wt vs nod2 mutant adults? Are the PCNA results in Fig 3 containing only females? Or mixed sex but the female signal swamps the male signal? It would be interesting (and add to the rigor and comprehensiveness of the manuscript) if the authors could present data in Fig 1-4 with regard to sex. For example, in Figure 4G, does the goblet cell number variability and/or association with genotype change when graphed according to sex?

3. NOD2-deficient intestines contain larger population of dysregulated immune cells vs wt. Fig 2K - nod2 mutants have greater number of Lcp1+ cells. This conclusion is not supported by the data (as presented) - could the authors show these data as a super plot or similar (PMID 32346721), where we could see the number of Lcp1+ cells per fish (unit of biological replicate) and the number of Lcp1+ cells per um or ROI (tissue-level variability)?

4. An interesting result from the scRNAseq is the upregulation of estrogen-responsive genes in nod2 mutants vs wt. The vtg genes suggest the involvement of nuclear estrogen receptors (esr1, esr2a, esr2b), but shouldn't the manuscript also consider the possibility that a membrane estrogen receptor, eg gper1, might also be involved? For example, in Fig 5, can the manuscript show the expression of gper1 in intestine, and how it might vary by cell type in wt vs nod2 mutants?

5. Related, tamoxifen is a selective estrogen receptor modulator, meaning it acts as an agonist in some cells but an antagonist in others. Are the authors arguing here that tamoxifen is acting as an estrogen receptor antagonist? In that case, Fig 6 is missing a key control - what happens in wt larvae exposed to vehicle (shown) vs E2 (shown) vs tam (shown) vs E2+tam (not shown)? Because the authors are not taking a genetic approach (eg exposing esr or gper mutants), it would add additional rigor to the manuscript if these experiments could be repeated with an additional estrogen receptor antagonist, such as ICI182,780 (an anti-estrogen, not a selective estrogen receptor modulator). If the results are consistent, this would more clearly demonstrate a role for estrogens and for nuclear estrogen receptors. Alternatively, if the results are discordant, this could suggest a role for GPER, which could be further tested using GPER-specific agonists/antagonists that have low/no affinity for nuclear estrogen receptors.

6. Limitations section - the NOD2 mutant phenotypes are compelling, but it would be more rigorous to mention, as a limitation, that the phenotypes you see could be hypomorphic and not due to a true null allele (eg, even in the absence of NOD2 protein, there could be transcriptional adaptation occurring, see for example PMID 39939773, 31951195, 40128410, 30944477, where the nod2 mutant RNA is degraded and triggers upregulation of compensatory genes that can partially compensate for loss of NOD2 protein). This is supported by the MDP experiments (NOD2 ligand) where there is still a small effect in nod2 mutants. Doing additional experiments to test for the presence of transcriptional adaption will NOT change the manuscript's conclusions and is not necessary; adding a sentence or two in the limitations acknowledging the possibility of compensation is sufficient.

7. Fig 1B - shorter gut length phenotype in NOD2 mutants. Is gut length a function of fish length (eg standard length, as in PMID 19891001)? Could the reduced gut length in the 9 NOD2 mutants examined really be due to those fish being shorter (eg not controlling for standard length) and not a function of genotype?

8. Fig 3G, 3H: In panel H, EdU-pos cells were quantified using flow cytometry, why were they not quantified this way in panel G? How were EdU-pos cells quantified in panel G?

9. Fig 3J: the conclusion that nod2 mutants have reduced cell proliferation in intestine (PCNA-pos cells) is not supported by the data (as presented). Could the authors show these data as a super plot or similar (PMID 32346721), where we could see the number/percent of PCNA+ cells per fish (unit of biological replicate) and the number/percent of PCNA+ cells per um or ROI (tissue-level variability)?

10. Same comment for Suppl Fig 5 (see #9)

11. Analogous comment for graphs in Fig 4 (see #9)

12. Methods - please provide more details on how fish were housed singly (Fig 1I-M). Do fish in different tanks housed on the same system sharing recirculating water have different bacterial community composition in their guts?

Rev. 3:

The manuscript by Eklund and Foley represents an impressive body of work that advances understanding of the function of the IBD-associated NOD2 gene function in the vertebrate intestinal epithelium. Using single cell RNAseq, the authors identify a role for NOD2 in repression of estrogen-response genes. They go on to test the functional relevance of this mis-regulation using pharmacological approaches that support a role for excessive estrogen-response gene expression in NOD2-associated intestinal pathology. Specific comments on the manuscript are listed below.

1. A key assay throughout the paper is the quantification of cell proliferation in the intestinal epithelium. Confusingly, the authors use two different assays and three different representations of their data. In some instances they quantify EdU+ cells by immunohistochemistry, and either report this as the number of EdU+ cells/gut (preferable, because the values are easy to understand) or as a percentage in Fig 3G (presumably percentage of all epithelial cells?). They should use a consistent scoring method throughout. They should also provide more explanation of how this quantification is actually performed. Do they reconstruct the volume of the gut tube? What region of the gut is quantified (the representative images for Fig 3F looks different from that of Supplemental Fig 5 or Fig 6A and C)? For Fig 3H they report a different assay for quantifying EdU+ cells by flow cytometry. What is the reason for using this different assay in this one instance?

2. Another key assay is the quantification of goblet cells. For this they report quantifying the Alcian positive area in a region of interest. This would involve setting some threshold of blue intensity to discriminate background from signal. How was this done in an unbiased manner?

3. The results switch between adult and larval experiments extensively. It would be helpful for the authors to explain the motivation for performing experiments at these specific stages. It would be helpful in the figures to include larval or adult icons.

4. The authors cite two other independently generated nod2 deficient zebrafish. They should provide more explanation of how the different mutants were made and they similarities and differences in the phenotypes reported.

5. Humans do not typically harbor complete deletions of NOD2, as in this zebrafish model. The authors should discuss how their results with nod2 deficient zebrafish fit into what is known about the spectrum of NOD2 alleles in humans that are associated with disease.

Dear Dr Foley,

Thank you for your patience while we considered your revised manuscript entitled "Estrogen impacts NOD2-dependent regulation of intestinal homeostasis" for publication as a Research Article at PLOS Biology. This revised version of your manuscript has been evaluated by the PLOS Biology editors, the Academic Editor and one of the original reviewers.

Based on the reviews (attached below), we are likely to accept this manuscript for publication, provided you satisfactorily address the remaining points raised by Reviewer 2. Regarding the tamoxifen discussion (Point 2), you could simply modify the sentence to say that TAM can sometimes act as an agonist. Please also make sure to address the data and other policy-related requests stated below my signature.

As you address these items, please take this last chance to review your reference list to ensure that it is complete and correct. If you have cited papers that have been retracted, please include the rationale for doing so in the manuscript text, or remove these references and replace them with relevant current references. Any changes to the reference list should be mentioned in the cover letter that accompanies your revised manuscript.

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Please do not hesitate to contact me should you have any questions.

Sincerely,

Ines

--

Ines Alvarez-Garcia, PhD

Senior Editor

PLOS Biology

ialvarez-garcia@plos.org

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DATA POLICY: IMPORTANT - PLEASE READ

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Reviewers' comments

Rev. 2:

I commend the authors for their response to reviewer comments. I think the revised manuscript is clearer and more rigorous. Two points which I think could be addressed further:

(1) I'm still unsure about the unit of biological replication in some experiments, which is why I originally suggested using SuperPlots. For instance, Figure 2K aims to show that nod2 mutants have more Lcp1+ cells than wild-type fish. The legend states that each group consists of five fish, yet the graph displays dozens of data points. If a single fish is considered one replicate, shouldn't there only be five data points per group? My earlier SuperPlot suggestion was intended to have the authors add these five fish-level data points to the existing graph, allowing readers to see both the Lcp1+ cells per intestine/ROI and per fish simultaneously. Currently, each dot represents a measurement from a fish intestine image. Is this what counts as a replicate? If so, what is the reasoning, and why not use Lcp1+ cell counts per fish instead? After reviewing the methods section (see below), I still couldn't find clarification. Could the authors explicitly state what constitutes a unit of replication? While variability in results is expected (and reflects underlying biology), choosing different definitions for the unit of replication could impact the conclusions regarding differences between wild type and nod2 mutants.

"Quantification of Anxa4⁺ secretory cells, Lcp1⁺ leukocytes, and TUNEL⁺ apoptotic cells was performed on sagittal intestinal sections using Fiji (ImageJ). Individual villi were manually outlined using the DNA (nuclear) channel to define the epithelial region of interest. Within each villus ROI, Anxa4⁺, Lcp1⁺, and TUNEL⁺ cells were detected using a fixed threshold applied uniformly across all samples and counted manually using the cell counter tool. Total epithelial cell number per villus was determined by counting all DNA⁺ nuclei within the same ROI. To account for differences in villus size and cellular density between sections and fish, data were expressed as the percentage of marker-positive cells per villus, calculated as (number of Anxa4⁺, Lcp1⁺, or TUNEL⁺ cells ÷ total number of DNA⁺ nuclei within the ROI) x 100."

(2) Tamoxifen is a selective estrogen receptor modulator, and I believe the discussion section should more clearly address in the 'limitations' section that the authors are assuming TAM acts solely as an antagonist (though they may have strong reasons for making this assumption). However, TAM can also function as an ER agonist, and it may act as a GPER agonist as well (see PMID 15705806, 16239258). The revised discussion currently states, "…tamoxifen may engage additional target pathways." This wording seems somewhat vague and could be expanded to clarify that there is substantial evidence showing TAM can behave as an agonist in some tissues or contexts and as an antagonist in others, even within the same organism simultaneously, and how this might impact the interpretation of the author's results. This complexity helps explain why TAM cannot be used indefinitely in humans for treating ER-positive breast cancers. That said, I am not insisting on this point and will defer to the editor's judgment regarding how extensively this limitation should be addressed.

Dear Dr Foley,

Thank you for the submission of your revised Research Article entitled "Estrogen impacts NOD2-dependent regulation of intestinal homeostasis" for publication in PLOS Biology. On behalf of my colleagues and the Academic Editor, Ken Cadwell, I am delighted to let you know that we can in principle accept your manuscript for publication, provided you address any remaining formatting and reporting issues. These will be detailed in an email you should receive within 2-3 business days from our colleagues in the journal operations team; no action is required from you until then. Please note that we will not be able to formally accept your manuscript and schedule it for publication until you have completed any requested changes.

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Many congratulations and thanks again for choosing PLOS Biology for publication and supporting Open Access publishing. We look forward to publishing your study.

Sincerely,

Ines

--

Ines Alvarez-Garcia, PhD

Senior Editor

PLOS Biology

ialvarez-garcia@plos.org