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

Summary: In this study, the authors used proximity proteomics in U2OS cells to identify several E3 ubiquitin ligases recruited to stress granules (SGs), and they focused on MKRN2 as a novel regulator. They show that MKRN2 localization to SGs requires active ubiquitination via UBA1. Functional experiments demonstrated that MKRN2 knockdown increases the number of SG condensates, reduces their size, slightly raises SG liquidity during assembly, and slows disassembly after heat shock. Overexpression of MKRN2-GFP combined with confocal imaging revealed co-localization of MKRN2 and ubiquitin in SGs. By perturbing ubiquitination (using a UBA1 inhibitor) and inducing defective ribosomal products (DRiPs) with O-propargyl puromycin, they found that both ubiquitination inhibition and MKRN2 depletion lead to increased accumulation of DRiPs in SGs. The authors conclude that MKRN2 supports granulostasis, the maintenance of SG homeostasis , through its ubiquitin ligase activity, preventing pathological DRiP accumulation within SGs.

Major comments: - Are the key conclusions convincing? The key conclusions are partially convincing. The data supporting the role of ubiquitination and MKRN2 in regulating SG condensate dynamics are coherent, well controlled, and consistent with previous literature, making this part of the study solid and credible. However, the conclusions regarding the ubiquitin-dependent recruitment of MKRN2 to SGs, its relationship with UBA1 activity, the functional impact of the MKRN2 knockdown for DRiP accumulation are less thoroughly supported. These aspects would benefit from additional mechanistic evidence, validation in complementary model systems, or the use of alternative methodological approaches to strengthen the causal connections drawn by the authors. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The authors should qualify some of their claims as preliminary. 1) MKRN2 recruitment to SGs (ubiquitin-dependent): The proteomics and IF data are a reasonable starting point, but they do not yet establish that MKRN2 is recruited from its physiological localization to SGs in a ubiquitin-dependent manner. To avoid overstating this point the authors should qualify the claim and/or provide additional controls: show baseline localization of endogenous MKRN2 under non-stress conditions (which is reported in literature to be nuclear and cytoplasmatic), include quantification of nuclear/cytoplasmic distribution, and demonstrate a shift into bona fide SG compartments after heat shock. Moreover, co-localization of overexpressed GFP-MKRN2 with poly-Ub (FK2) should be compared to a non-stress control and to UBA1-inhibition conditions to support claims of stress- and ubiquitination-dependent recruitment. *

Authors: We will stain cells for endogenous MKRN2 and quantify nuc/cyto ratio of MKRN2 without heat stress, without heat stress + TAK243, with HS and with HS + TAK243. We will do the same in the MKRN2-GFP overexpressing line while also staining for FK2.

*2) Use and interpretation of UBA1 inhibition: UBA1 inhibition effectively blocks ubiquitination globally, but it is non-selective. The manuscript should explicitly acknowledge this limitation when interpreting results from both proteomics and functional assays. Proteomics hits identified under UBA1 inhibition should be discussed as UBA1-dependent associations rather than as evidence for specific E3 ligase recruitment. The authors should consider orthogonal approaches before concluding specificity. *

Authors: We have acknowledged the limitation of using only TAK243 in our study by rephrasing statements about dependency on “ubiquitination” to “UBA1-dependent associations”.

* 3) DRiP accumulation and imaging quality: The evidence presented in Figure 5 is sufficient to substantiate the claim that DRiPs accumulate in SGs upon ubiquitination inhibition or MKRN2 depletion but to show that the event of the SGs localization and their clearance from SGs during stress is promoted by MKRN3 ubiquitin ligase activity more experiments would be needed. *

Authors: We have acknowledged the fact that our experiments do not include DRiP and SG dynamics assays using ligase-dead mutants of MKRN2 by altering our statement regarding MKRN2-mediated ubiquitination of DRiPs in the text (as proposed by reviewer 1).

*- Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. Yes, a few targeted experiments would strengthen the conclusions without requiring the authors to open new lines of investigation. 1) Baseline localization of MKRN2: It would be important to show the baseline localization of endogenous and over-expressed MKRN2 (nuclear and cytoplasmic) under non-stress conditions and prior to ubiquitination inhibition. This would provide a reference to quantify redistribution into SGs and demonstrate recruitment in response to heat stress or ubiquitination-dependent mechanisms. *

Authors: We thank the reviewer for bringing this important control. We will address it in revisions.

We will quantify the nuclear/cytoplasmic distribution of endogenous and GFP-MKRN2 under control, TAK243, heat shock, and combined conditions, and assess MKRN2–ubiquitin colocalization by FK2 staining in unstressed cells.

* 2) Specificity of MKRN2 ubiquitin ligase activity: to address the non-specific effects of UBA1 inhibition and validate that observed phenotypes depend on MKRN2's ligase activity, the authors could employ a catalytically inactive MKRN2 mutant in rescue experiments. Comparing wild-type and catalytic-dead MKRN2 in the knockdown background would clarify the causal role of MKRN2 activity in SG dynamics and DRiP clearance. *

Authors: We thank the reviewer for this suggestion and have altered the phrasing of some of our statements in the text accordingly.

* 3) Ubiquitination linkage and SG marker levels: While the specific ubiquitin linkage type remains unknown, examining whether MKRN2 knockdown or overexpression affects total levels of key SG marker proteins would be informative. This could be done via Western blotting of SG markers along with ubiquitin staining, to assess whether MKRN2 influences protein stability or turnover through degradative or non-degradative ubiquitination. Such data would strengthen the mechanistic interpretation while remaining within the current study's scope. *

Authors: We thank the reviewer for requesting and will address it by performing MKRN2 KD and perform Western blot for G3BP1.

*

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. The experiments suggested in points 1 and 3 are realistic and should not require substantial additional resources beyond those already used in the study. • Point 1 (baseline localization of MKRN2): This involves adding two control conditions (no stress and no ubiquitination inhibition) for microscopy imaging. The setup is essentially the same as in the current experiments, with time requirements mainly dependent on cell culture growth and imaging. Overall, this could be completed within a few weeks. • Point 3 (SG marker levels and ubiquitination): This entails repeating the existing experiment and adding a Western blot for SG markers and ubiquitin. The lab should already have the necessary antibodies, and the experiment could reasonably be performed within a couple of weeks. • Point 2 (catalytically inactive MKRN2 mutant and rescue experiments): This is likely more time-consuming. Designing an effective catalytic-dead mutant depends on structural knowledge of MKRN2 and may require additional validation to confirm loss of catalytic activity. If this expertise is not already present in the lab, it could significantly extend the timeline. Therefore, this experiment should be considered only if similarly recommended by other reviewers, as it represents a higher resource and time investment.

Overall, points 1 and 3 are highly feasible, while point 2 is more substantial and may require careful planning.

• Are the data and the methods presented in such a way that they can be reproduced? Yes. The methodologies used in this study to analyze SG dynamics and DRiP accumulation are well-established in the field and should be reproducible, particularly by researchers experienced in stress granule biology. Techniques such as SG assembly and disassembly assays, use of G3BP1 markers, and UBA1 inhibition are standard and clearly described. The data are generally presented in a reproducible manner; however, as noted above, some results would benefit from additional controls or complementary experiments to fully support specific conclusions.

• Are the experiments adequately replicated and statistical analysis adequate? Overall, the experiments in the manuscript appear to be adequately replicated, with most assays repeated between three and five times, as indicated in the supplementary materials. The statistical analyses used are appropriate and correctly applied to the datasets presented. However, for Figure 5 the number of experimental replicates is not reported. This should be clarified, and if the experiment was not repeated sufficiently, additional biological replicates should be performed. Given that this figure provides central evidence supporting the conclusion that DRiP accumulation depends on ubiquitination-and partly on MKRN2's ubiquitin ligase activity-adequate replication is essential. *

Authors: We thank the reviewer for noting this accidental omission. We now clarify in the legend of Figure 5 that the experiments with DRiPs were replicated three times.

Minor comments: - Specific experimental issues that are easily addressable. • For the generation and the validation of MKRN2 knockdown in UOS2 cells data are not presented in the results or in the methods sections to demonstrate the effective knockdown of the protein of interest. This point is quite essential to demonstrate the validity of the system used

Authors: We thank the reviewer for requesting and will address it by performing MKRN2 KD and perform Western blot and RT-qPCR.

• * In the supplementary figure 2 it would be useful to mention if the Western Blot represent the input (total cell lysates) before the APEX-pulldown or if it is the APEX-pulldown loaded for WB. There is no consistence in the difference of biotynilation between different replicates shown in the 2 blots. For example in R1 and R2 G3BP1-APX TAK243 the biotynilation is one if the strongest condition while on the left blot, in the same condition comparison samples R3 and R4 are less biotinilated compared to others. It would be useful to provide an explanation for that to avoid any confusion for the readers. * Authors: We have added a mention in the legend of Figure S2 that these are total cell lysates before pulldown. The apparent differences in biotin staining are small and not sufficient to question the results of our APEX-proteomics.

• * In Figure 2D, endogenous MKRN2 localization to SGs appears reduced following UBA1 inhibition. However, it is not clear whether this reduction reflects a true relocalization or a decrease in total MKRN2 protein levels. To support the interpretation that UBA1 inhibition specifically affects MKRN2 recruitment to SGs rather than its overall expression, the authors should provide data showing total MKRN2 levels remain unchanged under UBA1 inhibition, for example via Western blot of total cell lysates. * Authors: Based on first principles in regulation of gene expression, it is unlikely that total MKRN2 expression levels would decrease appreciably through transcriptional or translational regulation within the short timescale of these experiments (1 h TAK243 pretreatment followed by 90 min of heat stress).

• * DRIPs accumulation is followed during assembly but in the introduction is highlighted the fact that ubiquitination events, other reported E3 ligases and in this study data on MKRN2 showed that they play a crucial role in the disassembly of SGs which is also related with cleareance of DRIPs. Authors could add tracking DRIPs accumulation during disassembly to be added to Figure 5. I am not sure about the timeline required for this but I am just adding as optional if could be addressed easily. * Authors: We thank the reviewer for proposing this experimental direction. However, in a previous study (Ganassi et al., 2016; 10.1016/j.molcel.2016.07.021), we demonstrated that DRiP accumulation during the stress granule assembly phase drives conversion to a solid-like state and delays stress granule disassembly. It is therefore critical to assess DRiP enrichment within stress granules immediately after their formation, rather than during the stress recovery phase, as done here.

• * The authors should clarify in the text why the cutoff used for the quantification in Figure 5D (PC > 3) differs from the cutoff used elsewhere in the paper (PC > 1.5). Providing a rationale for this choice will help the reader understand the methodological consistency and ensure that differences in thresholds do not confound interpretation of the results. * Authors: We thank the reviewer for this question. The population of SGs with a DRiP enrichment > 1.5 represents SGs with a significant DRiP enrichment compared to the surrounding (background) signal. As explained in the methods, the intensity of DRiPs inside each SG is corrected by the intensity of DRiPs two pixels outside of each SG. Thus, differences in thresholds between independent experimental conditions (5B versus 5D) do not confound interpretation of the results but depend on overall staining intensity that can different between different experimental conditions. Choosing the cut-off > 3 allows to specifically highlight the population of SGs that are strongly enriched with DRiPs. MKRN2 silencing caused a strong DRiP enrichment in the majority of the SGs analyzed and therefore we chose this way of data representation. Note that the results represent the average of the analysis of 3 independent experiments with high numbers of SGs automatically segmented and analyzed/experiment. Figure 5A, B: n = 3 independent experiments; number of SGs analyzed per experiment: HS + OP-puro (695; 1216; 952); TAK-243 + HS + OP-puro (1852; 2214; 1774). Figure 5C, D: n = 3 independent experiments; number of SGs analyzed per experiment: siRNA control, HS + OP-puro (1984; 1400; 1708); siRNA MKRN2, HS + OP-puro (912; 1074; 1532).

• * For Figure 3G, the authors use over-expressed MKRN2-GFP to assess co-localization with ubiquitin in SGs. Given that a reliable antibody for endogenous MKRN2 is available and that a validated MKRN2 knockdown line exists as an appropriate control, this experiment would gain significantly in robustness and interpretability if co-localization were demonstrated using endogenous MKRN2. In the current over-expression system, MKRN2-GFP is also present in the nucleus, whereas the endogenous protein does not appear nuclear under the conditions shown. This discrepancy raises concerns about potential over-expression artifacts or mislocalization. Demonstrating co-localization using endogenous MKRN2 would avoid confounding effects associated with over-expression. If feasible, this would be a relatively straightforward experiment to implement, as it relies on tools (antibody and knockdown line) already described in the manuscript.

* Authors: We thank the reviewer for requesting and will address it by performing MKRN2 KD, FK2 immunofluorescence microscopy and perform SG partition coefficient analysis.

* - Are prior studies referenced appropriately? • From line 54 to line 67, the manuscript in total cites eight papers regarding the role of ubiquitination in SG disassembly. However, given the use of UBA1 inhibition in the initial MS-APEX experiment and the extensive prior literature on ubiquitination in SG assembly and disassembly under various stress conditions, the manuscript would benefit from citing additional relevant studies to provide more specifc examples. Expanding the references would provide stronger context, better connect the current findings to prior work, and emphasize the significance of the study in relation to established literature *

Authors: We have added citations for the relevant studies.

• *

At line 59, it would be helpful to note that G3BP1 is ubiquitinated by TRIM21 through a Lys63-linked ubiquitin chain. This information provides important mechanistic context, suggesting that ubiquitination of SG proteins in these pathways is likely non-degradative and related to functional regulation of SG dynamics rather than protein turnover. * Authors: The reviewer is correct. We have added to the text that G3BP1 is ubiquitinated through a Lys63-linked ubiquitin chain.

• *

When citing references 16 and 17, which report that the E3 ligases TRIM21 and HECT regulate SG formation, the authors should provide a plausible explanation for why these specific E3 ligases were not detected in their proteomics experiments. Differences could arise from the stress stimulus used, cell type, or experimental conditions. Similarly, since MKRN2 and other E3 ligases identified in this study have not been reported in previous works, discussing these methodological or biological differences would help prevent readers from questioning the credibility of the findings. It would also be valuable to clarify in the Conclusion that different types of stress may activate distinct ubiquitination pathways, highlighting context-dependent regulation of SG assembly and disassembly. * Authors: We thank the reviewer for this suggestion. We added to the discussion plausible explanations for why our study identified new E3 ligases.

• *

Line 59-60: when referring to the HECT family of E3 ligases involved in ubiquitination and SG disassembly, it would be more precise to report the specific E3 ligase identified in the cited studies rather than only the class of ligase. This would provide clearer mechanistic context and improve accuracy for readers. * Authors: We have added this detail to the discussion.

• *

The specific statement on line 182 "SG E3 ligases that depend on UBA1 activity are RBULs" should be supported by reference. * Authors: We have added citations to back up our claim that ZNF598, CNOT4, MKRN2, TRIM25 and TRIM26 exhibit RNA-binding activity.

*- Are the text and figures clear and accurate?

• In Supplementary Figure 1, DMSO is shown in green and the treatment in red, whereas in the main figures (Figure 1B and 1F) the colours in the legend are inverted. To avoid confusion, the colour coding in figure legends should be consistent across all figures throughout the manuscript. *

Authors: We have made the colors consistent across the main and supplementary figures.

• *

At line 79, the manuscript states that "inhibition of ubiquitination delayed fluorescence recovery dynamics of G3BP1-mCherry, relative to HS-treated cells (Figure 1F, Supplementary Fig. 6A)." However, the data shown in Figure 1F appear to indicate the opposite effect: the TAK243-treated condition (green curve) shows a faster fluorescence recovery compared to the control (red curve). This discrepancy between the text and the figure should be corrected or clarified, as it may affect the interpretation of the role of ubiquitination in SG dynamics. * Authors: Good catch. We now fixed the graphical mistake (Figure 1F and S6).

• * Line 86: adjust a missing bracket * Authors: Thank you, we fixed it.

• *

There appears to be an error in the legend of Supplementary Figure 3: the legend states that the red condition (MKRN2) forms larger aggregates, but both the main Figure 3C of the confocal images and the text indicate that MKRN2 (red) forms smaller aggregates. Please correct the legend and any corresponding labels so they are consistent with the main figure and the text. The authors should also double-check that the figure panel order, color coding, and statistical annotations match the legend and the descriptions in the Results section to avoid reader confusion.

* Authors: This unfortunate graphical mistake has been corrected.

• * At lines 129-130, the manuscript states that "FRAP analysis demonstrated that MKRN2 KD resulted in a slight increase in SG liquidity (Fig. 3F, Supplementary Fig. 6B)." However, the data shown in Figure 3F appear to indicate the opposite trend: the MKRN2 KD condition (red curve) exhibits a faster fluorescence recovery compared to the control (green curve). This discrepancy between the text and the figure should be corrected or clarified, as it directly affects the interpretation of MKRN2's role in SG disassembly. Ensuring consistency between the written description and the plotted FRAP data is essential for accurate interpretation. * Authors: We thank the reviewer and clarify in the legend of Figure 3F and the Results the correct labels: indeed faster fluorescence recovery seen in MKRN2 KD is correctly interpreted as increased liquidity in the text.

• *

At lines 132-133, the manuscript states: "Then, to further test the impact of MKRN2 on SG dynamics, we overexpressed MKRN2-GFP and observed that it was recruited to SG (Fig. 3G)." This description should be corrected or clarified, as the over-expressed MKRN2-GFP also appears to localize to the nucleus. * Authors: The text has been modified to reflect both the study of MKRN2 localization to SGs and of nuclear localization.

• *

At lines 134-135, the manuscript states that the FK2 antibody detects "free ubiquitin." This is incorrect. FK2 does not detect free ubiquitin; it recognizes only ubiquitin conjugates, including mono-ubiquitinated and poly-ubiquitinated proteins. The text should be corrected accordingly to avoid misinterpretation of the immunostaining data. * Authors: Thank you for pointing out this error. We have corrected it.

• * Figure 5A suffers from poor resolution, and no scale bar is provided, which limits interpretability. Additionally, the ROI selected for the green channel (DRIPs) appears to capture unspecific background staining, while the most obvious DRIP spots are localized in the nucleus. The authors should clarify this in the text, improve the image quality if possible, and ensure that the ROI accurately represents DRIP accumulation - in SGs rather than background signal. * Authors: We thank the reviewer for pointing the sub-optimal presentation of this figure. We modified Figure 5A to improve image quality and interpretation. Concerning the comment that “the most obvious DRIP spots are localized in the nucleus”, this is in line with our previous findings demonstrating that a fraction of DRiPs accumulates in nucleoli (Mediani et al. 2019 10.15252/embj.2018101341). To avoid misinterpretation, we modified Figure 5A as follows: (i) we provide a different image for control cells, exposed to heat shock and OP-puro; (ii) we select a ROI that only shows a few stress granules; (iii) we added arrowheads to indicate the nucleoli that are strongly enriched for DRiPs; (iv) we include a dotted line to show the nuclear membrane, helping to distinguish cytoplasm and nucleus in the red and green channel. We also include the scale bars (5 µm) in the image.

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

• In the first paragraph following the APEX proteomics results, the authors present validation data exclusively for MKRN2, justifying this early focus by stating that MKRN2 is the most SG-depleted E3 ligase. However, in the subsequent paragraph they introduce the RBULs and present knockdown data for MKRN2 along with two additional E3 ligases identified in the screen, before once again emphasizing that MKRN2 is the most SG-depleted ligase and therefore the main focus of the study. For clarity and logical flow, the manuscript would benefit from reordering the narrative. Specifically, the authors should first present the validation data for all three selected E3 ligases, and only then justify the decision to focus on MKRN2 for in-depth characterization. In addition to the extent of its SG depletion, the authors may also consider providing biologically relevant reasons for prioritizing MKRN2 (e.g., domain architecture, known roles in stress responses, or prior evidence of ubiquitination-related functions). Reorganizing this section would improve readability and better guide the reader through the rationale for the study's focus.*

Authors: We thank the reviewer for this suggested improvement to our “storyline”. As suggested by the reviewer, we have moved the IF validation of MKRN2 to the following paragraph in order to improve the flow of the manuscript. We added additional justification to prioritizing MKRN2 citing (Youn et al. 2018 and Markmiller et al. 2018).

• *

At lines 137-138, the manuscript states: "Together these data indicate that MKRN2 regulates the assembly dynamics of SGs by promoting their coalescence during HS and can increase SG ubiquitin content." While Figure 3G shows some co-localization of MKRN2 with ubiquitin, immunofluorescence alone is insufficient to claim an increase in SG ubiquitin content. This conclusion should be supported by orthogonal experiments, such as Western blotting, in vitro ubiquitination assays, or immunoprecipitation of SG components. Including a control under no-stress conditions would also help demonstrate that ubiquitination increases specifically in response to stress. The second part of the statement should therefore be rephrased to avoid overinterpretation, for example:"...and may be associated with increased ubiquitination within SGs, as suggested by co-localization, pending further validation by complementary assays." * Authors: The statement has been rephrased in a softer way as suggested by the reviewer.

• At line 157, the statement: "Therefore, we conclude that MKRN2 ubiquitinates a subset of DRiPs, avoiding their accumulation inside SGs" should be rephrased as a preliminary observation. While the data support a role for MKRN2 in SG disassembly and a reduction of DRIPs, direct ubiquitination of DRIPs by MKRN2 has not been demonstrated. A more cautious phrasing would better reflect the current evidence and avoid overinterpretation. * * *Authors: We thank the reviewer for this suggestion and have altered the phrasing of this statement accordingly.

*Reviewer #1 (Significance (Required)):

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

• This study provides a valuable advancement in understanding the role of ubiquitination in stress granule (SG) dynamics and the clearance of SGs formed under heat stress. A major strength is the demonstration of how E3 ligases identified through proteomic screening, particularly MKRN2, influence SG assembly and disassembly in a ubiquitination- and heat stress-dependent manner. The combination of proteomics, imaging, and functional assays provides a coherent mechanistic framework linking ubiquitination to SG homeostasis. Limitations of the study include the exclusive use of a single model system (U2OS cells), which may limit generalizability. Additionally, some observations-such as MKRN2-dependent ubiquitination within SGs and changes in DRIP accumulation under different conditions-would benefit from orthogonal validation experiments (e.g., Western blotting, immunoprecipitation, or in vitro assays) to confirm and strengthen these findings. Addressing these points would enhance the robustness and broader applicability of the conclusions.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

• The closest related result in literature is - Yang, Cuiwei et al. "Stress granule homeostasis is modulated by TRIM21-mediated ubiquitination of G3BP1 and autophagy-dependent elimination of stress granules." Autophagy vol. 19,7 (2023): 1934-1951. doi:10.1080/15548627.2022.2164427 - demonstrating that TRIM21, an E3 ubiquitin ligase, catalyzes K63-linked ubiquitination of G3BP1, a core SG nucleator, under oxidative stress. This ubiquitination by TRIM21 inhibits SG formation, likely by altering G3BP1's propensity for phase separation. In contrast, the MKRN2 study identifies a different E3 (MKRN2) that regulates SG dynamics under heat stress and appears to influence both assembly and disassembly. This expands the role of ubiquitin ligases in SG regulation beyond those previously studied (like TRIM21).

• Gwon and colleagues (Gwon Y, Maxwell BA, Kolaitis RM, Zhang P, Kim HJ, Taylor JP. Ubiquitination of G3BP1 mediates stress granule disassembly in a context-specific manner. Science. 2021;372(6549):eabf6548. doi:10.1126/science.abf6548) have shown that K63-linked ubiquitination of G3BP1 is required for SG disassembly after heat stress. This ubiquitinated G3BP1 recruits the segregase VCP/p97, which helps extract G3BP1 from SGs for disassembly. The MKRN2 paper builds on this by linking UBA1-dependent ubiquitination and MKRN2's activity to SG disassembly. Specifically, they show MKRN2 knockdown affects disassembly, and suggest MKRN2 helps prevent accumulation of defective ribosomal products (DRiPs) in SGs, adding a new layer to the ubiquitin-VCP model.

• Ubiquitination's impact is highly stress- and context-dependent (different chain types, ubiquitin linkages, and recruitment of E3s). The MKRN2 work conceptually strengthens this idea: by showing that MKRN2's engagement with SGs depends on active ubiquitination via UBA1, and by demonstrating functional consequences (SG dynamics + DRIP accumulation), the study highlights how cellular context (e.g., heat stress) can recruit specific ubiquitin ligases to SGs and modulate their behavior.

• There is a gap in the literature: very few (if any) studies explicitly combine the biology of DRIPs, stress granules, and E3 ligase mediated ubiquitination, especially in mammalian cells. There are relevant works about DRIP biology in stress granules, but those studies focus on chaperone-based quality control, not ubiquitin ligase-mediated ubiquitination of DRIPs. This study seems to be one of the first to make that connection in mammalian (or human-like) SG biology. A work on the plant DRIP-E3 ligase TaSAP5 (Zhang N, Yin Y, Liu X, et al. The E3 Ligase TaSAP5 Alters Drought Stress Responses by Promoting the Degradation of DRIP Proteins. Plant Physiol. 2017;175(4):1878-1892. doi:10.1104/pp.17.01319 ) shows that DRIPs can be directly ubiquitinated by E3s in other biological systems - which supports the plausibility of the MKRN2 mechanism, but it's not the same context.

• A very recent review (Yuan, Lin et al. "Stress granules: emerging players in neurodegenerative diseases." Translational neurodegeneration vol. 14,1 22. 12 May. 2025, doi:10.1186/s40035-025-00482-9) summarizes and reinforces the relationship among SGs and the pathogenesis of different neurodegenerative diseases (NDDs). By identifying MKRN2 as a new ubiquitin regulator in SGs, the current study could have relevance for neurodegeneration and proteotoxic diseases, providing a new candidate to explore in disease models.

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

The audience for this paper is primarily specialized, including researchers in stress granule biology, ubiquitin signaling, protein quality control, ribosome biology, and cellular stress responses. The findings will also be of interest to scientists working on granulostasis, nascent protein surveillance, and proteostasis mechanisms. Beyond these specific fields, the study provides preliminary evidence linking ubiquitination to DRIP handling and SG dynamics, which may stimulate new research directions and collaborative efforts across complementary areas of cell biology and molecular biology.

• Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I work in ubiquitin biology, focusing on ubiquitination signaling in physiological and disease contexts, with particular expertise in the identification of E3 ligases and their substrates across different cellular systems and in vivo models. I have less expertise in stress granule dynamics and DRiP biology, so my evaluation of those aspects is more limited and relies on interpretation of the data presented in the manuscript.

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

This study identifies the E3 ubiquitin ligase Makorin 2 (MKRN2) as a novel regulator of stress granule (SG) dynamics and proteostasis. Using APEX proximity proteomics, the authors demonstrate that inhibition of the ubiquitin-activating enzyme UBA1 with TAK243 alters the SG proteome, leading to depletion of several E3 ligases, chaperones, and VCP cofactors. Detailed characterization of MKRN2 reveals that it localizes to SGs in a ubiquitination-dependent manner and is required for proper SG assembly, coalescence, and disassembly. Functionally, MKRN2 prevents the accumulation of defective ribosomal products (DRiPs) within SGs, thereby maintaining granulostasis. The study provides compelling evidence that ubiquitination, mediated specifically by MKRN2, plays a critical role in surveilling stress-damaged proteins within SGs and maintaining their dynamic liquid-like properties. Major issues: 1. Figures 1-2: Temporal dynamics of ubiquitination in SGs. The APEX proteomics was performed at a single timepoint (90 min heat stress), yet the live imaging data show that SG dynamics and TAK243 effects vary considerably over time: • The peak or SG nucleation was actually at 10-30 min (Figure 1B). • TAK243 treatment causes earlier SG nucleation (Figure 1B) but delayed disassembly (Figure 1A-B, D). A temporal proteomic analysis at multiple timepoints (e.g., 30 min, 60 min, 90 min of heat stress, and during recovery) would reveal whether MKRN2 and other ubiquitination-dependent proteins are recruited to SGs dynamically during the stress response. It would also delineate whether different E3 ligases predominate at different stages of the SG lifecycle. While such experiments may be beyond the scope of the current study, the authors should at minimum discuss this limitation and acknowledge that the single-timepoint analysis may miss dynamic changes in SG composition. *

Authors: We thank the reviewer for identifying this caveat in our methodology. We now discuss this limitation and acknowledge that the single-timepoint analysis may miss dynamic changes in SG composition.

* Figures 2D-E, 3G: MKRN2 localization mechanism requires clarification. The authors demonstrate that MKRN2 localization to SGs is dependent on active ubiquitination, as TAK243 treatment significantly reduces MKRN2 partitioning into SGs (Figure 2D-E). However, several mechanistic questions remain: • Does MKRN2 localize to SGs through binding to ubiquitinated substrates within SGs, or does MKRN2 require its own ubiquitination activity to enter SGs? • The observation that MKRN2 overexpression increases SG ubiquitin content (Figure 3G-H) could indicate either: (a) MKRN2 actively ubiquitinates substrates within SGs, or (b) MKRN2 recruitment brings along pre-ubiquitinated substrates from the cytoplasm. • Is MKRN2 localization to SGs dependent on its E3 ligase activity? A catalytically inactive mutant of MKRN2 would help distinguish whether MKRN2 must actively ubiquitinate proteins to remain in SGs or whether it binds to ubiquitinated proteins independently of its catalytic activity. The authors should clarify whether MKRN2's SG localization depends on its catalytic activity or on binding to ubiquitinated proteins, as this would fundamentally affect the interpretation of its role in SG dynamics. *

Authors: We thank the reviewer for this experimental suggestion. We will perform an analysis of the SG partitioning coefficient between WT-MKRN2 and a RING mutant of MKRN2.

* Figures 3-4: Discrepancy between assembly and disassembly phenotypes. MKRN2 knockdown produces distinct phenotypes during SG assembly versus disassembly. During assembly: smaller, more numerous SGs that fail to coalesce (Figure 3A-E), while during disassembly: delayed SG clearance (Figure 4A-D). These phenotypes may reflect different roles for MKRN2 at different stages, but the mechanism underlying this stage-specificity is unclear: • Does MKRN2 have different substrates or utilize different ubiquitin chain types during assembly versus disassembly? • The increased SG liquidity upon MKRN2 depletion (Figure 3F) seems paradoxical with delayed disassembly- typically more liquid condensates disassemble faster. The authors interpret this as decreased coalescence into "dense and mature SGs," but this requires clarification. • How does prevention of DRiP accumulation relate to the assembly defect? One would predict that DRiP accumulation would primarily affect disassembly (by reducing liquidity), yet MKRN2 depletion impacts both assembly dynamics and DRiP accumulation. The authors should discuss how MKRN2's role in preventing DRiP accumulation mechanistically connects to both the assembly and disassembly phenotypes. *

Authors: We thank the reviewer and will add to the Discussion a mention of a precedent for this precise phenotype from our previous work (Seguin et al., 2014).

* Figure 5: Incomplete characterization of MKRN2 substrates. While the authors convincingly demonstrate that MKRN2 prevents DRiP accumulation in SGs (Figure 5C-D), the direct substrates of MKRN2 remain unknown. The authors acknowledge in the limitations that "the direct MKRN2 substrates and ubiquitin-chain types (K63/K48) are currently unknown." However, several approaches could strengthen the mechanistic understanding: • Do DRiPs represent direct MKRN2 substrates? Co-immunoprecipitation of MKRN2 followed by ubiquitin-chain specific antibodies (K48 vs K63) could reveal whether MKRN2 mediates degradative (K48) or non-degradative (K63) ubiquitination. *

Authors: The DRiPs generated in the study represent truncated versions of all the proteins that were in the process of being synthesized by the cell at the moment of the stress, and therefore include both MKRN2 specific substrates and MKRN2 independent substrates. Identifying specific MKRN2 substrates, while interesting as a new research avenue, is not within the scope of the present study.

• * Given that VCP cofactors (such as UFD1L, PLAA) are depleted from SGs upon UBA1 inhibition (Figure 2C) and these cofactors recognize ubiquitinated substrates, does MKRN2 function upstream of VCP recruitment? Testing whether MKRN2 depletion affects VCP cofactor localization to SGs would clarify this pathway. * Authors: We thank the reviewer for requesting and will address it by performing MKRN2 KD, VCP immunofluorescence microscopy and perform SG partition coefficient analysis.

• * The authors note that MKRN2 knockdown produces a phenotype reminiscent of VCP inhibition-smaller, more numerous SGs with increased DRiP partitioning. This similarity suggests MKRN2 may function in the same pathway as VCP. Direct epistasis experiments would strengthen this connection. * Authors: This study is conditional results of the above study. If VCP partitioning to SGs is reduced upon MKRN2 KD, which we do not know at this point, then MKRN2/VCP double KD experiment will be performed to strengthen this connection.

* Alternative explanations for the phenotype of delayed disassembly with TAK243 or MKRN2 depletion- the authors attribute this to DRiP accumulation, but TAK243 affects global ubiquitination. Could impaired degradation of other SG proteins (not just DRiPs) contribute to delayed disassembly? Does proteasome inhibition (MG-132 treatment) phenocopy the MKRN2 depletion phenotype? This would support that MKRN2-mediated proteasomal degradation (via K48 ubiquitin chains) is key to the phenotype. *

Authors: We are happy to provide alternative explanations in the Discussion in line with Reviewer #2 suggestion. The role of the proteosome is out of the scope of our study.

• Comparison with other E3 ligases (Supplementary Figure 5): The authors show that CNOT4 and ZNF598 depletion also affect SG dynamics, though to lesser extents than MKRN2. However: • Do these E3 ligases also prevent DRiP accumulation in SGs? Testing OP-puro partitioning in CNOT4- or ZNF598-depleted cells would reveal whether DRiP clearance is a general feature of SG-localized E3 ligases or specific to MKRN2. *

• * Are there redundant or compensatory relationships between these E3 ligases? Do double knockdowns have additive effects? * Authors: Our paper presents a study of the E3 ligase MKRN2. Generalizing these observations to ZNF598, CNOT4 and perhaps an even longer list of E3s, may be an interesting question, outside the scope of our mission.

• * The authors note that MKRN2 is "the most highly SG-depleted E3 upon TAK243 treatment"-does this mean MKRN2 has the strongest dependence on active ubiquitination for its SG localization, or simply that it has the highest basal level of SG partitioning? * Authors: We thank the reviewer for this smart question. MKRN2 has the strongest dependence on active ubiquitination as we now clarify better in the Results.

*Reviewer #2 (Significance (Required)):

This is a well-executed study that identifies MKRN2 as an important regulator of stress granule dynamics and proteostasis. The combination of proximity proteomics, live imaging, and functional assays provides strong evidence for MKRN2's role in preventing DRiP accumulation and maintaining granulostasis. However, key mechanistic questions remain, particularly regarding MKRN2's direct substrates, the ubiquitin chain types it generates, and how its enzymatic activity specifically prevents DRiP accumulation while promoting both SG coalescence and disassembly. Addressing the suggested revisions, particularly those related to MKRN2's mechanism of SG localization and substrate specificity, would significantly strengthen the manuscript and provide clearer insights into how ubiquitination maintains the dynamic properties of stress granules under proteotoxic stress.

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

In this paper, Amzallag et al. investigate the relationship between ubiquitination and the dynamics of stress granules (SGs). They utilize proximity ligation coupled mass spectrometry to identify SG components under conditions where the proteasome is inhibited by a small drug that targets UBiquitin-like modifier Activating enzyme 1 (UBA1), which is crucial for the initial step in the ubiquitination of misfolded proteins. Their findings reveal that the E3 ligase Makorin2 (MKRN2) is a novel component of SGs. Additionally, their data suggest that MKRN2 is necessary for processing damaged ribosome-associated proteins (DRIPs) during heat shock (HS). In the absence of MKRN2, DRIPs accumulate in SGs, which affects their dynamics. Major comments: Assess the knockdown efficiency (KD) for CNOT1, ZNF598, and MKRN2 to determine if the significant effect observed on SG dynamics upon MKRN2 depletion is due to the protein's function rather than any possible differences in KD efficiency. *

Authors: To address potential variability in knockdown efficiency, we will quantify CNOT4, ZNF598, and MKRN2 mRNA levels by RT-qPCR following siRNA knockdown.

* Since HS-induced stress granules (SGs) are influenced by the presence of TAK-243 or MKRN2 depletion, could it be that these granules become more mature and thus acquire more defective ribosomal products (DRIPs)? Do HS cells reach the same level of DRIPs, as assessed by OP-Puro staining, at a later time point? *

Authors: an interesting question. Mateju et al. carefully characterized the time course of DRiP accumulation in stress granules during heat shock, decreasing after the 90 minutes point (Appendix Figure S7; 10.15252/embj.201695957). We therefore interpret DRiP accumulation in stress granules following TAK243 treatment as a pathological state, reflecting impaired removal and degradation of DRiPs, rather than a normal, more “mature” stress granule state.

* Incorporating OP-Puro can lead to premature translation termination, potentially confounding results. Consider treating cells with a short pulse (i.e., 5 minutes) of OP-Puro just before fixation. *

Authors: Thank you for this suggestion. Treating the cell with a short pulse of OP-Puro just before fixation will lead to the labelling of a small amount of proteins, likely undetectable using conventional microscopy or Western blotting. Furthermore, it will lead to the unwanted labeling of stress responsive proteins that are translated with non canonical cap-independent mechanisms upon stress.

* Is MKRN2's dependence limited to HS-induced SGs? *

Authors: We will test sodium arsenite–induced stress and use immunofluorescence at discrete time points to assess whether the heat shock–related observations generalize to other stress types.

*

Minor comments: Abstract: Introduce UBA1. Introduction: The reference [2] should be replaced with 25719440. Results: Line 70, 'G3BP1 and 2 genes,' is somewhat misleading. Consider rephrasing into 'G3BP1 and G3BP2 genes'. Line 103: considers rephrasing 'we orthogonally validated the ubiquitin-dependent interaction' to 'we orthogonally validated the ubiquitin-dependent stress granule localization'. Line 125: '(fig.3C, EI Supplementary fig. 3)' Remove 'I'. Methods: line 260: the reference is not linked (it should be ref. [26]). Line 225: Are all the KDs being performed using the same method? Please specify. *

Authors: The text has been altered to reflect the reviewer’s suggestions.

*Fig.2C: Consider adding 'DEPLETED' on top of the scheme.

Reviewer #3 (Significance (Required)):

The study offers valuable insights into the degradative processes associated with SGs. The figures are clear, and the experimental quality is high. The authors do not overstate or overinterpret their findings, and the results effectively support their claims. However, the study lacks orthogonal methods to validate the findings and enhance the results. For instance, incorporating biochemical and reporter-based methods to measure degradation-related intermediate products (DRIPs) would be beneficial. Additionally, utilizing multiple methods to block ubiquitination, studying the dynamics of MKRN2 on SGs, and examining the consequences of excessive DRIPs on the cell fitness of SGs would further strengthen the research. *

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Referee #3

Evidence, reproducibility and clarity

In this paper, Amzallag et al. investigate the relationship between ubiquitination and the dynamics of stress granules (SGs). They utilize proximity ligation coupled mass spectrometry to identify SG components under conditions where the proteasome is inhibited by a small drug that targets UBiquitin-like modifier Activating enzyme 1 (UBA1), which is crucial for the initial step in the ubiquitination of misfolded proteins. Their findings reveal that the E3 ligase Makorin2 (MKRN2) is a novel component of SGs. Additionally, their data suggest that MKRN2 is necessary for processing damaged ribosome-associated proteins (DRIPs) during heat shock (HS). In the absence of MKRN2, DRIPs accumulate in SGs, which affects their dynamics.

Major comments:

Assess the knockdown efficiency (KD) for CNOT1, ZNF598, and MKRN2 to determine if the significant effect observed on SG dynamics upon MKRN2 depletion is due to the protein's function rather than any possible differences in KD efficiency. Since HS-induced stress granules (SGs) are influenced by the presence of TAK-243 or MKRN2 depletion, could it be that these granules become more mature and thus acquire more defective ribosomal products (DRIPs)? Do HS cells reach the same level of DRIPs, as assessed by OP-Puro staining, at a later time point? Incorporating OP-Puro can lead to premature translation termination, potentially confounding results. Consider treating cells with a short pulse (i.e., 5 minutes) of OP-Puro just before fixation. Is MKRN2's dependence limited to HS-induced SGs?

Minor comments:

Abstract:

Introduce UBA1. Introduction:

The reference [2] should be replaced with 25719440.

Results:

Line 70, 'G3BP1 and 2 genes,' is somewhat misleading. Consider rephrasing into 'G3BP1 and G3BP2 genes'. Line 103: considers rephrasing 'we orthogonally validated the ubiquitin-dependent interaction' to 'we orthogonally validated the ubiquitin-dependent stress granule localization'. Line 125: '(fig.3C, EI Supplementary fig. 3)' Remove 'I'. Methods:

line 260: the reference is not linked (it should be ref. [26]). Line 225: Are all the KDs being performed using the same method? Please specify.

Fig.2C: Consider adding 'DEPLETED' on top of the scheme.

Significance

The study offers valuable insights into the degradative processes associated with SGs. The figures are clear, and the experimental quality is high. The authors do not overstate or overinterpret their findings, and the results effectively support their claims. However, the study lacks orthogonal methods to validate the findings and enhance the results. For instance, incorporating biochemical and reporter-based methods to measure degradation-related intermediate products (DRIPs) would be beneficial. Additionally, utilizing multiple methods to block ubiquitination, studying the dynamics of MKRN2 on SGs, and examining the consequences of excessive DRIPs on the cell fitness of SGs would further strengthen the research.

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Referee #2

Evidence, reproducibility and clarity

This study identifies the E3 ubiquitin ligase Makorin 2 (MKRN2) as a novel regulator of stress granule (SG) dynamics and proteostasis. Using APEX proximity proteomics, the authors demonstrate that inhibition of the ubiquitin-activating enzyme UBA1 with TAK243 alters the SG proteome, leading to depletion of several E3 ligases, chaperones, and VCP cofactors. Detailed characterization of MKRN2 reveals that it localizes to SGs in a ubiquitination-dependent manner and is required for proper SG assembly, coalescence, and disassembly. Functionally, MKRN2 prevents the accumulation of defective ribosomal products (DRiPs) within SGs, thereby maintaining granulostasis. The study provides compelling evidence that ubiquitination, mediated specifically by MKRN2, plays a critical role in surveilling stress-damaged proteins within SGs and maintaining their dynamic liquid-like properties.

Major issues:

1. Figures 1-2: Temporal dynamics of ubiquitination in SGs. The APEX proteomics was performed at a single timepoint (90 min heat stress), yet the live imaging data show that SG dynamics and TAK243 effects vary considerably over time:
   • The peak or SG nucleation was actually at 10-30 min (Figure 1B).
   • TAK243 treatment causes earlier SG nucleation (Figure 1B) but delayed disassembly (Figure 1A-B, D). A temporal proteomic analysis at multiple timepoints (e.g., 30 min, 60 min, 90 min of heat stress, and during recovery) would reveal whether MKRN2 and other ubiquitination-dependent proteins are recruited to SGs dynamically during the stress response. It would also delineate whether different E3 ligases predominate at different stages of the SG lifecycle. While such experiments may be beyond the scope of the current study, the authors should at minimum discuss this limitation and acknowledge that the single-timepoint analysis may miss dynamic changes in SG composition.
2. Figures 2D-E, 3G: MKRN2 localization mechanism requires clarification. The authors demonstrate that MKRN2 localization to SGs is dependent on active ubiquitination, as TAK243 treatment significantly reduces MKRN2 partitioning into SGs (Figure 2D-E). However, several mechanistic questions remain:
   • Does MKRN2 localize to SGs through binding to ubiquitinated substrates within SGs, or does MKRN2 require its own ubiquitination activity to enter SGs?
   • The observation that MKRN2 overexpression increases SG ubiquitin content (Figure 3G-H) could indicate either: (a) MKRN2 actively ubiquitinates substrates within SGs, or (b) MKRN2 recruitment brings along pre-ubiquitinated substrates from the cytoplasm.
   • Is MKRN2 localization to SGs dependent on its E3 ligase activity? A catalytically inactive mutant of MKRN2 would help distinguish whether MKRN2 must actively ubiquitinate proteins to remain in SGs or whether it binds to ubiquitinated proteins independently of its catalytic activity. The authors should clarify whether MKRN2's SG localization depends on its catalytic activity or on binding to ubiquitinated proteins, as this would fundamentally affect the interpretation of its role in SG dynamics.
3. Figures 3-4: Discrepancy between assembly and disassembly phenotypes. MKRN2 knockdown produces distinct phenotypes during SG assembly versus disassembly. During assembly: smaller, more numerous SGs that fail to coalesce (Figure 3A-E), while during disassembly: delayed SG clearance (Figure 4A-D). These phenotypes may reflect different roles for MKRN2 at different stages, but the mechanism underlying this stage-specificity is unclear:
   • Does MKRN2 have different substrates or utilize different ubiquitin chain types during assembly versus disassembly?
   • The increased SG liquidity upon MKRN2 depletion (Figure 3F) seems paradoxical with delayed disassembly- typically more liquid condensates disassemble faster. The authors interpret this as decreased coalescence into "dense and mature SGs," but this requires clarification.
   • How does prevention of DRiP accumulation relate to the assembly defect? One would predict that DRiP accumulation would primarily affect disassembly (by reducing liquidity), yet MKRN2 depletion impacts both assembly dynamics and DRiP accumulation. The authors should discuss how MKRN2's role in preventing DRiP accumulation mechanistically connects to both the assembly and disassembly phenotypes.
4. Figure 5: Incomplete characterization of MKRN2 substrates. While the authors convincingly demonstrate that MKRN2 prevents DRiP accumulation in SGs (Figure 5C-D), the direct substrates of MKRN2 remain unknown. The authors acknowledge in the limitations that "the direct MKRN2 substrates and ubiquitin-chain types (K63/K48) are currently unknown." However, several approaches could strengthen the mechanistic understanding:
   • Do DRiPs represent direct MKRN2 substrates? Co-immunoprecipitation of MKRN2 followed by ubiquitin-chain specific antibodies (K48 vs K63) could reveal whether MKRN2 mediates degradative (K48) or non-degradative (K63) ubiquitination.
   • Given that VCP cofactors (such as UFD1L, PLAA) are depleted from SGs upon UBA1 inhibition (Figure 2C) and these cofactors recognize ubiquitinated substrates, does MKRN2 function upstream of VCP recruitment? Testing whether MKRN2 depletion affects VCP cofactor localization to SGs would clarify this pathway.
   • The authors note that MKRN2 knockdown produces a phenotype reminiscent of VCP inhibition-smaller, more numerous SGs with increased DRiP partitioning. This similarity suggests MKRN2 may function in the same pathway as VCP. Direct epistasis experiments would strengthen this connection.
5. Alternative explanations for the phenotype of delayed disassembly with TAK243 or MKRN2 depletion- the authors attribute this to DRiP accumulation, but TAK243 affects global ubiquitination. Could impaired degradation of other SG proteins (not just DRiPs) contribute to delayed disassembly? Does proteasome inhibition (MG-132 treatment) phenocopy the MKRN2 depletion phenotype? This would support that MKRN2-mediated proteasomal degradation (via K48 ubiquitin chains) is key to the phenotype.
6. Comparison with other E3 ligases (Supplementary Figure 5): The authors show that CNOT4 and ZNF598 depletion also affect SG dynamics, though to lesser extents than MKRN2. However:
   • Do these E3 ligases also prevent DRiP accumulation in SGs? Testing OP-puro partitioning in CNOT4- or ZNF598-depleted cells would reveal whether DRiP clearance is a general feature of SG-localized E3 ligases or specific to MKRN2.
   • Are there redundant or compensatory relationships between these E3 ligases? Do double knockdowns have additive effects?
   • The authors note that MKRN2 is "the most highly SG-depleted E3 upon TAK243 treatment"-does this mean MKRN2 has the strongest dependence on active ubiquitination for its SG localization, or simply that it has the highest basal level of SG partitioning?

Significance

This is a well-executed study that identifies MKRN2 as an important regulator of stress granule dynamics and proteostasis. The combination of proximity proteomics, live imaging, and functional assays provides strong evidence for MKRN2's role in preventing DRiP accumulation and maintaining granulostasis. However, key mechanistic questions remain, particularly regarding MKRN2's direct substrates, the ubiquitin chain types it generates, and how its enzymatic activity specifically prevents DRiP accumulation while promoting both SG coalescence and disassembly. Addressing the suggested revisions, particularly those related to MKRN2's mechanism of SG localization and substrate specificity, would significantly strengthen the manuscript and provide clearer insights into how ubiquitination maintains the dynamic properties of stress granules under proteotoxic stress.

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

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, the authors used proximity proteomics in U2OS cells to identify several E3 ubiquitin ligases recruited to stress granules (SGs), and they focused on MKRN2 as a novel regulator. They show that MKRN2 localization to SGs requires active ubiquitination via UBA1. Functional experiments demonstrated that MKRN2 knockdown increases the number of SG condensates, reduces their size, slightly raises SG liquidity during assembly, and slows disassembly after heat shock. Overexpression of MKRN2-GFP combined with confocal imaging revealed co-localization of MKRN2 and ubiquitin in SGs. By perturbing ubiquitination (using a UBA1 inhibitor) and inducing defective ribosomal products (DRiPs) with O-propargyl puromycin, they found that both ubiquitination inhibition and MKRN2 depletion lead to increased accumulation of DRiPs in SGs. The authors conclude that MKRN2 supports granulostasis, the maintenance of SG homeostasis , through its ubiquitin ligase activity, preventing pathological DRiP accumulation within SGs.

Major comments:

• Are the key conclusions convincing?

The key conclusions are partially convincing. The data supporting the role of ubiquitination and MKRN2 in regulating SG condensate dynamics are coherent, well controlled, and consistent with previous literature, making this part of the study solid and credible. However, the conclusions regarding the ubiquitin-dependent recruitment of MKRN2 to SGs, its relationship with UBA1 activity, the functional impact of the MKRN2 knockdown for DRiP accumulation are less thoroughly supported. These aspects would benefit from additional mechanistic evidence, validation in complementary model systems, or the use of alternative methodological approaches to strengthen the causal connections drawn by the authors. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The authors should qualify some of their claims as preliminary.

1) MKRN2 recruitment to SGs (ubiquitin-dependent): The proteomics and IF data are a reasonable starting point, but they do not yet establish that MKRN2 is recruited from its physiological localization to SGs in a ubiquitin-dependent manner. To avoid overstating this point the authors should qualify the claim and/or provide additional controls: show baseline localization of endogenous MKRN2 under non-stress conditions (which is reported in literature to be nuclear and cytoplasmatic), include quantification of nuclear/cytoplasmic distribution, and demonstrate a shift into bona fide SG compartments after heat shock. Moreover, co-localization of overexpressed GFP-MKRN2 with poly-Ub (FK2) should be compared to a non-stress control and to UBA1-inhibition conditions to support claims of stress- and ubiquitination-dependent recruitment.

2) Use and interpretation of UBA1 inhibition: UBA1 inhibition effectively blocks ubiquitination globally, but it is non-selective. The manuscript should explicitly acknowledge this limitation when interpreting results from both proteomics and functional assays. Proteomics hits identified under UBA1 inhibition should be discussed as UBA1-dependent associations rather than as evidence for specific E3 ligase recruitment. The authors should consider orthogonal approaches before concluding specificity.

3) DRiP accumulation and imaging quality: The evidence presented in Figure 5 is sufficient to substantiate the claim that DRiPs accumulate in SGs upon ubiquitination inhibition or MKRN2 depletion but to show that the event of the SGs localization and their clearance from SGs during stress is promoted by MKRN3 ubiquitin ligase activity more experiments would be needed. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. Yes, a few targeted experiments would strengthen the conclusions without requiring the authors to open new lines of investigation.

1) Baseline localization of MKRN2: It would be important to show the baseline localization of endogenous and over-expressed MKRN2 (nuclear and cytoplasmic) under non-stress conditions and prior to ubiquitination inhibition. This would provide a reference to quantify redistribution into SGs and demonstrate recruitment in response to heat stress or ubiquitination-dependent mechanisms.

2) Specificity of MKRN2 ubiquitin ligase activity: to address the non-specific effects of UBA1 inhibition and validate that observed phenotypes depend on MKRN2's ligase activity, the authors could employ a catalytically inactive MKRN2 mutant in rescue experiments. Comparing wild-type and catalytic-dead MKRN2 in the knockdown background would clarify the causal role of MKRN2 activity in SG dynamics and DRiP clearance.

3) Ubiquitination linkage and SG marker levels: While the specific ubiquitin linkage type remains unknown, examining whether MKRN2 knockdown or overexpression affects total levels of key SG marker proteins would be informative. This could be done via Western blotting of SG markers along with ubiquitin staining, to assess whether MKRN2 influences protein stability or turnover through degradative or non-degradative ubiquitination. Such data would strengthen the mechanistic interpretation while remaining within the current study's scope. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. The experiments suggested in points 1 and 3 are realistic and should not require substantial additional resources beyond those already used in the study. - Point 1 (baseline localization of MKRN2): This involves adding two control conditions (no stress and no ubiquitination inhibition) for microscopy imaging. The setup is essentially the same as in the current experiments, with time requirements mainly dependent on cell culture growth and imaging. Overall, this could be completed within a few weeks. - Point 3 (SG marker levels and ubiquitination): This entails repeating the existing experiment and adding a Western blot for SG markers and ubiquitin. The lab should already have the necessary antibodies, and the experiment could reasonably be performed within a couple of weeks. - Point 2 (catalytically inactive MKRN2 mutant and rescue experiments): This is likely more time-consuming. Designing an effective catalytic-dead mutant depends on structural knowledge of MKRN2 and may require additional validation to confirm loss of catalytic activity. If this expertise is not already present in the lab, it could significantly extend the timeline. Therefore, this experiment should be considered only if similarly recommended by other reviewers, as it represents a higher resource and time investment.

Overall, points 1 and 3 are highly feasible, while point 2 is more substantial and may require careful planning. - Are the data and the methods presented in such a way that they can be reproduced?

Yes. The methodologies used in this study to analyze SG dynamics and DRiP accumulation are well-established in the field and should be reproducible, particularly by researchers experienced in stress granule biology. Techniques such as SG assembly and disassembly assays, use of G3BP1 markers, and UBA1 inhibition are standard and clearly described. The data are generally presented in a reproducible manner; however, as noted above, some results would benefit from additional controls or complementary experiments to fully support specific conclusions. - Are the experiments adequately replicated and statistical analysis adequate?

Overall, the experiments in the manuscript appear to be adequately replicated, with most assays repeated between three and five times, as indicated in the supplementary materials. The statistical analyses used are appropriate and correctly applied to the datasets presented. However, for Figure 5 the number of experimental replicates is not reported. This should be clarified, and if the experiment was not repeated sufficiently, additional biological replicates should be performed. Given that this figure provides central evidence supporting the conclusion that DRiP accumulation depends on ubiquitination-and partly on MKRN2's ubiquitin ligase activity-adequate replication is essential.

Minor comments:

• Specific experimental issues that are easily addressable.
  • For the generation and the validation of MKRN2 knockdown in UOS2 cells data are not presented in the results or in the methods sections to demonstrate the effective knockdown of the protein of interest. This point is quite essential to demonstrate the validity of the system used
  • In the supplementary figure 2 it would be useful to mention if the Western Blot represent the input (total cell lysates) before the APEX-pulldown or if it is the APEX-pulldown loaded for WB. There is no consistence in the difference of biotynilation between different replicates shown in the 2 blots. For example in R1 and R2 G3BP1-APX TAK243 the biotynilation is one if the strongest condition while on the left blot, in the same condition comparison samples R3 and R4 are less biotinilated compared to others. It would be useful to provide an explanation for that to avoid any confusion for the readers.
  • In Figure 2D, endogenous MKRN2 localization to SGs appears reduced following UBA1 inhibition. However, it is not clear whether this reduction reflects a true relocalization or a decrease in total MKRN2 protein levels. To support the interpretation that UBA1 inhibition specifically affects MKRN2 recruitment to SGs rather than its overall expression, the authors should provide data showing total MKRN2 levels remain unchanged under UBA1 inhibition, for example via Western blot of total cell lysates.
  • DRIPs accumulation is followed during assembly but in the introduction is highlighted the fact that ubiquitination events, other reported E3 ligases and in this study data on MKRN2 showed that they play a crucial role in the disassembly of SGs which is also related with cleareance of DRIPs. Authors could add tracking DRIPs accumulation during disassembly to be added to Figure 5. I am not sure about the timeline required for this but I am just adding as optional if could be addressed easily.
  • The authors should clarify in the text why the cutoff used for the quantification in Figure 5D (PC > 3) differs from the cutoff used elsewhere in the paper (PC > 1.5). Providing a rationale for this choice will help the reader understand the methodological consistency and ensure that differences in thresholds do not confound interpretation of the results.
  • For Figure 3G, the authors use over-expressed MKRN2-GFP to assess co-localization with ubiquitin in SGs. Given that a reliable antibody for endogenous MKRN2 is available and that a validated MKRN2 knockdown line exists as an appropriate control, this experiment would gain significantly in robustness and interpretability if co-localization were demonstrated using endogenous MKRN2. In the current over-expression system, MKRN2-GFP is also present in the nucleus, whereas the endogenous protein does not appear nuclear under the conditions shown. This discrepancy raises concerns about potential over-expression artifacts or mislocalization. Demonstrating co-localization using endogenous MKRN2 would avoid confounding effects associated with over-expression. If feasible, this would be a relatively straightforward experiment to implement, as it relies on tools (antibody and knockdown line) already described in the manuscript.

• Are prior studies referenced appropriately?

  • From line 54 to line 67, the manuscript in total cites eight papers regarding the role of ubiquitination in SG disassembly. However, given the use of UBA1 inhibition in the initial MS-APEX experiment and the extensive prior literature on ubiquitination in SG assembly and disassembly under various stress conditions, the manuscript would benefit from citing additional relevant studies to provide more specifc examples. Expanding the references would provide stronger context, better connect the current findings to prior work, and emphasize the significance of the study in relation to established literature
  • At line 59, it would be helpful to note that G3BP1 is ubiquitinated by TRIM21 through a Lys63-linked ubiquitin chain. This information provides important mechanistic context, suggesting that ubiquitination of SG proteins in these pathways is likely non-degradative and related to functional regulation of SG dynamics rather than protein turnover.
  • When citing references 16 and 17, which report that the E3 ligases TRIM21 and HECT regulate SG formation, the authors should provide a plausible explanation for why these specific E3 ligases were not detected in their proteomics experiments. Differences could arise from the stress stimulus used, cell type, or experimental conditions. Similarly, since MKRN2 and other E3 ligases identified in this study have not been reported in previous works, discussing these methodological or biological differences would help prevent readers from questioning the credibility of the findings. It would also be valuable to clarify in the Conclusion that different types of stress may activate distinct ubiquitination pathways, highlighting context-dependent regulation of SG assembly and disassembly.
  • Line 59-60: when referring to the HECT family of E3 ligases involved in ubiquitination and SG disassembly, it would be more precise to report the specific E3 ligase identified in the cited studies rather than only the class of ligase. This would provide clearer mechanistic context and improve accuracy for readers.
  • The specific statement on line 182 "SG E3 ligases that depend on UBA1 activity are RBULs" should be supported by reference.
  • Are the text and figures clear and accurate?
  • In Supplementary Figure 1, DMSO is shown in green and the treatment in red, whereas in the main figures (Figure 1B and 1F) the colours in the legend are inverted. To avoid confusion, the colour coding in figure legends should be consistent across all figures throughout the manuscript.
  • At line 79, the manuscript states that "inhibition of ubiquitination delayed fluorescence recovery dynamics of G3BP1-mCherry, relative to HS-treated cells (Figure 1F, Supplementary Fig. 6A)." However, the data shown in Figure 1F appear to indicate the opposite effect: the TAK243-treated condition (green curve) shows a faster fluorescence recovery compared to the control (red curve). This discrepancy between the text and the figure should be corrected or clarified, as it may affect the interpretation of the role of ubiquitination in SG dynamics.
  • Line 86: adjust a missing bracket
  • There appears to be an error in the legend of Supplementary Figure 3: the legend states that the red condition (MKRN2) forms larger aggregates, but both the main Figure 3C of the confocal images and the text indicate that MKRN2 (red) forms smaller aggregates. Please correct the legend and any corresponding labels so they are consistent with the main figure and the text. The authors should also double-check that the figure panel order, color coding, and statistical annotations match the legend and the descriptions in the Results section to avoid reader confusion.
  • At lines 129-130, the manuscript states that "FRAP analysis demonstrated that MKRN2 KD resulted in a slight increase in SG liquidity (Fig. 3F, Supplementary Fig. 6B)." However, the data shown in Figure 3F appear to indicate the opposite trend: the MKRN2 KD condition (red curve) exhibits a faster fluorescence recovery compared to the control (green curve). This discrepancy between the text and the figure should be corrected or clarified, as it directly affects the interpretation of MKRN2's role in SG disassembly. Ensuring consistency between the written description and the plotted FRAP data is essential for accurate interpretation.
  • At lines 132-133, the manuscript states: "Then, to further test the impact of MKRN2 on SG dynamics, we overexpressed MKRN2-GFP and observed that it was recruited to SG (Fig. 3G)." This description should be corrected or clarified, as the over-expressed MKRN2-GFP also appears to localize to the nucleus.
  • At lines 134-135, the manuscript states that the FK2 antibody detects "free ubiquitin." This is incorrect. FK2 does not detect free ubiquitin; it recognizes only ubiquitin conjugates, including mono-ubiquitinated and poly-ubiquitinated proteins. The text should be corrected accordingly to avoid misinterpretation of the immunostaining data.
  • Figure 5A suffers from poor resolution, and no scale bar is provided, which limits interpretability. Additionally, the ROI selected for the green channel (DRIPs) appears to capture unspecific background staining, while the most obvious DRIP spots are localized in the nucleus. The authors should clarify this in the text, improve the image quality if possible, and ensure that the ROI accurately represents DRIP accumulation - in SGs rather than background signal.

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

• In the first paragraph following the APEX proteomics results, the authors present validation data exclusively for MKRN2, justifying this early focus by stating that MKRN2 is the most SG-depleted E3 ligase. However, in the subsequent paragraph they introduce the RBULs and present knockdown data for MKRN2 along with two additional E3 ligases identified in the screen, before once again emphasizing that MKRN2 is the most SG-depleted ligase and therefore the main focus of the study. For clarity and logical flow, the manuscript would benefit from reordering the narrative. Specifically, the authors should first present the validation data for all three selected E3 ligases, and only then justify the decision to focus on MKRN2 for in-depth characterization. In addition to the extent of its SG depletion, the authors may also consider providing biologically relevant reasons for prioritizing MKRN2 (e.g., domain architecture, known roles in stress responses, or prior evidence of ubiquitination-related functions). Reorganizing this section would improve readability and better guide the reader through the rationale for the study's focus.
• At lines 137-138, the manuscript states: "Together these data indicate that MKRN2 regulates the assembly dynamics of SGs by promoting their coalescence during HS and can increase SG ubiquitin content." While Figure 3G shows some co-localization of MKRN2 with ubiquitin, immunofluorescence alone is insufficient to claim an increase in SG ubiquitin content. This conclusion should be supported by orthogonal experiments, such as Western blotting, in vitro ubiquitination assays, or immunoprecipitation of SG components. Including a control under no-stress conditions would also help demonstrate that ubiquitination increases specifically in response to stress. The second part of the statement should therefore be rephrased to avoid overinterpretation, for example:"...and may be associated with increased ubiquitination within SGs, as suggested by co-localization, pending further validation by complementary assays."
• At line 157, the statement: "Therefore, we conclude that MKRN2 ubiquitinates a subset of DRiPs, avoiding their accumulation inside SGs" should be rephrased as a preliminary observation. While the data support a role for MKRN2 in SG disassembly and a reduction of DRIPs, direct ubiquitination of DRIPs by MKRN2 has not been demonstrated. A more cautious phrasing would better reflect the current evidence and avoid overinterpretation.

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

• This study provides a valuable advancement in understanding the role of ubiquitination in stress granule (SG) dynamics and the clearance of SGs formed under heat stress. A major strength is the demonstration of how E3 ligases identified through proteomic screening, particularly MKRN2, influence SG assembly and disassembly in a ubiquitination- and heat stress-dependent manner. The combination of proteomics, imaging, and functional assays provides a coherent mechanistic framework linking ubiquitination to SG homeostasis. Limitations of the study include the exclusive use of a single model system (U2OS cells), which may limit generalizability. Additionally, some observations-such as MKRN2-dependent ubiquitination within SGs and changes in DRIP accumulation under different conditions-would benefit from orthogonal validation experiments (e.g., Western blotting, immunoprecipitation, or in vitro assays) to confirm and strengthen these findings. Addressing these points would enhance the robustness and broader applicability of the conclusions.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

• The closest related result in literature is - Yang, Cuiwei et al. "Stress granule homeostasis is modulated by TRIM21-mediated ubiquitination of G3BP1 and autophagy-dependent elimination of stress granules." Autophagy vol. 19,7 (2023): 1934-1951. doi:10.1080/15548627.2022.2164427 - demonstrating that TRIM21, an E3 ubiquitin ligase, catalyzes K63-linked ubiquitination of G3BP1, a core SG nucleator, under oxidative stress. This ubiquitination by TRIM21 inhibits SG formation, likely by altering G3BP1's propensity for phase separation. In contrast, the MKRN2 study identifies a different E3 (MKRN2) that regulates SG dynamics under heat stress and appears to influence both assembly and disassembly. This expands the role of ubiquitin ligases in SG regulation beyond those previously studied (like TRIM21).
• Gwon and colleagues (Gwon Y, Maxwell BA, Kolaitis RM, Zhang P, Kim HJ, Taylor JP. Ubiquitination of G3BP1 mediates stress granule disassembly in a context-specific manner. Science. 2021;372(6549):eabf6548. doi:10.1126/science.abf6548) have shown that K63-linked ubiquitination of G3BP1 is required for SG disassembly after heat stress. This ubiquitinated G3BP1 recruits the segregase VCP/p97, which helps extract G3BP1 from SGs for disassembly. The MKRN2 paper builds on this by linking UBA1-dependent ubiquitination and MKRN2's activity to SG disassembly. Specifically, they show MKRN2 knockdown affects disassembly, and suggest MKRN2 helps prevent accumulation of defective ribosomal products (DRiPs) in SGs, adding a new layer to the ubiquitin-VCP model.
• Ubiquitination's impact is highly stress- and context-dependent (different chain types, ubiquitin linkages, and recruitment of E3s). The MKRN2 work conceptually strengthens this idea: by showing that MKRN2's engagement with SGs depends on active ubiquitination via UBA1, and by demonstrating functional consequences (SG dynamics + DRIP accumulation), the study highlights how cellular context (e.g., heat stress) can recruit specific ubiquitin ligases to SGs and modulate their behavior.
• There is a gap in the literature: very few (if any) studies explicitly combine the biology of DRIPs, stress granules, and E3 ligase mediated ubiquitination, especially in mammalian cells. There are relevant works about DRIP biology in stress granules, but those studies focus on chaperone-based quality control, not ubiquitin ligase-mediated ubiquitination of DRIPs. This study seems to be one of the first to make that connection in mammalian (or human-like) SG biology. A work on the plant DRIP-E3 ligase TaSAP5 (Zhang N, Yin Y, Liu X, et al. The E3 Ligase TaSAP5 Alters Drought Stress Responses by Promoting the Degradation of DRIP Proteins. Plant Physiol. 2017;175(4):1878-1892. doi:10.1104/pp.17.01319 ) shows that DRIPs can be directly ubiquitinated by E3s in other biological systems - which supports the plausibility of the MKRN2 mechanism, but it's not the same context.
• A very recent review (Yuan, Lin et al. "Stress granules: emerging players in neurodegenerative diseases." Translational neurodegeneration vol. 14,1 22. 12 May. 2025, doi:10.1186/s40035-025-00482-9) summarizes and reinforces the relationship among SGs and the pathogenesis of different neurodegenerative diseases (NDDs). By identifying MKRN2 as a new ubiquitin regulator in SGs, the current study could have relevance for neurodegeneration and proteotoxic diseases, providing a new candidate to explore in disease models.

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

The audience for this paper is primarily specialized, including researchers in stress granule biology, ubiquitin signaling, protein quality control, ribosome biology, and cellular stress responses. The findings will also be of interest to scientists working on granulostasis, nascent protein surveillance, and proteostasis mechanisms. Beyond these specific fields, the study provides preliminary evidence linking ubiquitination to DRIP handling and SG dynamics, which may stimulate new research directions and collaborative efforts across complementary areas of cell biology and molecular biology.

Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I work in ubiquitin biology, focusing on ubiquitination signaling in physiological and disease contexts, with particular expertise in the identification of E3 ligases and their substrates across different cellular systems and in vivo models. I have less expertise in stress granule dynamics and DRiP biology, so my evaluation of those aspects is more limited and relies on interpretation of the data presented in the manuscript.

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Reply to the reviewers

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

*The authors have a longstanding focus and reputation on single cell sequencing technology development and application. In this current study, the authors developed a novel single-cell multi-omic assay termed "T-ChIC" so that to jointly profile the histone modifications along with the full-length transcriptome from the same single cells, analyzed the dynamic relationship between chromatin state and gene expression during zebrafish development and cell fate determination. In general, the assay works well, the data look convincing and conclusions are beneficial to the community. *

Thank you for your positive feedback.

*There are several single-cell methodologies all claim to co-profile chromatin modifications and gene expression from the same individual cell, such as CoTECH, Paired-tag and others. Although T-ChIC employs pA-Mnase and IVT to obtain these modalities from single cells which are different, could the author provide some direct comparisons among all these technologies to see whether T-ChIC outperforms? *

In a separate technical manuscript describing the application of T-ChIC in mouse cells (Zeller, Blotenburg et al 2024, bioRxiv, 2024.05. 09.593364), we have provided a direct comparison of data quality between T-ChIC and other single-cell methods for chromatin-RNA co-profiling (Please refer to Fig. 1C,D and Fig. S1D, E, of the preprint). We show that compared to other methods, T-ChIC is able to better preserve the expected biological relationship between the histone modifications and gene expression in single cells.

*In current study, T-ChIC profiled H3K27me3 and H3K4me1 modifications, these data look great. How about other histone modifications (eg H3K9me3 and H3K36me3) and transcription factors? *

While we haven't profiled these other modifications using T-ChIC in Zebrafish, we have previously published high quality data on these histone modifications using the sortChIC method, on which T-ChIC is based (Zeller, Yeung et al 2023). In our comparison, we find that histone modification profiles between T-ChIC and sortChIC are very similar (Fig. S1C in Zeller, Blotenburg et al 2024). Therefore the method is expected to work as well for the other histone marks.

*T-ChIC can detect full length transcription from the same single cells, but in FigS3, the authors still used other published single cell transcriptomics to annotate the cell types, this seems unnecessary? *

We used the published scRNA-seq dataset with a larger number of cells to homogenize our cell type labels with these datasets, but we also cross-referenced our cluster-specific marker genes with ZFIN and homogenized the cell type labels with ZFIN ontology. This way our annotation is in line with previous datasets but not biased by it. Due the relatively smaller size of our data, we didn't expect to identify unique, rare cell types, but our full-length total RNA assay helps us identify non-coding RNAs such as miRNA previously undetected in scRNA assays, which we have now highlighted in new figure S1c .

*Throughout the manuscript, the authors found some interesting dynamics between chromatin state and gene expression during embryogenesis, independent approaches should be used to validate these findings, such as IHC staining or RNA ISH? *

We appreciate that the ISH staining could be useful to validate the expression pattern of genes identified in this study. But to validate the relationships between the histone marks and gene expression, we need to combine these stainings with functional genomics experiments, such as PRC2-related knockouts. Due to their complexity, such experiments are beyond the scope of this manuscript (see also reply to reviewer #3, comment #4 for details).

*In Fig2 and FigS4, the authors showed H3K27me3 cis spreading during development, this looks really interesting. Is this zebrafish specific? H3K27me3 ChIP-seq or CutTag data from mouse and/or human embryos should be reanalyzed and used to compare. The authors could speculate some possible mechanisms to explain this spreading pattern? *

Thanks for the suggestion. In this revision, we have reanalysed a dataset of mouse ChIP-seq of H3K27me3 during mouse embryonic development by Xiang et al (Nature Genetics 2019) and find similar evidence of spreading of H3K27me3 signal from their pre-marked promoter regions at E5.5 epiblast upon differentiation (new Figure S4i). This observation, combined with the fact that the mechanism of pre-marking of promoters by PRC1-PRC2 interaction seems to be conserved between the two species (see (Hickey et al., 2022), (Mei et al., 2021) & (Chen et al., 2021)), suggests that the dynamics of H3K27me3 pattern establishment is conserved across vertebrates. But we think a high-resolution profiling via a method like T-ChIC would be more useful to demonstrate the dynamics of signal spreading during mouse embryonic development in the future. We have discussed this further in our revised manuscript.

Reviewer #1 (Significance (Required)):

*The authors have a longstanding focus and reputation on single cell sequencing technology development and application. In this current study, the authors developed a novel single-cell multi-omic assay termed "T-ChIC" so that to jointly profile the histone modifications along with the full-length transcriptome from the same single cells, analyzed the dynamic relationship between chromatin state and gene expression during zebrafish development and cell fate determination. In general, the assay works well, the data look convincing and conclusions are beneficial to the community. *

Thank you very much for your supportive remarks.

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

*Joint analysis of multiple modalities in single cells will provide a comprehensive view of cell fate states. In this manuscript, Bhardwaj et al developed a single-cell multi-omics assay, T-ChIC, to simultaneously capture histone modifications and full-length transcriptome and applied the method on early embryos of zebrafish. The authors observed a decoupled relationship between the chromatin modifications and gene expression at early developmental stages. The correlation becomes stronger as development proceeds, as genes are silenced by the cis-spreading of the repressive marker H3k27me3. Overall, the work is well performed, and the results are meaningful and interesting to readers in the epigenomic and embryonic development fields. There are some concerns before the manuscript is considered for publication. *

We thank the reviewer for appreciating the quality of our study.

*Major concerns: *

1. • A major point of this study is to understand embryo development, especially gastrulation, with the power of scMulti-Omics assay. However, the current analysis didn't focus on deciphering the biology of gastrulation, i.e., lineage-specific pioneer factors that help to reform the chromatin landscape. The majority of the data analysis is based on the temporal dimension, but not the cell-type-specific dimension, which reduces the value of the single-cell assay. *

We focused on the lineage-specific transcription factor activity during gastrulation in Figure 4 and S8 of the manuscript and discovered several interesting regulators active at this stage. During our analysis of the temporal dimension for the rest of the manuscript, we also classified the cells by their germ layer and "latent" developmental time by taking the full advantage of the single-cell nature of our data. Additionally, we have now added the cell-type-specific H3K27-demethylation results for 24hpf in response to your comment below. We hope that these results, together with our openly available dataset would demonstrate the advantage of the single-cell aspect of our dataset.

1. *The cis-spreading of H3K27me3 with developmental time is interesting. Considering H3k27me3 could mark bivalent regions, especially in pluripotent cells, there must be some regions that have lost H3k27me3 signals during development. Therefore, it's confusing that the authors didn't find these regions (30% spreading, 70% stable). The authors should explain and discuss this issue. *

Indeed we see that ~30% of the bins enriched in the pluripotent stage spread, while 70% do not seem to spread. In line with earlier observations(Hickey et al., 2022; Vastenhouw et al., 2010), we find that H3K27me3 is almost absent in the zygote and is still being accumulated until 24hpf and beyond. Therefore the majority of the sites in the genome still seem to be in the process of gaining H3K27me3 until 24hpf, explaining why we see mostly "spreading" and "stable" states. Considering most of these sites are at promoters and show signs of bivalency, we think that these sites are marked for activation or silencing at later stages. We have discussed this in the manuscript ("discussion"). However, in response to this and earlier comment, we went back and searched for genes that show H3K27-demethylation in the most mature cell types (at 24 hpf) in our data, and found a subset of genes that show K27 demethylation after acquiring them earlier. Interestingly, most of the top genes in this list are well-known as developmentally important for their corresponding cell types. We have added this new result and discussed it further in the manuscript (Fig. 2d,e, , Supplementary table 3).

*Minors: *

1. • The authors cited two scMulti-omics studies in the introduction, but there have been lots of single-cell multi-omics studies published recently. The authors should cite and consider them. *

We have cited more single-cell chromatin and multiome studies focussed on early embryogenesis in the introduction now.

*2. T-ChIC seems to have been presented in a previous paper (ref 15). Therefore, Fig. 1a is unnecessary to show. *

Figure 1a. shows a summary of our Zebrafish TChIC workflow, which contains the unique sample multiplexing and sorting strategy to reduce batch effects, which was not applied in the original TChIC workflow. We have now clarified this in "Results".

1. *It's better to show the percentage of cell numbers (30% vs 70%) for each heatmap in Figure 2C. *

We have added the numbers to the corresponding legends.

1. *Please double-check the citation of Fig. S4C, which may not relate to the conclusion of signal differences between lineages. *

The citation seems to be correct (Fig. S4C supplements Fig. 2C, but shows mesodermal lineage cells) but the description of the legend was a bit misleading. We have clarified this now.

*5. Figure 4C has not been cited or mentioned in the main text. Please check. *

Thanks for pointing it out. We have cited it in Results now.

Reviewer #2 (Significance (Required)):

*Strengths: This work utilized a new single-cell multi-omics method and generated abundant epigenomics and transcriptomics datasets for cells covering multiple key developmental stages of zebrafish. *

*Limitations: The data analysis was superficial and mainly focused on the correspondence between the two modalities. The discussion of developmental biology was limited. *

*Advance: The zebrafish single-cell datasets are valuable. The T-ChIC method is new and interesting. *

*The audience will be specialized and from basic research fields, such as developmental biology, epigenomics, bioinformatics, etc. *

*I'm more specialized in the direction of single-cell epigenomics, gene regulation, 3D genomics, etc. *

Thank you for your remarks.

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

*This manuscript introduces T‑ChIC, a single‑cell multi‑omics workflow that jointly profiles full‑length transcripts and histone modifications (H3K27me3 and H3K4me1) and applies it to early zebrafish embryos (4-24 hpf). The study convincingly demonstrates that chromatin-transcription coupling strengthens during gastrulation and somitogenesis, that promoter‑anchored H3K27me3 spreads in cis to enforce developmental gene silencing, and that integrating TF chromatin status with expression can predict lineage‑specific activators and repressors. *

*Major concerns *

1. *Independent biological replicates are absent, so the authors should process at least one additional clutch of embryos for key stages (e.g., 6 hpf and 12 hpf) with T‑ChIC and demonstrate that the resulting data match the current dataset. *

Thanks for pointing this out. We had, in fact, performed T-ChIC experiments in four rounds of biological replicates (independent clutch of embryos) and merged the data to create our resource. Although not all timepoints were profiled in each replicate, two timepoints (10 and 24hpf) are present in all four, and the celltype composition of these replicates from these 2 timepoints are very similar. We have added new plots in figure S2f and added (new) supplementary table (#1) to highlight the presence of biological replicates.

2. *The TF‑activity regression model uses an arbitrary R² {greater than or equal to} 0.6 threshold; cross‑validated R² distributions, permutation‑based FDR control, and effect‑size confidence intervals are needed to justify this cut‑off. *

Thank you for this suggestion. We did use 10-fold cross validation during training and obtained the R2 values of TF motifs from the independent test set as an unbiased estimate. However, the cutoff of R2 > 0.6 to select the TFs for classification was indeed arbitrary. In the revised version, we now report the FDR-adjusted p-values for these R2 estimates based on permutation tests, and select TFs with a cutoff of padj supplementary table #4 to include the p-values for all tested TFs. However, we see that our arbitrary cutoff of 0.6 was in fact, too stringent, and we can classify many more TFs based on the FDR cutoffs. We also updated our reported numbers in Fig. 4c to reflect this. Moreover, supplementary table #4 contains the complete list of TFs used in the analysis to allow others to choose their own cutoff.

3. *Predicted TF functions lack empirical support, making it essential to test representative activators (e.g., Tbx16) and repressors (e.g., Zbtb16a) via CRISPRi or morpholino knock‑down and to measure target‑gene expression and H3K4me1 changes. *

We agree that independent validation of the functions of our predicted TFs on target gene activity would be important. During this revision, we analysed recently published scRNA-seq data of Saunders et al. (2023) (Saunders et al., 2023), which includes CRISPR-mediated F0 knockouts of a couple of our predicted TFs, but the scRNAseq was performed at later stages (24hpf onward) compared to our H3K4me1 analysis (which was 4-12 hpf). Therefore, we saw off-target genes being affected in lineages where these TFs are clearly not expressed (attached Fig 1). We therefore didn't include these results in the manuscript. In future, we aim to systematically test the TFs predicted in our study with CRISPRi or similar experiments.

4. *The study does not prove that H3K27me3 spreading causes silencing; embryos treated with an Ezh2 inhibitor or prc2 mutants should be re‑profiled by T‑ChIC to show loss of spreading along with gene re‑expression. *

We appreciate the suggestion that indeed PRC2-disruption followed by T-ChIC or other forms of validation would be needed to confirm whether the H3K27me3 spreading is indeed causally linked to the silencing of the identified target genes. But performing this validation is complicated because of multiple reasons: 1) due to the EZH2 contribution from maternal RNA and the contradicting effects of various EZH2 zygotic mutations (depending on where the mutation occurs), the only properly validated PRC2-related mutant seems to be the maternal-zygotic mutant MZezh2, which requires germ cell transplantation (see Rougeot et al. 2019 (Rougeot et al., 2019)) , and San et al. 2019 (San et al., 2019) for details). The use of inhibitors have been described in other studies (den Broeder et al., 2020; Huang et al., 2021), but they do not show a validation of the H3K27me3 loss or a similar phenotype as the MZezh2 mutants, and can present unwanted side effects and toxicity at a high dose, affecting gene expression results. Moreover, in an attempt to validate, we performed our own trials with the EZH2 inhibitor (GSK123) and saw that this time window might be too short to see the effect within 24hpf (attached Fig. 2). Therefore, this validation is a more complex endeavor beyond the scope of this study. Nevertheless, our further analysis of H3K27me3 de-methylation on developmentally important genes (new Fig. 2e-f, Sup. table 3) adds more confidence that the polycomb repression plays an important role, and provides enough ground for future follow up studies.

*Minor concerns *

1. *Repressive chromatin coverage is limited, so profiling an additional silencing mark such as H3K9me3 or DNA methylation would clarify cooperation with H3K27me3 during development. *

We agree that H3K27me3 alone would not be sufficient to fully understand the repressive chromatin state. Extension to other chromatin marks and DNA methylation would be the focus of our follow up works.

*2. Computational transparency is incomplete; a supplementary table listing all trimming, mapping, and peak‑calling parameters (cutadapt, STAR/hisat2, MACS2, histoneHMM, etc.) should be provided. *

As mentioned in the manuscript, we provide an open-source pre-processing pipeline "scChICflow" to perform all these steps (github.com/bhardwaj-lab/scChICflow). We have now also provided the configuration files on our zenodo repository (see below), which can simply be plugged into this pipeline together with the fastq files from GEO to obtain the processed dataset that we describe in the manuscript. Additionally, we have also clarified the peak calling and post-processing steps in the manuscript now.

*3. Data‑ and code‑availability statements lack detail; the exact GEO accession release date, loom‑file contents, and a DOI‑tagged Zenodo archive of analysis scripts should be added. *

We have now publicly released the .h5ad files with raw counts, normalized counts, and complete gene and cell-level metadata, along with signal tracks (bigwigs) and peaks on GEO. Additionally, we now also released the source datasets and notebooks (.Rmarkdown format) on Zenodo that can be used to replicate the figures in the manuscript, and updated our statements on "Data and code availability".

*4. Minor editorial issues remain, such as replacing "critical" with "crucial" in the Abstract, adding software version numbers to figure legends, and correcting the SAMtools reference. *

Thank you for spotting them. We have fixed these issues.

Reviewer #3 (Significance (Required)):

The method is technically innovative and the biological insights are valuable; however, several issues-mainly concerning experimental design, statistical rigor, and functional validation-must be addressed to solidify the conclusions.

Thank you for your comments. We hope to have addressed your concerns in this revised version of our manuscript.

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

This manuscript introduces T‑ChIC, a single‑cell multi‑omics workflow that jointly profiles full‑length transcripts and histone modifications (H3K27me3 and H3K4me1) and applies it to early zebrafish embryos (4-24 hpf). The study convincingly demonstrates that chromatin-transcription coupling strengthens during gastrulation and somitogenesis, that promoter‑anchored H3K27me3 spreads in cis to enforce developmental gene silencing, and that integrating TF chromatin status with expression can predict lineage‑specific activators and repressors.

Major concerns

1. Independent biological replicates are absent, so the authors should process at least one additional clutch of embryos for key stages (e.g., 6 hpf and 12 hpf) with T‑ChIC and demonstrate that the resulting data match the current dataset.
2. The TF‑activity regression model uses an arbitrary R² {greater than or equal to} 0.6 threshold; cross‑validated R² distributions, permutation‑based FDR control, and effect‑size confidence intervals are needed to justify this cut‑off.
3. Predicted TF functions lack empirical support, making it essential to test representative activators (e.g., Tbx16) and repressors (e.g., Zbtb16a) via CRISPRi or morpholino knock‑down and to measure target‑gene expression and H3K4me1 changes.
4. The study does not prove that H3K27me3 spreading causes silencing; embryos treated with an Ezh2 inhibitor or prc2 mutants should be re‑profiled by T‑ChIC to show loss of spreading along with gene re‑expression.

Minor concerns

1. Repressive chromatin coverage is limited, so profiling an additional silencing mark such as H3K9me3 or DNA methylation would clarify cooperation with H3K27me3 during development.
2. Computational transparency is incomplete; a supplementary table listing all trimming, mapping, and peak‑calling parameters (cutadapt, STAR/hisat2, MACS2, histoneHMM, etc.) should be provided.
3. Data‑ and code‑availability statements lack detail; the exact GEO accession release date, loom‑file contents, and a DOI‑tagged Zenodo archive of analysis scripts should be added.
4. Minor editorial issues remain, such as replacing "critical" with "crucial" in the Abstract, adding software version numbers to figure legends, and correcting the SAMtools reference.

Significance

The method is technically innovative and the biological insights are valuable; however, several issues-mainly concerning experimental design, statistical rigor, and functional validation-must be addressed to solidify the conclusions.

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

Joint analysis of multiple modalities in single cells will provide a comprehensive view of cell fate states. In this manuscript, Bhardwaj et al developed a single-cell multi-omics assay, T-ChIC, to simultaneously capture histone modifications and full-length transcriptome and applied the method on early embryos of zebrafish. The authors observed a decoupled relationship between the chromatin modifications and gene expression at early developmental stages. The correlation becomes stronger as development proceeds, as genes are silenced by the cis-spreading of the repressive marker H3k27me3. Overall, the work is well performed, and the results are meaningful and interesting to readers in the epigenomic and embryonic development fields. There are some concerns before the manuscript is considered for publication.

Major concerns:

1. A major point of this study is to understand embryo development, especially gastrulation, with the power of scMulti-Omics assay. However, the current analysis didn't focus on deciphering the biology of gastrulation, i.e., lineage-specific pioneer factors that help to reform the chromatin landscape. The majority of the data analysis is based on the temporal dimension, but not the cell-type-specific dimension, which reduces the value of the single-cell assay.
2. The cis-spreading of H3K27me3 with developmental time is interesting. Considering H3k27me3 could mark bivalent regions, especially in pluripotent cells, there must be some regions that have lost H3k27me3 signals during development. Therefore, it's confusing that the authors didn't find these regions (30% spreading, 70% stable). The authors should explain and discuss this issue.

Minors:

1. The authors cited two scMulti-omics studies in the introduction, but there have been lots of single-cell multi-omics studies published recently. The authors should cite and consider them.
2. T-ChIC seems to have been presented in a previous paper (ref 15). Therefore, Fig. 1a is unnecessary to show.
3. It's better to show the percentage of cell numbers (30% vs 70%) for each heatmap in Figure 2C.
4. Please double-check the citation of Fig. S4C, which may not relate to the conclusion of signal differences between lineages.
5. Figure 4C has not been cited or mentioned in the main text. Please check.

Significance

Strengths: This work utilized a new single-cell multi-omics method and generated abundant epigenomics and transcriptomics datasets for cells covering multiple key developmental stages of zebrafish. Limitations: The data analysis was superficial and mainly focused on the correspondence between the two modalities. The discussion of developmental biology was limited.

Advance: The zebrafish single-cell datasets are valuable. The T-ChIC method is new and interesting.

The audience will be specialized and from basic research fields, such as developmental biology, epigenomics, bioinformatics, etc.

I'm more specialized in the direction of single-cell epigenomics, gene regulation, 3D genomics, etc.

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

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Referee #1

Evidence, reproducibility and clarity

The authors have a longstanding focus and reputation on single cell sequencing technology development and application. In this current study, the authors developed a novel single-cell multi-omic assay termed "T-ChIC" so that to jointly profile the histone modifications along with the full-length transcriptome from the same single cells, analyzed the dynamic relationship between chromatin state and gene expression during zebrafish development and cell fate determination. In general, the assay works well, the data look convincing and conclusions are beneficial to the community.

There are several single-cell methodologies all claim to co-profile chromatin modifications and gene expression from the same individual cell, such as CoTECH, Paired-tag and others. Although T-ChIC employs pA-Mnase and IVT to obtain these modalities from single cells which are different, could the author provide some direct comparisons among all these technologies to see whether T-ChIC outperforms?

In current study, T-ChIC profiled H3K27me3 and H3K4me1 modifications, these data look great. How about other histone modifications (eg H3K9me3 and H3K36me3) and transcription factors?

T-ChIC can detect full length transcription from the same single cells, but in FigS3, the authors still used other published single cell transcriptomics to annotate the cell types, this seems unnecessary?

Throughout the manuscript, the authors found some interesting dynamics between chromatin state and gene expression during embryogenesis, independent approaches should be used to validate these findings, such as IHC staining or RNA ISH?

In Fig2 and FigS4, the authors showed H3K27me3 cis spreading during development, this looks really interesting. Is this zebrafish specific? H3K27me3 ChIP-seq or CutTag data from mouse and/or human embryos should be reanalyzed and used to compare. The authors could speculate some possible mechanisms to explain this spreading pattern?

Significance

The authors have a longstanding focus and reputation on single cell sequencing technology development and application. In this current study, the authors developed a novel single-cell multi-omic assay termed "T-ChIC" so that to jointly profile the histone modifications along with the full-length transcriptome from the same single cells, analyzed the dynamic relationship between chromatin state and gene expression during zebrafish development and cell fate determination. In general, the assay works well, the data look convincing and conclusions are beneficial to the community.

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Reply to the reviewers

1. General Statements

We thank the reviewers for their overall support, thorough review, and thoughtful comments. The points raised were all warranted and we feel that addressing them has improved the quality of our manuscript. Below we respond to each of the points raised.

2. Point-by-point description of the revisions

Reviewer #1

Minor comments:

Are the lgl-1; pac-1 M-Z- double mutants dead? Only the phenotype of pac-1(M-Z-); lgl-1 (M+Z-) is shown. In figures and text throughout, it should be clear whether mutants are referring to zygotic loss or both maternal and zygotic loss, as this distinction could have major implications on the interpretation of experiments.

Almost all experiments we performed used a combination of RNAi of lgl-1 in a homozygous pac-1 null mutant background, or the other way around. RNAi should eliminate maternal product, but we hesitate to use the terminology M/Z since it has previously been used for protein degradation strategies.

We have updated the text and figure 1 to address the potential of maternal product masking earlier phenotypes, and performed additional RNAi experiments to demonstrate that the phenotypes obtained by RNAi for either pac-1 or lgl-1 in a homozygous mutant background for the other are the same as for the genetic double mutant. The results are shown as additional images and quantifications in figure 1B,C. We also updated the legend to figure 1 to make it clear that double genetic mutants are obtained from heterozygous lgl-1/+ parents.

Regarding the phenotype of lgl-1; pac-1 M-Z- double mutants: assuming the reviewer refers to M-Z- double genetic mutants, we cannot make such embryos as the pac-1(M-Z-); lgl-1(M+Z-) animals are already lethal.

In Figure 1C, it would be more appropriate to show a fully elongated WT embryo to contrast with arrested elongation in mutant embryos.

We agree with the reviewer and have replaced the 2-fold WT embryo with a 3-fold embryo.

Is the lateral spread of DLG-1 in double mutant embryos a result of failure to polarize DLG-1, or failure to maintain polarity? This should be straightforward to address in higher time resolution movies.

We have analyzed additional embryos at early stages of development. In lgl-1; pac-1 embryos we never see the appearance of complete junctions: defects are apparent already at dorsal intercalation. We interpret these results as a failure to properly polarize DLG-1. We have added additional images to Figure S2 and added this sentence to the text: Imaging of embryos from early stages of development on showed that normal continuous junctional DLG-1 bands are never established in pac-1(RNAi); lgl-1(mib201) embryos (Fig. S2B).

The lack of enhancement of hmp-1(fe4) by lgl-1(RNAi) is quite interesting, given that pac-1 does enhance hmp-1(fe4). To rule out the possibility that this result stems from incomplete lgl-1 RNAi, this experiment should be repeated using the lgl-1 null mutant.

We have done this experiment by recreating the fe4 S823F mutation in the lgl-1(null) mutant background as well as in the wild-type CGC1 background using CRISPR/Cas9. The phenotype of both was similar, but differs from that of the original PE97 strain. In the original strain, there is ~50% embryonic lethality but worms that complete embryogenesis grow up to be fertile adults. In our new "fe4" strains, nearly all animals are severely malformed with little to no elongation taking place. We are able to maintain both strains (with and without lgl-1) homozygous but with difficulty as only ~5% of animals grow up and give progeny. Apparently, there are genetic differences between PE97 and our CGC1 background that cause phenotypic differences despite having the same amino acid change in HMP-1.

Nevertheless, using our original embryonic viability criterium of 'hatching', loss of lgl-1 does not enhance the S823F mutation. We have included the following text in the manuscript:

To rule out that the lack of enhancement by lgl-1(RNAi) is due to incomplete inactivation of lgl-1, we also re-created the hmp-1(fe4) mutation (S823F) by CRISPR in lgl-1(mib201) mutant animals and wild-type controls. The phenotype of the S823F mutant we created is more severe than that of the original PE97 hmp-1(fe4) strain, with only ~5% of animals becoming fertile adults (Fig. S2F). This likely represents the presence of compensatory changes that have accumulated over time in PE97. Nevertheless, consistent with our RNAi results, the presence of lgl-1(mib201) did not further exacerbate the phenotype of HMP-1(S823F) (Fig. S2E, F). Taken together, the lack of enhancement of hmp-1(S823F) mutants by inactivation of loss of lgl-1 This observation argues against a primary role for lgl-1 in regulating cell junctions.

• Related to point 4, do pac-1 or lgl-1 null mutants enhance partial knockdown of junction protein DLG-1, or is this effect (of pac-1) specific to HMP-1/AJs?*

We have attempted to address this point using feeding RNAi against dlg-1. However, we were not able to obtain partial depletion of DLG-1. On RNAi feeding plates, control, pac-1, and lgl-1 animals did not show significant embryonic lethality. We checked RNAi effectiveness with a DLG-1::mCherry strain and found RNAi by feeding to be very ineffective. Since we could not deplete DLG-1 to a level that results in partial embryonic lethality, we were not able to address this question properly.

Does lgl-1 loss affect PAC-1 protein localization and vice versa?

It does not. We have added the following text and a figure panel: Loss-of-function mutants that strongly enhance a phenotype are often interpreted as acting in parallel pathways. We therefore examined whether loss of lgl-1 or pac-1 alters the localization of endogenously GFP-tagged LGL-1 or PAC-1. In neither null background did we detect changes in the subcellular localization of the other protein, consistent with LGL-1 and PAC-1 functioning in parallel pathways (Fig. S1D).

Reviewer #2

Very little of the imaging data are analyzed quantitatively, and in many cases it is not clear how many embryos were analyzed. While the images that are presented show clear defects, readers cannot determine how reproducible, strong or significant the phenotypes are.

We completely agree with the reviewer that interpretation of our data requires this information and apologize for the omission in the first manuscript version. The phenotypes are highly penetrant and consistent (timing of arrest, % lethality, junctional defects), and we have now added quantifications throughout the manuscript.

In particular, the data below should be quantified and, where possible, analyzed statistically:

• The frequency of the various junctional phenotypes shown in 2C

We have now quantified the junctional phenotypes. The junctional defects are highly penetrant: >90% of lgl-1; pac-1 embryos have junctional defects (new Fig. 2B). We used airy-scan confocal imaging to analyze the distribution of the different phenotypes (unaffected, spread laterally, and ring-like pattern). The results are shown in Fig. 2G.

• The expansion of DLG-1::mCherry in pac-1 lgl-1 embryos should be quantified (related to Figure 2B). For example, the percentage of membrane (marked by PH::GFP) occupied by DLG-1 could be quantified.

We have performed this quantification, shown in Fig. 2D.

- Similarly, the expansion of the aPKC domain should be quantified (Figure 3A).

An objective quantification of aPKC signal is difficult due to the relatively weak expression of aPKC::GFP and the lack of a clear demarcating boundary. This is part of the reason we measured tortuosity as a more quantifyable indicator of apical domain expansion. We have now added a qualitative observation table as Figure 3B. In addition, we have expanded the quantification of cell geometry by measuring lateral and basal surfaces. Lateral surfaces were decreased. We added the following text:

To better understand the reason for the change in geometry, we also measured the lengths of the lateral and basal surfaces (Fig. 3F). We found that the absolute lengths of the apical surfaces were not significantly different between pac-1(RNAi); lgl-1(mib201) and control animals. Instead, the lengths of the lateral domain were reduced (Fig. 3F). Hence, the more dome-shaped appearance of epidermal cells in pac-1; lgl-1 double mutant animals is due to a decrease in lateral domain size, which is consistent with the observed lateral spreading of aPKC.

• How many embryos were analyzed for each marker shown in Figure 2A, and what proportion showed the described phenotypes? This could be given in the text or in a panel.

We have added these numbers to panel 2B, and indicated the percentage in the text.

• The frequency of the various junctional phenotypes shown in 4F.

To address this, we have changed figure 4F to show three types of phenotype (strong, mild, no phenotype) and added how frequently we observed each to the panels. In rescue experiments, 18/24 embryos showed no junctional defects, while 6/24 showed a mild defect (compared to 100% severe in non-rescued embryos). To make room for this and other quantifications in Figure 4, we moved the demonstration that PAC-1 is depleted by RNAi to supplemental figure S4.

Because the genetic perturbations used are global (either deletions or RNAi), it is not established whether PAC-1/LGL-1 act in epidermal epithelial cells per se (versus an earlier requirement that manifests in epidermal epithelial cells). While I agree that this is the most likely scenario, other mechanisms are possible.

Our experiments indeed use global depletion/deletion of lgl-1 and pac-1. We cannot exclude therefore that other tissues do not contribute to the epithelial phenotypes. We assume that other tissues would be affected as well, and in fact have observed abnormal looking pharynx tissue (see our response to reviewer 3 below for examples). As the epidermis is one of the first tissue to develop it is likely the first in which phenotypes become apparent.

In particular, the overall GFP::aPKC levels appear notably higher in pac-1 lgl-1 embryos in Figure 3A. aPKC levels should be quantified to determine if this is true of pac-1 lgl-1 embryos. If so, couldn't that explain (or at least contribute to) the observed phenotypes?

Overall higher levels could indeed contribute to the phenotype. However, we have now quantified total aPKC levels in control and pac-1; lgl-1 embryos found no difference between them. We have added the following text to the manuscript: To determine if increased expression of aPKC might explain the broadened apical localization, we measured total intensity levels of aPKC::GFP. However, we detected no differences in fluorescence levels between control and pac-1(RNAi); lgl-1(mib201) animals (Fig. S3B, C).

Minor

Figure 4: For completeness, please include the embryonic viability of pac-1 lgl-1 +/- embryos treated with EV and cdc-42(RNAi), as was done for pac-1 lgl-1 pkc-3(ts) in Figure 4E. Presumably the increased proportion of viable embryos with the lgl-1 deletion allele is reflected in an overall increase in embryonic viability.

The embryonic viability indeed increases, but not as much as one might think because 15% of embryos die from the cdc-42 RNAi itself. The most important rescue argument is that we can obtain adult pac-1; lgl-1 animals with cdc-42 RNAi.

We have now included the overall rescue and the following text: Overall, cdc-42 RNAi caused a mild increase in embryonic viability (Fig. 4A). However, total embryonic viability may underestimate rescue of pac-1; lgl-1 embryonic lethality, because it also includes the ~15% lethality caused by cdc-42 inactivation itself, even among animals wild type for lgl-1.

The orientation of the inset images in Figures 2C, 3A and 3D is confusing. An illustration showing how these images are oriented relative to each other would be helpful.

We have added a figure showing how the junctions are oriented in the figures (Fig. 2E). We have also added supplemental videos S3 and S4 that should illustrate the phenotype more clearly as well.

For completeness, it would be good to test whether lgl-1(delta) is also synthetically lethal with picc-1(RNAi) (Zilberman 2017).

We like this idea and had already looked into this. Lgl-1 and picc-1 are not synthetic lethal (see graph in word file submitted). However, PICC-1 is not the only junctional localization signal for PAC-1, as demonstrated by the Nance lab. We find the data interesting but feel that it deserves a more thorough structure/function investigation of PAC-1 than we can provide here. Therefore we would prefer not to include this data.

Reviewer #3

We thank the reviewer for their support of our manuscript.

A few small areas to improve this manuscript:

p. 6 like 139: "remain" should be "remaining"

We have fixed this typo.

Could the authors mention what is the phenotype of the 10% of pac-1 animals that die?

Yes. They die with pleotropic phenotypes not resembling those of our pac-1; lgl-1 double mutant embryos. We have added examples of these to Figure S1.

Based on the Supplemental figures, it made me curious to ask: Did the authors notice changes in dorsal epidermal fusions? Cadherin normally disappears in the dorsal hyp7 cells at this time. Did the timing of the fusions change at all?

We haven't analyzed this in detail but our time-lapse videos show that dorsal fusions still take place and do not seem to be particularly delayed (overall development is slightly delayed but the delay in fusion is consistent with overall delay).

Again, curiosity driven by the Supplemental figures: did the authors notice defects in apical regions of internal organs, like the pharynx or intestine? The CDC-42 biosensor is asymmetrical in the developing intestine. See: DOI: 10.1242/bio.056911

We did not pay much attention to the intestine as PAC-1 is barely detectable in this tissue. The pharynx is formed, which we can easily detect in arrested embryos as we use GFP or BFP expressed under the myo-2 promoter to mark the deletion of pac-1. While we did not look closely, we do observe defects in pharynx development.

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Referee #3

Evidence, reproducibility and clarity

This manuscript by Jarosinska and colleagues addresses a long-standing mystery in the apical/basal polarity field: why LGL-1 and PAC-1/RhoGAP19D, which are essential in Drosophila, and in some tissue culture contexts, are not essential in C. elegans embryos.

The authors take an open-ended approach by using genetics, in the form of a genome wide RNAi screen, to find other proteins that enhance the mild phenotypes of lgl-1 mutant embryos. They uncover strong synthetic lethality when they reduce pac-1, a well-documented CDC-42 GAP that supports apical/basal polarity during early embryogenesis, and yet is also only partially required during embryogenesis.

The phenotypic analysis to understand why the embryos die when missing both lgl-1 and pac-1 leads to a careful analysis of known junctional molecules in C. elegans. Using newly made endogenously tagged junctional proteins, including DLG-1 and AFD, so that they can examine all three C. elegans apical junction complexes, the authors find a penetrant defect in the epidermal junctions as the embryos undergo elongation, an actomyosin dependent contractile event that dramatically reshapes the embryos into long, skinny tubes. With disorganized junctions, the embryos die due to ruptures, or hernias, as shown in the Supplemental Movie 2. In addition, and quite excitingly, the apical domains of the embryos are expanded. These defects are then partially rescued by removing CDC-42 or aPKC using RNAi depletion.

Major comments:

The claims and conclusions are supported by the data.

The data is presented in such a way that it is easy to understand what was done, and how measurements were obtained and evaluated.

Rigorous documentation of how the strains were built and how the genome wide RNAi screen was conducted is included in the Supplemental files.

Beautiful use of CRISPR to do the genetics:

since when they made the deletion of lgl-1 they replaced the coding sequence with GFP, they could use GFP to count the animals carrying the deletion in their double mutant analysis with pac-1 deletion mutants.

Figures are very nicely done.

The writing is clear.

Minor comments:

A few small areas to improve this manuscript:

p. 6 like 139: "remain" should be "remaining"

Could the authors mention what is the phenotype of the 10% of pac-1 animals that die?

Based on the Supplemental figures, it made me curious to ask: Did the authors notice changes in dorsal epidermal fusions? Cadherin normally disappears in the dorsal hyp7 cells at this time. Did the timing of the fusions change at all?

Again, curiosity driven by the Supplemental figures: did the authors notice defects in apical regions of internal organs, like the pharynx or intestine? The CDC-42 biosensor is asymmetrical in the developing intestine. See: DOI: 10.1242/bio.056911

Significance

This study raises interesting and important questions for the general polarity field. Early embryos have hugely redundant methods to maintain apical/basal polarity, which in C. elegans masked the roles for lgl-1 and pac-1 at earlier events, like compaction, when apical/basal polarity is first established. However, during elongation, when healthy strong junctions are a requirement, the double mutant loss of LGL-1 and PAC-1 results in expanded apical domain, that is lethal.

The study will be of interest to the broader polarity community, and to developmental biologist interested in how the apical junctions are assembled and strengthened during morphogenesis. The Discussion does a good job of showing what aspects of this study are novel, and which support prior findings that suggested, for example, that PAC-1 may have roles independent of CDC-42. I appreciate the comment that our field needs more and more sensitive biosensors to fully address the changes of key polarity regulators.

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Referee #2

Evidence, reproducibility and clarity

Summary: This study focuses on the polarization of epidermal epithelial cells in C. elegans. Whereas the basolateral polarity protein is LGL-1 is required for epithelial polarity in flies, LGL-1 is dispensable for polarization and viability in C. elegans. Through a whole-genome RNAi screen, Jarosinska et al discover that the depletion of the RhoGAP PAC-1 is synthetically lethal with an lgl-1 deletion mutant. pac-1 lgl-1 double mutants have significant polarity defects in the epidermal epithelial, including mislocalization of junctional markers and expansion of the apical aPKC domain. As a result pac-1 lgl-1 double mutants fail to maintain surface epithelial and arrest development. Genetic interaction data suggest that increased CDC42 and aPKC activity in pac-1 lgl-1 contributes, as least in part, to the polarity defects and resulting embryonic lethality.

Major comments:

Very little of the imaging data are analyzed quantitatively, and in many cases it is not clear how many embryos were analyzed. While the images that are presented show clear defects, readers cannot determine how reproducible, strong or significant the phenotypes are. In particular, the data below should be quantified and, where possible, analyzed statistically:

• The frequency of the various junctional phenotypes shown in 2C
• The expansion of DLG-1::mCherry in pac-1 lgl-1 embryos should be quantified(related to Figure 2B). For example, the percentage of membrane (marked by PH::GFP) occupied by DLG-1 could be quantified.
• Similarly, the expansion of the aPKC domain should be quantified (Figure 3A).
• How many embryos were analyzed for each marker shown in Figure 2A, and what proportion showed the described phenotypes? This could be given in the text or in a panel.
• The frequency of the various junctional phenotypes shown in 4F.

Because the genetic perturbations used are global (either deletions or RNAi), it is not established whether PAC-1/LGL-1 act in epidermal epithelial cells per se (versus an earlier requirement that manifests in epidermal epithelial cells). While I agree that this is the most likely scenario, other mechanisms are possible. In particular, the overall GFP::aPKC levels appear notably higher in pac-1 lgl-1 embryos in Figure 3A. aPKC levels should be quantified to determine if this is true of pac-1 lgl-1 embryos. If so, couldn't that explain (or at least contribute to) the observed phenotypes?

Minor

Figure 4: For completeness, please include the embryonic viability of pac-1 lgl-1 +/- embryos treated with EV and cdc-42(RNAi), as was done for pac-1 lgl-1 pkc-3(ts) in Figure 4E. Presumably the increased proportion of viable embryos with the lgl-1 deletion allele is reflected in an overall increase in embryonic viability.

The orientation of the inset images in Figures 2C, 3A and 3D is confusing. An illustration showing how these images are oriented relative to each other would be helpful.

For completeness, it would be good to test whether lgl-1(delta) is also synthetically lethal with picc-1(RNAi) (Zilberman 2017).

Significance

LGL-1 is a conserved polarity protein that is essential for viability in Drosophila. In contrast, lgl-1 mutants are viable and have weak polarity phenotypes in C. elegans. A previous study showed that LGL-1 acts redundantly with the posterior polarity proteins PAR-2 during establishment of anterior/posterior polarity in the one-cell worm embryo. Here, Jarosinska et al show that LGL-1 acts redundantly with another protein, the RhoGAP protein PAC-1, in the polarization of the embryonic epidermal epithelial. The strength of this study is the identification of redundant roles for PAC-1 and LGL-1, the apparent strength of the polarity defects in the double mutant and the broader implication that LGL-1 may act in a range of redundant, cell/tissue specific pathways to regulate polarity. The primary weakness of this study is the lack of quantification. Additionally, the aPKC and CDC42 genetic interaction data hint at potential pathways, but fall short of establishing LGL-1's or PAC-1's mechanism of action.

Advance: This works identifies a redundant genetic interaction between LGL-1 and PAC-1. While the data require additional quantification, the phenotypes presented appear clear and strong. Although the molecular mechanism by which LGL-1 and PAC-1 act is not well established in the current work, the core observation is significant and should provide a foundation for future studies dissecting the molecular mechanisms.

Audience: This work will be of interest to a broad audience. LGL-1 is conserved and its role in cell polarization and epithelial polarity is very actively studied, including in mammalian systems.

Field of expertise. C elegans embryonic development; cell polarity.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Jarosinska and colleagues address the roles of two polarity regulators, pac-1 and lgl-1, in C. elegans epidermal polarity. Loss of function mutations in either of these gene individually does not block polarization, but through a genome-wide RNAi screen, the authors find that pac-1 and lgl-1 enhance each other to cause apical-basal polarity defects and arrest during epidermal morphogenesis. The remainder of the paper focuses on testing genetic interactions between both proteins and AJ proteins (HMP-1) as well as apical proteins (CDC-42, PKC-3). These experiments reveal some interesting differences in how lgl-1 and pac-1 interface with junctional proteins (pac-1 enhances hmp-1 but lgl-1 does not) and apical proteins (lgl-1 suppresses pkc-3 or cdc-42 partial loss but pac-1 does not).

Minor comments:

1. Are the lgl-1; pac-1 M-Z- double mutants dead? Only the phenotype of pac-1(M-Z-); lgl-1 (M+Z-) is shown. In figures and text throughout, it should be clear whether mutants are referring to zygotic loss or both maternal and zygotic loss, as this distinction could have major implications on the interpretation of experiments.
2. In Figure 1C, it would be more appropriate to show a fully elongated WT embryo to contrast with arrested elongation in mutant embryos.
3. Is the lateral spread of DLG-1 in double mutant embryos a result of failure to polarize DLG-1, or failure to maintain polarity? This should be straightforward to address in higher time resolution movies.
4. The lack of enhancement of hmp-1(fe4) by lgl-1(RNAi) is quite interesting, given that pac-1 does enhance hmp-1(fe4). To rule out the possibility that this result stems from incomplete lgl-1 RNAi, this experiment should be repeated using the lgl-1 null mutant.
5. Related to point 4, do pac-1 or lgl-1 null mutants enhance partial knockdown of junction protein DLG-1, or is this effect (of pac-1) specific to HMP-1/AJs?
6. Does lgl-1 loss affect PAC-1 protein localization and vice versa?

Significance

Overall, the manuscript provides additional insights into apical-basal polarization in C. elegans and demonstrates that lgl-1 is likely working in a similar way as in Drosophila, despite the lack of a phenotype in single lgl-1 mutants. I found the experiments to be done rigorously and interpretations of the data appropriate. All of my suggestions on improving the manuscript are minor; suggested experiments should be viewed as optional ways to strengthen the conclusions/impact of the study.

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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

Summary

In this paper, Wang and Shu et al. investigate the extent to which the negative binomial (NB) distribution captures the statistical properties of single-cell like count data and the effects of using this model to interpret biophysical parameters. Assuming an underlying telegraph model of transcription, they demonstrate how the NB can produce similar if not equivalent fits to simulated data from various parameter regimes, regimes which can, notably, fall outside of the bursty transcription limit in which the telegraph model is known to have a NB form. The authors then assess how model selection favors the NB or Poisson models over the underlying telegraph model, and how technical noise can lead to greater selection/representation of the NB over the parameter regime. Finally, they demonstrate how the broader applicability of the NB impacts inference of burst size and frequency (commonly inferred from NB fits on single-cell data), preserving relative rather than absolute information.

The authors use both method of moments and MLE-based approaches to obtain and compare model fits over the same parameter regimes. They also develop the aeBIC metric which balances parametric complexity and distributional similarity to the desired, ground truth distribution, to more quickly approximate the BIC (used for model selection).

Major comments:

The likelihood of model fits is used as a main criteria for model selection and comparison (e.g., in the BIC/aeBIC metrics), however it is possible that analysis of the curvature of the likelihood may suggest greater uncertainty/less information about parameter estimates for the different statistical models across the transcriptional regimes tested. Since a major component of this study is to demonstrate to readers that nuanced model selection is important for interpreting single-cell data, it would support these efforts to see if the telegraph versus NB model fits, for example, demonstrate differences in their respective Hessian matrices for the MLE estimates. This would help determine, for those interested in comparing these fits on their data, if there is potential here to distinguish the more optimal/true model or not (i.e., what the extent of the limitations are). The authors describe how in the infinite limit of N_sigma the NB and telegraph models converge to the same distribution, which provides another biological scenario outside transcriptional bursting where the NB can be interpreted as a good statistical model. However, though many parameter regimes are possible not all are observed in real data. Thus for readers to understand how likely these regimes are to be present in the data it would be helpful to discuss in what biological scenarios such a limit may appear and if it is likely to be a common instance, etc (perhaps given the ranges of on/off times observed in the literature https://pmc.ncbi.nlm.nih.gov/articles/PMC10860890/). This would parallel the discussion in the study on the bursty transcription model, often described in the literature as a widespread phenomenon. The p_cap parameter is described as representing technical capture and affords the conclusion in the Discussion that the NB can improve capture of technical noise beyond the biological noise in the system. However, as mentioned later in the Discussion, this effect could also arise from cell to cell differences in transcription rate (extrinsic, biological noise), which cannot be distinguished in this model. This point should be made clearer earlier on, as without use of control genes/spike-ins/etc we cannot distinguish the biological and technical components encompassed by the p_cap term (i.e., whether or not a spread in total UMIs observed over droplets is due to biological or technical capture differences). Since the aeBIC is being presented as a new, faster method in this study, the timing and memory usage in performing these calculations, for each model, should be presented somewhere. The Methods should also have a more explicit description of the steps/tools used to calculate the aeBIC.

Minor comments:

Figure S4 mentioned comparison of scRNA-seq with smFISH data to approximate p_cap, however given that smFISH data would have its own technical biases it does not seem exactly clear how a map from smFISH to scRNA-seq would work such as to illuminate the gap incurred by technical bias/capture. Perhaps previous literature/methods doing this can be cited here, or this idea can be fleshed out in the Discussion text for readers interested in better estimating p_cap. In Figure 4 the pink color of the Poisson in c is hard to see, and it may be easier to write the names of the different models in the respective regions that they cover (similarly in Figure 5 c) For Figure 8, it may be easier for the reader to interpret the several plots in a row by repeating the x-axis labels under each set of plots and collating all the legend labels into one box somewhere near the first plots.

Significance

General assessment: Overall, the paper is a clear and concise view on the use of the NB in analysis of sparse, transcriptomic count data, the potential effects of technical and biological noise on the pertinence of the NB as the statistical representation, and the impacts on user interpretation of biophysical parameters from these model fits. This study is useful for both biologists and computational scientists looking to gain mechanistic insight from single-cell data.

The strength of the paper is that the methodology is straightforward and uses simple numerical experiments to demonstrate how and when several common distributions can describe the type of data we encounter in single-cell genomics. They additionally connect these results to common biological interpretations from single-cell measurements and outline regimes in which inferences are likely to be incorrect.

The paper could benefit from more discussion on the biological interpretations of the findings and regimes analyzed, particularly to help readers interested in how this impacts their data analysis. Supplemental analysis on whether other criteria could potentially distinguish the models in question would also help support the conclusions of model selection/identifiability and if other properties of these model fits can be used for selection or not.

Advance: The study builds on others in the field by not just fitting several common models to this type of sparse, transcriptomic count data but also describing why these overlapping fits arise and how that affects biological interpretation. Often the focus is more on choosing a sufficient statistical representation without the underlying, mechanistic connections between the models. The results here are thus more technical and mechanistic in nature, describing both the theoretical connections between common single-cell count models and their biophysical interpretations.

Audience: This result is likely to be of interest to scientists performing data analysis and method development in single-cell genomics, particularly with mechanistic insight in mind. This would be more of interest within the domain of transcriptomics, but it also presents a methodology for studying limitations of identifiability in noisy systems which could be of interest to other biological domains.

My expertise is in developing representation learning methods and stochastic models of transcription for single-cell biology, which covers the classical models described in this study.

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Referee #2

Evidence, reproducibility and clarity

The study is generally well reasoned and thorough, and should be of interest to the community. My only critique relates to the treatment of extrinsic noise and the related discussion: Many studies have concluded that extrinsic noise (e.g., cell-to-cell variability in the transcription rate) is a larger contribution to noise in gene expression than intrinsic noise. (For example, see the seminal review by Raj and van Oudenaarden (PMID: 18957198) and early examples such as Raser and O'Shea: Raser JM, O'Shea EK. Science. 2004;304:1811. doi: 10.1126/science.1098641). For this reason, one must be careful in assuming that the telegraph model by itself fully captures biological variability. I believe this point could be more clearly made in the paper. Did the authors treat a case in which the gene undergoes state switching, but where there is also a significant contribution of extrinsic noise, for example, through variability in the transcription rate and/or other papers? I could not tell for sure if this was explicitly studied. This would be an important scenario to study, because it may be the most likely. I would have thought that this is the most biologically realistic scenario (i.e., strong contributions of both intrinsic and extrinsic noise, along with state switching). My prior assumption has been that the NB model is often empirically indicated because it somehow well captures this combination of intrinsic (including state switching) + extrinsic noise. Could the authors comment on whether this assumption is consistent with their findings? (Neither Case I or Case II in the manuscript captures this scenario). Related to the treatment of extrinsic noise, I was confused by this sentence: "Any variation in the effective transcription rate due to variability in the transcription rate (extrinsic noise on the transcription rate) between cells is indistinguishable from variability in the transcript capture probability and hence is automatically accounted for in our present method. " But doesn't the distribution of transcription rates vary significantly, depending on whether the variation comes from technical noise versus extrinsic biological variability? For example, one source of extrinsic biological variability is differences in RNA polymerase concentrations in different cells. Wouldn't one need to know what kind of distribution to use to capture these effects? In this case, I believe one would need to study various types of compound distributions, depending on the assumptions underlying the biological extrinsic variability.

Significance

This paper presents a thorough study of the conditions under which the negative binomial model of transcript distributions can map onto other widely used models, namely the telegraph model of stochastic gene expression. The study is generally well reasoned and thorough, and should be of interest to the community (namely: single cell transcriptomics community, bio mathematicians, biological noise community).

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Referee #1

Evidence, reproducibility and clarity

The authors present an investigation into the surprising effectiveness of the negative-binomial distribution in modelling transcript counts in single cell RNA sequencing experiments. With experimentally motivated ground-truth models that incorporate transcriptional bursting, they show that when transcription activity is large compared to degradation these distributions coincide. With a novel model selection metric, they indicate the regions of parameter space in which the negative-binomial model is a good approximation to the underlying true model. With this procedure, they also indicate that transcriptional burst parameters are unlikely to be reconstructed by an effective negative-binomial function, but that nevertheless, relative rankings between genes can be identified robustly.

I would like to commend the authors on an interesting and fairly comprehensive investigation on a topic of considerable importance in the interpretation of single cell RNA sequencing experiments, and on a well written paper. I have no major comments on issues that affect the conclusions of the paper, although I have a few minor suggestions that might aid reader's understanding of the results and their applicability.

General

It would be nice to have a comparison with some real data for the burst frequency and size, just to indicate to the reader how important these regions are compared to what might be measured. For example, if most genes are outside of the region that does not accommodate the NB distribution, then the conclusion is quite different than if most real counts are unlikely to accommodated by the NB.

Inter-cellular variability of transcription dynamics is quite a significant point of interest, so it would be good to have stated earlier that this is not considered, with the mitigation that is noted later. This is particularly important given that in the introduction, the cases mentioned seem to imply that an NB distribution would be more likely with higher inter-cellular variability.

Introduction

It would be nice to have a bit more detail here, for example on what UMIs are, and what the parameters of the NB distribution represent in general.

For smFISH, I would have thought that the more simple explanation is that the NB is often the simplest distribution with some overdispersion that fits the data, and the parameters don't necessarily need to be biologically interpretable?

It's noted later that the capture probability of modern RNASeq protocols can be ~0.3, which doesn't seem very different compared to 0.7-0.9 of smFISH, so some context here would be good.

Results

Eq 1: I don't think you lose anything by giving the Pochammer symbol and Kummer confluent geometric function explicitly here, and it would make it it a lot easier to read. That said, this equation also seems to come out of nowhere, so a reference would be nice.

I think the moment matching is reasonably convincing, but it might require a little more explicit motivation for a more general audience.

Thm. 1: Do these converge at similar rates, and if not, does that have any implications for the interpretation of the comparisons (as these are evaluated with specific values)? This might be worth a short comment.

Fig 3. In the description for this in the text, it would be nice to have an expression of the KL divergence (and what order the arguments are in), for anyone unfamiliar.

The discussion of the aeBIC seems a bit circuitous. A reasonable prior intention might be to average (or apply a voting function) to individual BIC values, rather than the aeBIC constructed here. And in fact the text goes on to note after the description that this is a good estimate of the expectation of the BIC after all, with some computational advantages. So it might be better to have a more straightforward presentation where this is proposed as an approximation to the expectation of the BIC in the first place.

Section 2.4: The intro to this section could do with a bit more background of the capture, PCR, sequencing, etc, stages, and what exactly the data generated here represents. Otherwise the discussion of zero inflation and UMIs is a little confusing.

It would also be nice to have a comment here on the effect of sequencing depth, or similar (compared to capture probability), even if this wouldn't change the interpretation.

Significance

The paper provides novel arguments towards the support of the negative-binomial distribution in describing single cell RNA sequencing data, with particular relevance to transcriptional bursting observed in numerous datasets. The paper follows from some notable prior work in the field, and integrates these into a more consistent description, particularly in relation to newer techniques such as UMIs.

The ubiquity of the negative-binomial distribution means that these arguments will be of relevance to those that perform theoretical or statistical modelling of single cell RNA sequencing data, and theoretically justifies many widely held assumptions. However, the paper does not make any reference to specific reference datasets or commonly observed values, so where in the parameter space data likely lies would still need to be evaluated on a case-by-case basis.

My expertise is in mathematical modelling and statistics, with some experience of the analysis of single cell RNA sequencing data.

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Reply to the reviewers

The PDF version of point-by-point response includes figures (I, II, III,... IX) that are not included in the manuscript nor in this post but serve to illustrate and clarify our replies to the reviewers' comments.

Dear Editor,

Many thanks for forwarding the comments from reviewers #1-#4 regarding our manuscript (Preprint #RC-2025-03087144), entitled "HIV-1 Envelope glycoprotein modulates CXCR4 clustering and dynamics on the T cell membrane", by Quijada-Freire A. et al.

We have carefully reviewed all reviewer comments and prepared our specific, detailed responses. Alongside this, we have created a revised version of the manuscript to post them on BioRxiv, and we are pleased to announce that we will transfer this new version to an affiliate journal for consideration.

Reviewer #1

Thank you very much for considering that our manuscript evaluates an important question and that the reagents used are well prepared and characterized. We also much appreciate that you consider the information generated as potentially useful for those studying HIV infection processes and strategies to prevent infection.

• While a single particle tracking routine was applied to the data, it's not clear how the signal from a single GFP was defined and if movement during the 100 ms acquisition time impacts this. My concern would be that the routine is tracking fluctuations, and these are related to single particle dynamics, it appears from the movies that the density or the GFP tagged receptors in the cells is too high to allow clear tracking of single molecules. SPT with GFP is very difficult due to bleaching and relatively low quantum yield. Current efforts in this direction that are more successful include using SNAP tags with very photostable organic fluorophores. The data likely does mean something is happening with the receptor, but they need to be more conservative about the interpretation. *

Some of the paradoxical effects might be better understood through deeper analysis of the SPT data, particularly investigation of active transport and more detailed analysis of "immobile" objects. Comments on early figures illustrate how this could be approached. This would require selecting acquisitions where the GFP density is low enough for SPT and performing a more detailed analysis, but this may be difficult to do with GFP.

When the authors discuss clusters of 3, how do they calibrate the value of GFP and the impact of diffusion on the measurement. One way to approach this might be single molecules measurements of dilute samples on glass vs in a supported lipid bilayer to map the streams of true immobility to diffusion at >1 µm2/sec.

We fully understand the reviewer's apprehensions regarding the application of these high-end biophysical techniques, in particular the associated complexity of the data analysis. We provide below extensive explanations on our methodology, which we hope will satisfactorily address all of the reviewer's concerns.

We would first like to emphasize that the experimental conditions and the quantitative analysis used in our current experiments are similar to the established protocols and methodologies applied by our group previously (Martinez-Muñoz et al. Mol. Cell, 2018; García-Cuesta et al. PNAS, 2022; Gardeta et al. Frontiers in Immunol., 2022; García-Cuesta et al.eLife, 2024; Gardeta et al. Cell. Commun. Signal., 2025) and by others (Calebiro et al. PNAS, 2013; Jaqaman et al. Cell,2011; Mattila et al. Immunity, 2013; Torreno-Pina et al. PNAS, 2014; Torreno-Pina et al. PNAS, 2016).

As SPT (single-particle tracking) experiments require low-expressing conditions in order to follow individual trajectories (Manzo & García-Parajo Rep. Prog. Phys., 2015), we transiently transfected Jurkat CD4+ cells with CXCR4-AcGFP or CXCR4R334X-AcGFP. At 24 h post-transfection, cells expressing low CXCR4-AcGFP levels were selected by a MoFlo Astrios Cell Sorter (Beckman-Coulter) to ensure optimal conditions for SPT. Using Dako Qifikit (DakoCytomation), we quantified the number of CXCR4 receptors and found ∼8,500 - 22,000 CXCR4-AcGFP receptors/cell, which correspond to a particle density ∼2 - 4.5 particles/mm2 (Figure I, only for review purposes) and are similar to the expression levels found in primary human lymphocytes.

These cells were resuspended in RPMI supplemented with 2% FBS, NaPyr and L-glutamine and plated on 96-well plates for at least 2 h. Cells were centrifuged and resuspended in a buffer with HBSS, 25 mM HEPES, 2% FBS (pH 7.3) and plated on glass-bottomed microwell dishes (MatTek Corp.) coated with fibronectin (FN) (Sigma-Aldrich, 20 mg/ml, 1 h, 37{degree sign}C). To observe the effect of the ligand, we coated dishes with FN + CXCL12; FN + X4-gp120 or FN + VLPs, as described in material and methods; cells were incubated (20 min, 37{degree sign}C, 5% CO2) before image acquisition.

For SPT measurements, we use a total internal reflection fluorescence (TIRF) microscope (Leica AM TIRF inverted) equipped with an EM-CCD camera (Andor DU 885-CS0-#10-VP), a 100x oil-immersion objective (HCX PL APO 100x/1.46 NA) and a 488-nm diode laser. The microscope was equipped with incubator and temperature control units; experiments were performed at 37{degree sign}C with 5% CO2. To minimize photobleaching effects before image acquisition, cells were located and focused using the bright field, and a fine focus adjustment in TIRF mode was made at 5% laser power, an intensity insufficient for single-particle detection that ensures negligible photobleaching. Image sequences of individual particles (500 frames) were acquired at 49% laser power with a frame rate of 10 Hz (100 ms/frame). The penetration depth of the evanescent field used was 90 nm.

We performed automatic tracking of individual particles using a very well established and common algorithm first described by Jaqaman (Jaqaman et al. Nat. Methods, 2008). Nevertheless, we would stress that we implemented this algorithm in a supervised fashion, i.e., we visually inspect each individual trajectory reconstruction in a separate window. Indeed, this algorithm is not able to quantify merging or splitting events.

We follow each individual fluorescence spot frame-by-frame using a three-by-three matrix around the centroid position of the spot, as it diffuses on the cell membrane. To minimize the effect of photon fluctuations, we averaged the intensity over 20 frames. Nevertheless, to assure the reviewer that most of the single molecule traces last for at least 50 frames (i.e., 5 seconds), we provide the following data and arguments. We currently measure the photobleaching times from individual CD86-AcGFP spots exclusively having one single photobleaching step to guarantee that we are looking at individual CD86-AcGFP molecules. The distribution of the photobleaching times is shown below (Figure II, only for review purposes). Fitting of the distribution to a single exponential decay renders a t0 value of ~5 s. Thus, with 20 frames averaging, we are essentially measuring the whole population of monomers in our experiments. As the survival time of a molecule before photobleaching will strongly depend on the excitation conditions, we used low excitation conditions (2 mW laser power, which corresponds to an excitation power density of ~0.015 kW/cm2 considering the illumination region) and longer integration times (100 ms/frame) to increase the signal-to-background for single GFP detection while minimizing photobleaching.

To infer the stoichiometry of receptor complexes, we also perform single-step photobleaching analysis of the TIRF trajectories to establish the existence of different populations of monomers, dimers, trimers and nanoclusters and extract their percentage. Some representative trajectories of CXCR4-AcGFP with the number of steps detected are shown in new Supplementary Figure 1.

The emitted fluorescence (arbitrary units, a.u.) of each spot in the cells is quantified and normalized to the intensity emitted by monomeric CD86-AcGFP spots that strictly showed a single photobleaching step (Dorsch et al. Nat. Methods,2009). We have preferred to use CD86-AcGFP in cells rather than AcGFP on glass to exclude any potential effect on the different photodynamics exhibited by AcGFP when bound directly to glass. We have also previously shown pharmacological controls to exclude CXCL12-mediated receptor clustering due to internalization processes (Martinez-Muñoz et al. Mol. Cell, 2018) that, together with the evaluation of single photobleaching steps and intensity histograms, allow us to exclude the presence of vesicles in our data. Thus, the dimers, trimers and nanoclusters found in our data do correspond to CXCR4 molecules on the cell surface. Finally, distribution of monomeric particle intensities, obtained from the photobleaching analysis, was analyzed by Gaussian fitting, rendering a mean value of 980 {plus minus} 86 a.u. This value was then used as the monomer reference to estimate the number of receptors per particle in both cases, CXCR4-AcGFP and CXCR4R334X-AcGFP (new Supplementary Figure 1).

• I understand that the CXCL12 or gp120 are attached to the substrate with fibronectin for adhesion. I'm less clear how how that VLPs are integrated. Were these added to cells already attached to FN?*

For TIRF-M experiments, cells were adhered to glass-bottomed microwell dishes coated with fibronectin, fibronectin + CXCL12, fibronectin + X4-gp120, or fibronectin + VLPs. As for CXCL12 and X4-gp120, the VLPs were attached to fibronectin taking advantage of electrostatic interactions. To clarify the integration of the VLPs in these assays, we have stained the microwell dishes coated with fibronectin and those coated with fibronectin + VLPs with wheat germ agglutinin (WGA) coupled to Alexa647 (Figure III, only for review purposes) and evaluated the staining by confocal microscopy. These results indicate the presence of carbohydrates on the VLPs and are, therefore, indicative of the presence of VLPs on the fibronectin layer.

Moreover, it is important to remark that the effect of the VLPs on CXCR4 behavior at the cell surface observed by TIRF-M confirmed that the VLPs remained attached to the substrate during the experiment.

• Fig 1A- The classification of particle tracks into mobile and immobile is overly simplistic description that goes back to bulk FRAP measurements and it not really applicable to single molecule tracking data, where it's rare to see anything that is immobile and alive. An alternative classification strategy uses sub-diffusion, normal diffusion and active diffusion (or active transport) to descriptions and particles can transition between these classes over the tracking period. Fig 1B- this data might be better displayed as histograms showing distributions within the different movement classes.*

In agreement with the reviewer's commentary, the majority of the particles detected in our TIRF-M experiments were indeed mobile. However, we also detected a variable, and biologically appreciable, percentage of immobile particles depending on the experimental condition analyzed (Figure 1A in the main manuscript). To establish a stringent threshold for identifying these immobile particles under our specific experimental conditions, we used purified monomeric AcGFP proteins immobilized on glass coverslips. Our analysis demonstrated that 95% of these immobilized proteins showed a diffusion coefficient £0.0015 mm2/s; consequently, this value was established as the cutoff to distinguish immobile from mobile trajectories. While the observation of truly immobile entities in a dynamic, living system is rare, the presence of these particles under our conditions is biologically significant. For instance, the detection of large, immobile receptor nanoclusters at the plasma membrane is entirely consistent with facilitating key cellular processes, such as enabling the robust signaling cascade triggered by ligand binding or promoting the crucial events required for efficient viral entry into the cells.

Regarding the mobile receptors (defined as those with D1-4 values exceeding 0.0015 mm2/s), we observed distinct diffusion profiles derived from mean square displacement (MSD) plots (Figure V) (Manzo & García-Parajo Rep. Prog. Phys., 2015), which were further classified based on motion, using the moment scaling spectrum (MSS) (Ewers et al. PNAS, 2005). Under all experimental conditions, the majority of mobile particles, ∼85%, showed confined diffusion: for example under basal conditions, without ligand addition, ∼90% of mobile particles showed confined diffusion, ∼8.5% showed Brownian-free diffusion and ∼1.5% exhibited directed motion (new Supplementary Figure 5A in the main manuscript). These data have been also included in the revised manuscript to show, in detail, the dynamic parameters of CXCR4.

Due to the space constraints, it is very difficult to include all the figures generated. However, to ensure comprehensive assessment and transparency (for the purpose of this review), we have included below representative plots of the MSD values as a function of time from individual trajectories, showing different types of motion obtained in our experiments (Figure IV, only for review purposes).

• Fig 1C,D- It would be helpful to see a plot of D vs MSI at a single particle level. In comparing C and D I'm surprised there is not a larger difference between CXCL12 and X4-gp120. It would also be very important to see the behaviour of X4-gp120 on the CXCR4 deficient Jurkat that would provide a picture of CD4 diffusion. The CXCR4 nanoclustering related to the X4-gp120 could be dominated by CD4 behaviour.*

As previously described, all analyses were performed under SPT conditions (see previous response to point 1 in this reply). Figure 1C details the percentage of oligomers (>3 receptors/particle) calibrated using Jurkat CD4+ cells electroporated with monomeric CD86-AcGFP (Dorsch et al. Nat. Methods, 2009). The monomer value was determined by analyzing photobleaching steps as described in our previous response to point 1.

In our experiments, we observed a trend towards a higher number of oligomers upon activation with CXCL12 compared with X4-gp120. This trend was further supported by measurements of Mean Spot Intensity. However, the values are also influenced by the number of larger spots, which represents a minor fraction of the total spots detected.

The differences between the effect triggered by CXCL12 or X4-gp120 might also be attributed to a combination of factors related to differences in ligand concentration, their structure, and even to the technical requirements of TIRF-M. Both ligands are in contact with the substrate (fibronectin) and the specific nature of this interaction may differ between both ligands and influence their accessibility to CXCR4. Moreover, the requirement of the prior binding of gp120 to CD4 before CXCR4 engagement, in contrast to the direct binding of CXCL12 to CXCR4, might also contribute to the differences observed.

We previously reported that CXCL12-mediated CXCR4 dynamics are modulated by CD4 co-expression (Martinez-Muñoz et al. Mol. Cell, 2018). We have now detected the formation of CD4 heterodimers with both CXCR4 and CXCR4R334X, and found that these conformations are influenced by gp120-VLPs. In the present manuscript, we did not focus on CD4 clustering as it has been extensively characterized previously (Barrero-Villar et al. J. Cell Sci., 2009; Jiménez-Baranda et al. Nat. Cell. Biol., 2007; Yuan et al. Viruses, 2021). Regarding the investigation of the effects of X4-gp120 on CXCR4-deficient Jurkat cells, which would provide a picture of CD4 diffusion, we would note that a previous report has already addressed this issue using single-molecule super-resolution imaging, and revealed that CD4 molecules on the cell membrane are predominantly found as individual molecules or small clusters of up to 4 molecules, and that the size and number of these clusters increases upon virus binding or gp120 activation (Yuan et al. Viruses, 2021).

• Fig S1D- This data is really interesting. However, if both the CD4 and the gp120 have his tags they need to be careful as poly-His tags can bind weakly to cells and increasing valency could generate some background. So, they should make the control is fair here. Ideally, using non-his tagged person of sCD4 and gp120 would be needed ideal or they need a His-tagged Fab binding to gp120 that doesn't induce CXCR4 binding.*

New Supplementary Figure 2D shows that X4-gp120 does not bind Daudi cells (these cells do not express CD4) in the absence of soluble CD4. While the reviewer is correct to state that both proteins contain a Histidine Tag, cell binding is only detected if X4-gp120 binds sCD4. Nonetheless, we have included in the revised Supplementary Figure 2D a control showing the negative binding of sCD4 to Daudi cells in the absence of X4-gp120. Altogether, these results confirm that only sCD4/X4-gp120 complexes bind these cells.

• Fig S4- Panel D needs a scale bar. I can't figure out what I'm being shown without this.*

Apologies. A scale bar has been included in this panel (new Supplementary Figure 6D).

Reviewer #2

• This study is well described in both the main text and figures. Introduction provides adequate background and cites the literature appropriately. Materials and Methods are detailed. Authors are careful in their interpretations, statistical comparisons, and include necessary controls in each experiment. The Discussion presents a reasonable interpretation of the results. Overall, there are no major weaknesses with this manuscript.*

We very much appreciate the positive comments of the reviewer regarding the broad interest and strength of our work.

• NL4-3deltaIN and immature HIV virions are found to have less associated gp120 relative to wild-type particles. It is not obvious why this is the case for the deltaIN particles or genetically immature particles. Can the authors provide possible explanations? (A prior paper was cited, Chojnacki et al Science, 2012 but can the current authors provide their own interpretation.)*

Our conclusion from the data is actually exactly the opposite. As shown in Figure 2D, the gp120 staining intensity was higher for NL4-3DIN particles (1,786 a.u.) than for gp120-VLPs (1,223 a.u.), indicating lower expression of Env proteins in the latter. Furthermore, analysis of gp120 intensity per particle (Figure 2E) confirmed that gp120-VLPs contained fewer gp120 molecules per particle than NL4-3DIN virions. These levels were comparable with, or even lower than, those observed in primary HIV-1 viruses (Zhu et al. Nature, 2006). This reduction was a direct consequence of the method used to generate the VLPs, as our goal was to produce viral particles with minimal gp120 content to prevent artifacts in receptor clustering that might occur using high levels of Env proteins in the VLPs to activate the receptors.

This misunderstanding may arise from the fact that we also compared Gag condensation and Env distribution on the surface of gp120-VLPs with those observed in genetically immature particles and integrase-defective NL4-3ΔIN virions, which served as controls. STED microscopy data revealed differences in Env distribution between gp120-VLPs and NL4-3ΔIN virions, supporting the classification of gp120-VLPs as mature particles (Figure 2 A,B).

Reviewer #3

We thank the reviewer for considering that our work offers new insights into the spatial organization of receptors during HIV-1 entry and infection and that the manuscript is well written, and the findings significant.

• For mechanistic basis of gp120-CXCR4 versus CXCL12-CXCR4 differences. Provide additional structural or biochemical evidence to support the claim that gp120 stabilises a distinct CXCR4 conformation compared to CXCL12. If feasible, include molecular modelling, mutagenesis, or cross-linking experiments to corroborate the proposed conformational differences.*

We appreciate the opportunity to clarify this point. The specific claim that gp120 stabilizes a conformation of CXCR4 that is distinct from the CXCL12-bound state was not explicitly stated in our manuscript, although we agree that our data strongly support this possibility. It is important to consider that CXCL12 binds directly to CXCR4, whereas gp120 requires prior sequential binding to CD4, and its subsequent interaction is with a CXCR4 molecule that is already forming part of the CD4/CXCR4 complex, as demonstrated by our FRET experiments and supported by previous studies (Zaitseva et al. J. Leuk. Biol., 2005; Busillo & Benovic Biochim. Biophys. Acta, 2007; Martínez-Muñoz et al. PNAS, 2014). This difference makes it inherently complex to compare the conformational changes induced by gp120 and CXCL12 on CXCR4.

However, our findings show that both stimuli induce oligomerization of CXCR4, a phenomenon not observed when mutant CXCR4R334X was exposed to the chemokine CXCL12 (García-Cuesta et al. PNAS, 2022).

1. CXCL12 induced oligomerization of CXCR4 but did not affect the dynamics of CXCR4R334X (Martinez-Muñoz et al. Mol. Cell, 2018; García-Cuesta et al. PNAS, 2022). By contrast, X4-gp120 and the corresponding VLPs-which require initial binding to CD4 to engage the chemokine receptor-stabilized oligomers of both CXCR4 and CXCR4R334X.

FRET analysis revealed distinct FRET50 values for CD4/CXCR4 (2.713) and CD4/CXCR4R334X (0.399) complexes, suggesting different conformations for each complex. Consistent with previous reports (Balabanian et al. Blood, 2005; Zmajkovicova et al. Front. Immunol., 2024; García-Cuesta et al. PNAS, 2022), the molecular mechanisms activated by CXCL12 are distinct when comparing CXCR4 with CXCR4R334X. For instance, CXCL12 induces internalization of CXCR4, but not of mutant CXCR4R334X. Conversely, X4-gp120 triggers approximately 25% internalization of both receptors. Similarly, CXCL12 does not promote CD4 internalization in cells co-expressing CXCR4 or CXCR4R334X, whereas X4-gp120 does, although CD4 internalization was significantly higher in cells co-expressing CXCR4.

These findings suggest that CD4 influences the conformation and the oligomerization state of both co-receptors. To further support this hypothesis, we have conducted new in silico molecular modeling of CD4 in complex with either CXCR4 or its mutant CXCR4R334X using AlphaFold 3.0 (Abramson et al. Nature, 2024). The server was provided with both sequences, and the interaction between the two molecules for each protein was requested. It produced a number of solutions, which were then analyzed using the software ChimeraX 1.10 (Meng et al. Protein Sci., 2023). CXCR4 and its mutant, CXCR4R334X bound to CD4, were superposed using one of the CD4 molecules from each complex, with the aim of comparing the spatial positioning of CD4 molecules when interacting with CXCR4.

As illustrated in Figure V (only for review purposes), the superposition of the CD4/CXCR4 complexes was complete. However, when CD4/CXCR4 complexes were superimposed with CD4/CXCR4R334X complexes using the same CD4 molecule as a reference, indicated by an arrow in the figure, a clear structural deviation became evident. The main structural difference detected was the positioning of the CD4 transmembrane domains when interacting with either the wild-type or mutant CXCR4. While in complexes with CXCR4, the angle formed by the lines connecting residues E416 at the C-terminus end of CD4 with N196 in CXCR4 was 12{degree sign}, for the CXCR4R334X complex, this angle increased to 24{degree sign}, resulting in a distinct orientation of the CD4 extracellular domain (Figure VI, only for review purposes).

To further analyze the models obtained, we employed PDBsum software (Laskowski & Thornton Protein Sci., 2021) to predict the CD4/CXCR4 interface residues. Data indicated that at least 50% of the interaction residues differed when the CD4/CXCR4 interaction surface was compared with that of the CD4/CXCR4R334X complex (Figure VII, only for review purposes). It is important to note that while some hydrogen bonds were present in both complex models, others were exclusive to one of them. For instance, whereas Cys394(CD4)-Tyr139 and Lys299(CD4)-Glu272 were present in both CD4/CXCR4 and CD4/CXCR4R334X complexes, the pairs Asn337(CD4)-Ser27(CXCR4R334X) and Lys325(CD4)-Asp26(CXCR4R334X) were only found in CD4/CXCR4R334X complexes.

These findings, which are consistent with our FRET results, suggest distinct interaction surfaces between CD4 and the two chemokine receptors. Overall, these results are compatible with differences in the spatial conformation adopted by these complexes.

• For Empty VLP effects on CXCR4 dynamics: Explore potential causes for the observed effects of Env-deficient VLPs. It's valuable to include additional controls such as particles from non-producer cells, lipid composition analysis, or blocking experiments to assess nonspecific interactions. *

As VLPs are complex entities, we thought that the relevant results should be obtained comparing the effects of Env(-) VLPs with gp120-VLPs. Therefore, we would first remark that regardless of the effect of Env(-) VLPs on CXCR4 dynamics, the most evident finding in this study is the strong effect of gp120-VLPs compared with control Env(-) VLPs. Nevertheless, regarding the effect of the Env(-) VLPs compared with medium, we propose several hypotheses. As several virions can be tethered to the cell surface via glycosaminoglycans (GAGs), we hypothesized that VLPs-GAGs interactions might indirectly influence the dynamics of CXCR4 and CXCR4R334X at the plasma membrane. Additionally, membrane fluidity is essential for receptor dynamics, therefore VLPs interactions with proteins, lipids or any other component of the cell membrane could also alter receptor behavior. It is well known that lipid rafts participate in the interaction of different viruses with target cells (Nayak & Hu Subcell. Biochem., 2004; Manes et al. Nat. Rev. Immunol., 2003; Rioethmullwer et al. Biochim. Biophys. Acta, 2006) and both the lipid composition and the presence of co-expressed proteins modulate ligand-mediated receptor oligomerization (Gardeta et al. Frontiers in Immunol., 2022; Gardeta et al. Cell. Commun. Signal., 2025). We have thus performed Raster Image Correlation Spectroscopy (RICS) analysis to assess membrane fluidity through membrane diffusion measurements on cells treated with Env(-) VLPs.

Jurkat cells were labeled with Di-4-ANEPPDHG and seeded on FN and on FN + VLPs prior to analysis by RICS on confocal microscopy. The results indicated no significant differences in membrane diffusion under the treatment tested, thereby discarding an effect of VLPs on overall membrane fluidity (Figure VIII, only for review purposes).

Nonetheless, these results do not rule out other non-specific interactions of Env(-) VLPs with membrane proteins that could affect receptor dynamics. For instance, it has been reported that C-type lectin DC-SIGN acts as an efficient docking site for HIV-1 (Cambi et al. J. Cell. Biol., 2004; Wu & KewalRamani Nat. Rev. Immunol., 2006). However, a detailed investigation of these possible mechanisms is beyond the scope of this manuscript.

• For Direct link between clustering and infection efficiency - Test whether disruption of CXCR4 clustering (e.g., using actin cytoskeleton inhibitors, membrane lipid perturbants, or clustering-deficient mutants) alters HIV-1 fusion or infection efficiency*.

Designing experiments using tools that disrupt receptor clustering by interacting with the receptors themselves is difficult and challenging, as these tools bind the receptor and can therefore alter parameters such as its conformation and/or its distribution at the cell membrane, as well as affect some cellular processes such as HIV-1 attachment and cell entry. Moreover, effects on actin polymerization or lipids dynamics can affect not only receptor clustering but also impact on other molecular mechanisms essential for efficient infection.

Many previous reports have, nonetheless, indirectly correlated receptor clustering with cell infection efficiency. Cholesterol plays a key role in the entry of several viruses. Its depletion in primary cells and cell lines has been shown to confer strong resistance to HIV-1-mediated syncytium formation and infection by both CXCR4- and CCR5-tropic viruses (Liao et al. AIDS Res. Hum. Retrovisruses, 2021). Moderate cholesterol depletion also reduces CXCL12-induced CXCR4 oligomerization and alters receptor dynamics (Gardeta et al. Cell. Commun. Signal., 2025). By restricting the lateral diffusion of CD4, sphingomyelinase treatment inhibits HIV-1 fusion (Finnegan et al. J. Virol., 2007). Depletion of sphingomyelins also disrupts CXCL12-mediated CXCR4 oligomerization and its lateral diffusion (Gardeta et al. Front Immunol., 2022). Additional reports highlight the role of actin polymerization at the viral entry site, which facilitates clustering of HIV-1 receptors, a crucial step for membrane fusion (Serrano et al. Biol. Cell., 2023). Blockade of actin dynamics by Latrunculin A treatment, a drug that sequesters actin monomers and prevents its polymerization, blocks CXCL12-induced CXCR4 dynamics and oligomerization (Martínez-Muñoz et al. Mol. Cell, 2018).

Altogether, these findings strongly support our hypothesis of a direct link between CXCR4 clustering and the efficiency of HIV-1 infection.

• CD4/CXCR4 co-endocytosis hypothesis - Support the proposed model with direct evidence from live-cell imaging or co-localization experiments during viral entry. Clarification is needed on whether internalization is simultaneous or sequential for CD4 and CXCR4.*

When referring to endocytosis of CD4 and CXCR4, we only hypothesized that HIV-1 might promote the internalization of both receptors either sequentially or simultaneously. The hypothesis was based in several findings:

1) Previous studies have suggested that HIV-1 glycoproteins can reduce CD4 and CXCR4 levels during HIV-1 entry (Choi et al. Virol. J., 2008; Geleziunas et al. FASEB J, 1994; Hubert et al. Eur. J. Immunol., 1995).

2) Receptor endocytosis has been proposed as a mechanism for HIV-1 entry (Daecke et al. J. Virol., 2005; Aggarwal et al.Traffick, 2017; Miyauchi et al. Cell, 2009; Carter et al. Virology, 2011).

3) Our data from cells activated with X4-gp120 demonstrated internalization of CD4 and chemokine receptors, which correlated with HIV-1 infection in PBMCs from WHIM patients and healthy donors.

4) CD4 and CXCR4 have been shown to co-localize in lipid rafts during HIV-1 infection (Manes et al. EMBO Rep., 2000; Popik et al. J. Virol., 2002)

5) Our FRET data demonstrated that CD4 and CXCR4 form heterocomplexes and that FRET efficiency increased after gp120-VLPs treatment.

We agree with the reviewer that further experiments are required to test this hypothesis, however, we believe that this is beyond the scope of the current manuscript.

Minor Comments:

• The conclusions rely solely on the HXB2 X4-tropic Env. It would strengthen the study to assess whether other X4 or dual-tropic strains induce similar receptor clustering and dynamics.*

The primary goal of our current study was to investigate the dynamics of the co-receptor CXCR4 during HIV-1 infection, motivated by previous reports showing CD4 oligomerization upon HIV-1 binding and gp120 stimulation (Yuan et al.Viruses, 2021). We initially used a recombinant X4-gp120, a soluble protein that does not fully replicate the functional properties of the native HIV-1 Env. Previous studies have shown that Env consists of gp120 trimers, which redistribute and cluster on the surface of virions following proteolytic Gag cleavage during maturation (Chojnacki et al. Nat. Commun., 2017). An important consideration in receptor oligomerization studies is the concentration of recombinant gp120 used, as it does not accurately reflect the low number of Env trimers present on native HIV-1 particles (Hart et al. J. Histochem. Cytochem., 1993; Zhu et al. Nature, 2006). To address these limitations, we generated virus-like particles (VLPs) containing low levels of X4-gp120 and repeated the dynamic analysis of CXCR4. The use of primary HIV-1 isolates was limited, in this project, to confirm that PBMCs from both healthy donors and WHIM patients were equally susceptible to infection. This result using a primary HIV-1 virus supports the conclusion drawn from our in vitroapproaches. We thus believe that although the use of other X4- and dual-tropic strains may complement and reinforce the analysis, it is far beyond the scope of the current manuscript.

• Given the observed clustering effects, it would be valuable to explore whether gp120-induced rearrangements alter epitope exposure to broadly neutralizing antibodies like 17b or 3BNC117. This would help connect the mechanistic insights to therapeutic relevance.*

As 3BNC117, VRC01 and b12 are broadly neutralizing mAbs that recognize conformational epitopes on gp120 (Li et al. J. Virol., 2011; Mata-Fink et al. J. Mol. Biol., 2013), they will struggle to bind the gp120/CD4/CXCR4 complex and therefore may not be ideal for detecting changes within the CD4/CXCR4 complex. The experiment suggested by the reviewer is thus challenging but also very complex. It would require evaluating antibody binding in two experimental conditions, in the absence and in the presence of oligomers. However, our data indicate that receptor oligomerization is promoted by X4-gp120 binding, and the selected antibodies are neutralizing mAbs, so they should block or hinder the binding of gp120 and, consequently, receptor oligomerization. An alternative approach would be to study the neutralizing capacity of these mAbs on cells expressing CD4/CXCR4 or CD4/CXCR4R334X complexes. Variations in their neutralizing activity could be then extrapolated to distinct gp120 conformations, which in turn may reflect differences between CD4/CXCR4 and CD4/CXCR4R334X complexes.

We thus assessed the ability of the VRC01 and b12, anti-gp120 mAbs, which were available in our laboratory, to neutralize gp120 binding on cells expressing CD4/CXCR4 or CD4/CXCR4R334X. Specifically, increasing concentrations of each antibody were preincubated (60 min, 37ºC) with a fixed amount of X4-gp120 (0.05 mg/ml). The resulting complexes were then incubated with Jurkat cells expressing CD4/CXCR4 or CD4/CXCR4R334X (30 min, 37ºC) and, finally, their binding was analyzed by flow cytometry. Although we did not observe statistically significant differences in the neutralization capacity of b12 or VRC01 for the binding of X4-gp120 depending on the presence of CXCR4 or CXCR4334X, we observed a trend for greater concentrations of both mAbs to neutralize X4-gp120 binding in Jurkat CD4/CXCR4 cells than in Jurkat CD4/CXCR4R334X cells (Figure IX, only for review purposes).

These slight alterations in the neutralizing capacity of b12 and VRC01 mAbs may thus suggest minimal differences in the conformations of gp120 depending of the coreceptor used. We also detected that X4-gp120 and VLPs expressing gp120, which require initial binding to CD4 to engage the chemokine receptor, stabilized oligomers of both CXCR4 and CXCR4R334X, but FRET data indicated distinct FRET50 values between the partners, (2.713) for CD4/CXCR4 and (0.399) for CD4/CXCR4R334X (Figure 5A,B in the main manuscript). Moreover, we also detected significantly more CD4 internalization mediated by X4-gp120 in cells co-expressing CD4 and CXCR4 than in those co-expressing CD4 and CXCR4R334X (Figure 6 in the main manuscript). Overall these latter data and those included in Figures V, VI and VII of this reply, indicate distinct conformations within each receptor complexes.

• TIRF imaging limits analysis to the cell substrate interface. It would be useful to clarify whether CXCR4 receptor clustering occurs elsewhere, such as at immunological synapses or during cell-to-cell contact.*

In recent years, chemokine receptor oligomerization has gained significant research interest due to its role in modulating the ability of cells to sense chemoattractant gradients. This molecular organization is now recognized as a critical factor in governing directed cell migration (Martínez-Muñoz et al. Mol. Cell, 2018; García-Cuesta et al. PNAS, 2022, Hauser et al.Immunity, 2016). In addition, advanced imaging techniques such as single-molecule and super-resolution microscopy have been used to investigate the spatial distribution and dynamic behaviour of CXCR4 within the immunological synapse in T cells (Felce et al. Front. Cell Dev. Biol., 2020). Building on these findings, we are currently conducting a project focused on characterizing CXCR4 clustering specifically within this specialized cellular region.

• In LVP experiments, it would be useful to report transduction efficiency (% GFP+ cells) alongside MSI data to relate VLP infectivity with receptor clustering functionally.*

These experiments were designed to validate the functional integrity of the gp120 conformation on the LVPs, confirming their suitability for subsequent TIRF microscopy. Our objective was to establish a robust experimental tool rather than to perform a high-throughput quantification of transduction efficiency. It is for that reason that these experiments were included in new Supplementary Figure S6, which also contains the complete characterization of gp120-VLPs and LVPs. In such experimental conditions, quantifying the percentage of GFP-positive cells relative to the total number of cells plated in each well is very difficult. However, in line with the reviewer's commentary and as we used the same number of cells in each experimental condition, we have included, in the revised manuscript, a complementary graph illustrating the GFP intensity (arbitrary units) detected in all the wells analyzed (new Supplementary Fig. 6E).

• To ensure that differences in fusion events (Figure 7B) are attributable to target cell receptor properties, consider confirming that effector cells express similar levels of HIV-1 Env. Quantifying gp120 expression by flow cytometry or western blot would rule out the confounding effects of variable Env surface density.*

In these assays (Figure 7B), we used the same effector cells (cells expressing X4-gp120) in both experimental conditions, ensuring that any observed differences should be attributable solely to the target cells, either JKCD4X4 or JKCD4X4R334X. For this reason, in Figure 7A we included only the binding of X4-gp120 to the target cells which demonstrated similar levels of the receptors expressed by the cells.

• HIV-mediated receptor downregulation may occur more slowly than ligand-induced internalization. Including a 24-hour time point would help assess whether gp120 induces delayed CD4 or CXCR4 loss beyond the early effects shown and to better capture potential delayed downregulation induced by gp120.*

The reviewer suggests using a 24-hour time point to facilitate detection of receptor internalization. However, such an extended incubation time may introduce some confounding factors, including receptor degradation, recycling and even de novo synthesis, which could affect the interpretation of the results. Under our experimental conditions, we observed that CXCL12 did not trigger CD4 internalization whereas X4-gp120 did. Interestingly, CD4 internalization depended on the co-receptor expressed by the cells.

• Increase label font size in microscopy panels for improved readability.*

Of course; the font size of these panels has been increased in the revised version.

• Consider adding more references on ligand-induced co-endocytosis of CD4 and chemokine receptors during HIV-1 entry.*

We have added more references to support this hypothesis (Toyoda et al. J. Virol., 2015; Venzke et al. J. Virol., 2006; Gobeil et al J. Virol., 2013).

• For Statistical analysis. Biological replicates are adequate, and statistical tests are generally appropriate. For transparency, report n values, exact p-values, and the statistical test used in every figure legend and discussed in the results.*

Thank you for highlighting the importance of transparency in statistical reporting. We confirm that the n values for all experiments have been included in the figure legends. The statistical tests used for each analysis are also clearly indicated in the figure legends, and the interpretation of these results is discussed in detail in the Results section. Furthermore, the Methods section specifies the tests applied and the thresholds for significance, ensuring full transparency regarding our analytical approach.

In accordance with established conventions in the field, we have utilized categorical significance indicators (e.g., n.s., *, **, ***) within our figures to enhance readability and focus on biological trends. This approach is widely adopted in high-impact literature to prevent visual clutter. However, to ensure full transparency and reproducibility, we have ensured that the underlying statistical tests and thresholds are clearly defined in the respective figure legends and Methods section.

Reviewer #4

We thank the reviewer for considering that this work is presented in a clear fashion, and the main findings are properly highlighted, and for remarking that the paper is of interest to the retrovirology community and possibly to the broader virology community.

We also agree on the interest that X4-gp120 clusters CXCR4R334X suggests a different binding mechanism for X4-gp120 from that of the natural ligand CXCL12, an aspect that we are now evaluating. These data also indicate that WHIM patients can be infected by HIV-1 similarly to healthy people.

• The observation that "empty VLPs" reduce CXCR4 diffusivity is potentially interesting. However, it is not supported by the data owing to insufficient controls. The authors correctly discuss the limitations of that observation in the Discussion section (lines 702-704). However, they overinterpret the observation in the Results section (lines 509-512), suggesting non-specific interactions between empty VLPs, CD4 and CXCR4. I suggest either removing the sentence from the Results section or replacing it with a sentence similar to the one in the Discussion section.*

In accordance with the reviewer`s suggestion, the sentence in the result section has been replaced with one similar to that found in the discussion section. In addition, we have performed Raster Image Correlation Spectroscopy (RICS) analysis using the Di-4-ANEPPDHQ lipid probe to assess membrane fluidity by means of membrane diffusion, and compared the results with those of cells treated with Env(-) VLPs. The results indicated that VLPs did not modulate membrane fluidity (Figure VIII in this reply). Nonetheless, these results do not rule out other potential non-specific interactions of the Env(-) VLPs with other components of the cell membrane that might affect receptor dynamics (see our response to point 2 of reviewer #3 p. 14-15 of this reply).

• In the case of the WHIM mutant CXCR4-R334X, the addition of "empty VLPs" did not cause a significant change in the diffusivity of CXCR4-R334X (Figure 4B). This result is in contrast with the addition of empty VLPs to WT CXCR4. However, the authors neither mention nor comment on that result in the results section. Please mention the result in the paper and comment on it in relation to the addition of empty VLPs to WT CXCR4.*

We would remark that the main observation in these experiments should focus on the effect of gp120-VLPs, and the results indicates that gp120-VLPs promoted clustering of CXCR4 and of CXCR4R334X and reduced their diffusion at the cell membrane. The Env(- ) VLPs were included as a negative control in the experiments, to compare the data with those obtained using gp120-VLPs. However, once we observed some residual effect of the Env(-) VLPs, we decided to give a potential explanation, formulated as a hypothesis, that the Env(-) VLPs modulated membrane fluidity. We have now performed a RICS analysis using Di-4-ANEPPDHQ as a lipid probe (Figure IX only for review purposes). The results suggest that Env(-) VLPs do not modulate cell membrane fluidity, although we do not rule out other potential interactions with membrane proteins that might alter receptor dynamics. We appreciate the reviewer's observation and agree that this result can be noted. However, since the main purpose of Figure 4B is to show that gp120-VLPs modulate the dynamics of CXCR4R334X rather than to remark that the Env(-) VLPs also have some effects, we consider that a detailed discussion of this specific aspect would detract from the central finding and may dilute the primary narrative of the study.

Minor comments

• It would be helpful for the reader to combine thematically or experimentally linked figures, e.g., Figures 3 and 4.*

• Figures 3 and 4 are very similar. Please unify the colours in them and the order of the panels (e.g. Figure 3 panel A shows diffusivity of CXCR4, while Figure 4 panel A shows MSI of CXCR4-R334X).*

While we considered consolidating Figures 3 and 4, we believe that maintaining them as separate entities enhances conceptual clarity. Since Figure 3 establishes the baseline dynamics for wild-type CXCR4 and Figure 4 details the distinct behavior of the CXCR4R334X mutant, keeping them separate allows the reader to fully appreciate the specificities of each system before making a cross-comparison.

• Some parts of the Discussion section could be shortened, moved to the Introduction (e.g.,lines 648-651), or entirely removed (e.g.,lines 633-635 about GPCRs).*

In accordance, the Discussion section has been reorganized and shortened to improve clarity.

• I suggest renaming "empty VLPs" to "Env(−) VLPs" (or similar). The name empty VLPs can mislead the reader into thinking that these are empty vesicles.*

The term empty VLPs has been renamed to Env(−) VLPs throughout the manuscript to more accurately reflect their composition. Many thanks for this suggestion.

• Line 492 - please rephrase "...lower expression of Env..." to "...lower expression of Env or its incorporation into the VLPs...".*

The sentence has been rephrased

• Line 527 - The data on CXCL12 modulating CXCR4-R334X dynamics and clustering are not present in Figure 4 (or any other Figure). Please add them or rephrase the sentence with an appropriate reference. Make clear which results are yours.*

• Line 532 - Do the data in the paper really support a model in which CXCL12 binds to CXCR4-R334X? If not, please rephrase with an appropriate reference.*

Previous studies support the association of CXCL12 with CXCR4R334X (Balabanian et al. Blood, 2005; Hernandez et al. Nat Genet., 2003; Busillo & Benovic Biochim. Biophys. Acta, 2007). In fact, this receptor has been characterized as a gain-of-function variant for this ligand (McDermott et al. J. Cell. Mol. Med., 2011). The revised manuscript now includes these bibliographic references to support this commentary. In any case, our previous data indicate that CXCL12 binding does not affect CXCR4R334X dynamics (García-Cuesta et al. PNAS, 2022).

• Line 695 - "...lipid rafts during HIV-1 (missing word?) and their ability to..." During what?*

Many thanks for catching this mistake. The sentence now reads: "Although direct evidence for the internalization of CD4 and CXCR4 as complexes is lacking, their co-localization in lipid rafts during HIV-1 infection (97-99) and their ability to form heterocomplexes (22) strongly suggest they could be endocytosed together."

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Referee #4

Evidence, reproducibility and clarity

This paper provides new insights into the organisational changes of the X4-tropic HIV-1 co-receptor CXCR4 upon binding of the viral receptor-binding protein X4-gp120, either in its soluble form or when displayed on virus-like particles (VLPs) as Env. The study employs single-particle tracking total internal reflection fluorescence (SPT-TIRF) microscopy to quantify the dynamics and clustering of CXCR4 on CD4+ T cells. The data show that CXCR4 clusters in the presence of X4-gp120 and VLPs, a phenomenon also observed for the primary HIV-1 receptor CD4. The authors also show that a WHIM mutant of CXCR4 (CXCR4-R334X) that does not cluster in the presence of its natural ligand, CXCL12, clusters in the presence of X4-gp120 and VLPs.

The following points should be clarified or improved prior to publication:

Major comments:

1. The observation that "empty VLPs" reduce CXCR4 diffusivity is potentially interesting. However, it is not supported by the data owing to insufficient controls. The authors correctly discuss the limitations of that observation in the Discussion section (lines 702-704). However, they overinterpret the observation in the Results section (lines 509-512), suggesting non-specific interactions between empty VLPs, CD4 and CXCR4. I suggest either removing the sentence from the Results section or replacing it with a sentence similar to the one in the Discussion section.
2. In the case of the WHIM mutant CXCR4-R334X, the addition of "empty VLPs" did not cause a significant change in the diffusivity of CXCR4-R334X (Figure 4B). This result is in contrast with the addition of empty VLPs to WT CXCR4. However, the authors neither mention nor comment on that result in the results section. Please mention the result in the paper and comment on it in relation to the addition of empty VLPs to WT CXCR4.

Minor comments:

1. It would be helpful for the reader to combine thematically or experimentally linked figures, e.g., Figures 3 and 4.
2. Figures 3 and 4 are very similar. Please unify the colours in them and the order of the panels (e.g. Figure 3 panel A shows diffusivity of CXCR4, while Figure 4 panel A shows MSI of CXCR4-R334X).
3. Some parts of the Discussion section could be shortened, moved to the Introduction (e.g., lines 648-651), or entirely removed (e.g., lines 633-635 about GPCRs).
4. I suggest renaming "empty VLPs" to "Env(−) VLPs" (or similar). The name empty VLPs can mislead the reader into thinking that these are empty vesicles.
5. Line 492 - please rephrase "...lower expression of Env..." to "...lower expression of Env or its incorporation into the VLPs...".
6. Line 527 - The data on CXCL12 modulating CXCR4-R334X dynamics and clustering are not present in Figure 4 (or any other Figure). Please add them or rephrase the sentence with an appropriate reference. Make clear which results are yours.
7. Line 532 - Do the data in the paper really support a model in which CXCL12 binds to CXCR4-R334X? If not, please rephrase with an appropriate reference.
8. Line 695 - "...lipid rafts during HIV-1 (missing word?) and their ability to..." During what?

Significance

In summary, the work is presented in a clear fashion, and the main findings are properly highlighted. The paper is of interest to the retrovirology community and possibly to the broader virology community. The findings are not entirely surprising because it has been shown previously that the binding of Env to CD4 mediates CD4 clustering, which would also suggest clustering of the co-receptor. Nonetheless, the paper provides strong evidence that CXCR4 clusters and changes its dynamics in the presence of CD4 and X4-gp120. Moreover, the evidence that X4-gp120 clusters CXCR4-R334X is of high interest because it suggests a different binding mechanism for X4-gp120 from that of the natural ligand CXCL12, raising questions for further research. The diffusivity data with empty VLPs require additional controls to strengthen the evidence. My expertise is in virology and structural biology. I did not comment on the technical aspects of the light-microscopy experiments in the study because these are beyond my expertise.

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Referee #3

Evidence, reproducibility and clarity

The author investigates how the HIV-1 Env glycoprotein modulates the nanoscale organisation and dynamics of the CXCR4 co-receptor on CD4⁺ T cells. The author demonstrates that HIV-1 Env induces CXCR4 clustering distinct from that triggered by its natural ligand (CXCL12), implicating spatial receptor organization as a determinant of infection. This study investigates how HIV-1 Env (specifically X4-tropic gp120) alters the membrane organization and dynamics of the chemokine receptor CXCR4 and its WHIM-associated mutant, CXCR4R334X, in a CD4-dependent manner. Using single-particle tracking total internal reflection fluorescence microscopy (SPT-TIRF-M), the authors demonstrate that both soluble gp120 and virus-like particles (VLPs) displaying gp120 induce CXCR4 nanoclustering, reduce receptor diffusivity, and promote immobile nanoclusters of CXCR4 at the membrane of Jurkat T cells and primary CD4⁺ T cell blasts.The work offers new insights into the spatial organisation of receptors during HIV-1 entry and infection. The manuscript is well-written, and the findings are significant.

Major Comments: 1. For mechanistic basis of gp120-CXCR4 versus CXCL12-CXCR4 differences

Provide additional structural or biochemical evidence to support the claim that gp120 stabilises a distinct CXCR4 conformation compared to CXCL12.

If feasible, include molecular modelling, mutagenesis, or cross-linking experiments to corroborate the proposed conformational differences. 2. For Empty VLP effects on CXCR4 dynamics

Explore potential causes for the observed effects of Env-deficient VLPs. It's valuable to include additional controls such as particles from non-producer cells, lipid composition analysis, or blocking experiments to assess nonspecific interactions. 3. For Direct link between clustering and infection efficiency - Test whether disruption of CXCR4 clustering (e.g., using actin cytoskeleton inhibitors, membrane lipid perturbants, or clustering-deficient mutants) alters HIV-1 fusion or infection efficiency. 4. CD4/CXCR4 co-endocytosis hypothesis - Support the proposed model with direct evidence from live-cell imaging or co-localization experiments during viral entry. Clarification is needed on whether internalization is simultaneous or sequential for CD4 and CXCR4.

Minor Comments: 1. The conclusions rely solely on the HXB2 X4-tropic Env. It would strengthen the study to assess whether other X4 or dual-tropic strains induce similar receptor clustering and dynamics. 2. Given the observed clustering effects, it would be valuable to explore whether gp120-induced rearrangements alter epitope exposure to broadly neutralizing antibodies like 17b or 3BNC117. This would help connect the mechanistic insights to therapeutic relevance. 3 . TIRF imaging limits analysis to the cell substrate interface. It would be useful to clarify whether CXCR4 receptor clustering occurs elsewhere, such as at immunological synapses or during cell-to-cell contact. 4. In LVP experiments, it would be useful to report transduction efficiency (% GFP+ cells) alongside MSI data to relate VLP infectivity with receptor clustering functionally. 5. To ensure that differences in fusion events (Figure 7B) are attributable to target cell receptor properties, consider confirming that effector cells express similar levels of HIV-1 Env. Quantifying gp120 expression by flow cytometry or western blot would rule out the confounding effects of variable Env surface density 6. HIV-mediated receptor downregulation may occur more slowly than ligand-induced internalization. Including a 24-hour time point would help assess whether gp120 induces delayed CD4 or CXCR4 loss beyond the early effects shown and to better capture potential delayed downregulation induced by gp120. 7. Increase label font size in microscopy panels for improved readability. 8. Consider adding more references on ligand-induced co-endocytosis of CD4 and chemokine receptors during HIV-1 entry. For Statistical analysis. Biological replicates are adequate, and statistical tests are generally appropriate. For transparency, report n values, exact p-values, and the statistical test used in every figure legend and discussed in the results.

Referee cross-commenting

Overall, the manuscript provides compelling mechanistic insight into HIV-1 entry by demonstrating Env-induced CXCR4 clustering, including in WHIM mutant receptors. While the core findings are well supported and of high interest, clarifications regarding Env trimer densities, receptor internalization, and the contribution of empty VLPs would further strengthen the work.

Significance

Nature and significance of the advance

This work marks a conceptual and mechanistic breakthrough in understanding HIV-1 entry. It goes beyond the static view of Env-co-receptor interaction to show that nanoscale reorganization of CXCR4, distinct from chemokine-induced clustering, occurs during HIV-1 Env engagement and may be essential for infection Context within existing literature. Previous studies established Env-induced CD4 clustering (Yin et al., 2020) and chemokine-induced CXCR4 nanocluster formation (Martínez-Muñoz et al., 2018), but the exact nanoscale rearrangement of CXCR4 in the context of HIV-1 Env and physiological Env densities remains unquantified. This study addresses this gap using SPT-TIRF, STED microscopy, and functional assays.

Audience and influence

The findings will be of interest to researchers in HIV virology, membrane receptor biology, viral entry mechanisms, and therapeutic target development. The receptor-clustering aspect could also influence broader fields of study, such as GPCR organization and immune receptor signalling.

Reviewer expertise

I can evaluate HIV-1 entry mechanisms, viral glycoprotein-host-host-host receptor interactions, single-molecule fluorescence microscopy, and membrane protein dynamics. I am less equipped to evaluate the deep structural modelling aspects, though the in silico AlphaFold results are straightforward to interpret in context.

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Referee #2

Evidence, reproducibility and clarity

The authors examine the distribution of CXCR4 on the cell surface following exposure to gp120 and HIV virus-like particles (VLPs) using single particle tracking total internal reflection fluorescence (SPT-TIRF) microscopy. They show that gp120 and VLPs promote clustering of wild-type CXCR4 and CXCR4.R334X from a person with WHIM syndrome. The HIV Env-induced clustering involves heterodimeric interactions between CXCR4 and CD4 and spatial distribution and dynamics are distinct from that induced by CXCR4's natural ligand, CXCL12. The authors suggest the CD4-CXCR4 interaction may be targeted to specifically block HIV infection.

Major comments

This study is well described in both the main text and figures. Introduction provides adequate background and cites the literature appropriately. Materials and Methods are detailed. Authors are careful in their interpretations, statistical comparisons, and include necessary controls in each experiment. The Discussion presents a reasonable interpretation of the results. Overall, there are no major weaknesses with this manuscript.

Minor comments

Ln 477-497. NL4-3deltaIN and immature HIV virions are found to have less associated gp120 relative to wild-type particles. It is not obvious why this is the case for the deltaIN particles or genetically immature particles. Can the authors provide possible explanations? (A prior paper was cited, Chojnacki et al Science, 2012 but can the current authors provide their own interpretation.)

Significance

The current study builds on prior works that examined CXCR4 distribution, HIV pseudotyped infection in CXCR4.R334X cells, but goes beyond these studies in resolution and depth of analysis of CXCR4/CD4 nanoclustering, AF3 modeling of CXCR4/CD4 heterodimer, as well as demonstration of replication of HIV in CXCR4.R334X cells.

Audience:

Scientists interested in HIV-1, cell biologists and virologists interested in receptor nanoclustering

Reviewer expertise:

HIV-1 Envelope glycoproteins and entry assays, HIV broadly neutralizing antibodies, HIV vaccine design

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Referee #1

Evidence, reproducibility and clarity

The authors investigate the impact of surface bound HIV gp120 and VLPs on CXCR4 dynamics in Jurkat T cells expressing WT or WHIM syndrome mutated CXCR4, which has a defective response to CXCL12. Jurkat cells were transfected with CXCR4-AcGFP. Images were acquired and a single particle tracking routine was applied to generate information about nanoclustering and diffusion, and FRET was used to investigate CD4-CXCR4 proximity. They compare effects of soluble gp120 to immature and mature VLPs, which include varying degrees of gp120 clustering. They find that solid phase gp120 or VLP can increase CXCR4 clustering size and decrease diffusion in Jurkat cells. Surprisingly, VLP lacking gp120 could increase CXCR4 clustering and speed, which is paradoxical as there were no known ligands on the VLPs, but they likely carry many cellular proteins with potential interactions. The impact of CXCL12 and gp120 binding to CXCR4 was different in terms of clustering and receptor down-regulation.

While a single particle tracking routine was applied to the data, it's not clear how the signal from a single GFP was defined and if movement during the 100 ms acquisition time impacts this. My concern would be that the routine is tracking fluctuations, and these are related to single particle dynamics, it appears from the movies that the density or the GFP tagged receptors in the cells is too high to allow clear tracking of single molecules. SPT with GFP is very difficult due to bleaching and relatively low quantum yield. Current efforts in this direction that are more successful include using SNAP tags with very photostable organic fluorophores. The data likely does mean something is happening with the receptor, but they need to be more conservative about the interpretation.

Some of the paradoxical effects might be better understood through deeper analysis of the SPT data, particularly investigation of active transport and more detailed analysis of "immobile" objects. Comments on early figures illustrate how this could be approached. This would require selecting acquisitions where the GFP density is low enough for SPT and performing a more detailed analysis, but this may be difficult to do with GFP.

When the authors discuss clusters of <2 or >3, how do they calibrate the value of GFP and the impact of diffusion on the measurement. One way to approach this might be single molecules measurements of dilute samples on glass vs in a supported lipid bilayer to map the streams of true immobility to diffusion at >1 µm2/sec.

I understand that the CXCL12 or gp120 are attached to the substrate with fibronectin for adhesion. I'm less clear how how that VLPs are integrated. Were these added to cells already attached to FN? Fig 1A- The classification of particle tracks into mobile and immobile is overly simplistic description that goes back to bulk FRAP measurements and it not really applicable to single molecule tracking data, where it's rare to see anything that is immobile and alive. An alternative classification strategy uses sub-diffusion, normal diffusion and active diffusion (or active transport) to descriptions and particles can transition between these classes over the tracking period. Fig 1B- this data might be better displayed as histograms showing distributions within the different movement classes. Fig 1C,D- It would be helpful to see a plot of D vs MSI at a single particle level. In comparing C and D I'm surprised there is not a larger difference between CXCL12 and X4-gp120. It would also be very important to see the behaviour of X4-gp120 on the CXCR4 deficient Jurkat that would provide a picture of CD4 diffusion. The CXCR4 nanoclustering related to the X4-gp120 could be dominated by CD4 behaviour.

Fig S1D- This data is really interesting. However, if both the CD4 and the gp120 have his tags they need to be careful as poly-His tags can bind weakly to cells and increasing valency could generate some background. So, they should make the control is fair here. Ideally, using non-his tagged person of sCD4 and gp120 would be needed ideal or they need a His-tagged Fab binding to gp120 that doesn't induce CXCR4 binding.

Fig S4- Panel D needs a scale bar. I can't figure out what I'm being shown without this.

Significance

The strengths are that its an important question and the reagents are well prepared and characterised. They are detecting quantitative effects that will likely be reproducible. The information generated is potentially useful for those studying HIV infection processes and strategies to prevent infection.

The major weakness is that the conditions for the SPT experiments are not ideal in that the density of particles is too high for SPT and the single molecule basis for assessing nanoclusters is not clear. This means that the data is getting at complex molecules phenomena and less likely be generating pure single molecules measurements.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC-2025-03206

Corresponding author(s____): Teresa M. Przytycka

General Statements

We thank all the reviewers for their time and their constructive criticism, based on which we have revised our manuscript. All review comments in are italics. Our responses are indicated in normal font except the excerpts from manuscript which are shown within double quote and in italics. The line numbers indicated here refer to those in the revised manuscript.

Point-by-point description of the revisions

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

This paper addresses the interesting question of how cell size may scale with organ size in different tissues. The approach is to mine data from the fly single cell atlas (FCA) which despite its name is a database of gene expression levels in single isolated nuclei. Using this data, they infer cell size based on ribosomal protein gene expression, and based on this approach infer that there are tissue and sex specific differences in scaling, some of which may be driven by differences in ribosomal protein gene expression.

Response: Indeed, using the FCA dataset, we infer sex-specific differences in both cell size and cell number, which we validated with targeted experiments. We show that Drosophila cell types scale through distinct strategies-via cell size, cell number, or a mix of both-in an allometric rather than uniform fashion. We further propose that these scaling differences are driven, at least in part, by variation in translational activity, reflected in the expression of ribosomal proteins, translation elongation factors, and Myc.

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I think the idea of mining this database is a clever one, however there a number of concerns about whether the existing data can really be used to draw the conclusions that are stated.

__Response: __We are pleased to see that the reviewer found the question and our approach interesting.

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*One concern has to do with the assumption that RP (ribosome protein) expression is a proxy for cell size. It is well established that ribosome abundance scales with cell size, but is there reason to believe that ribosome nuclear gene EXPRESSION correlates with ribosome abundance? *

I'm not saying that this can't be true, but it seems like a big assumption that needs to be justified with some data. Maybe this is well known in the Drosophila literature, but in that case the relevant literature really needs to be cited.

__Response: __To avoid any misunderstanding: we use sex-biased RP expression as an indicator of sex differences in cell size only within the same cell type or subtype, as defined by expression-based clustering in the FCA-not as a general estimator of cell size. This measure is applied strictly within the same clusters, never between different ones. To prevent overinterpretation, we replaced the term 'proxy' with 'indicator,' since the earlier wording might have implied that ribosomal gene expression was being used to estimate cell size more broadly.

We should have begun by providing more background on the well-established link between ribosomal protein gene dosage and cell growth. This context was missing from the introduction, so we have now added a full paragraph outlining what is known about this connection:

*Added at line 85: *

"Cell growth, which supports both cell enlargement and cell division, demands elevated protein synthesis, accomplished by boosting translation rates. Indeed, ribosome abundance is known to scale with cell size in many organisms (Schmoller and Skotheim 2015; Cadart and Heald 2022; Serbanescu et al. 2022). Long before it was known that DNA was the carrier of genetic information, Drosophila researchers had identified a large class of mutations known as "Minutes" (Schultz 1929). These were universally haplo-insufficient. A single wild type copy resulted in a tiny slowly growing fly, and the homozygous loss-of-function alleles were lethal. In clones, the Minute cells are clearly smaller and compete poorly with surrounding wild type cells. We now know that most of the Minute loci encode ribosomal proteins (Marygold et al. 2007). Similarly, the Drosophila diminutive locus, also characterized by small flies almost a century ago, is now known to encode the Myc oncogene (Gallant 2013). This is significant as Myc is a regulator of ribosomal protein encoding genes in metazoans, including Drosophila (Grewal et al. 2005). The ribosome is assembled in a specialized nuclear structure called the nucleolus (Ponti 2025). Across species, including Drosophila (Diegmiller et al. 2021) and C. elegans (Ma et al. 2018), nucleolar size scales with cell size and is broadly correlated with growth in cell size and/or cell number, processes that are directly relevant to sex-specific allometry. Collectively, these and many other studies offer compelling evidence that ribosomal biogenesis is positively associated with cell size and growth, underscoring the value of measuring ribosome biogenesis as a metric."

We understand that the reviewer is asking whether reduced RP mRNA expression directly leads to reduced functional ribosome assembly. We do not have a definitive answer to that specific question. However, we directly measured translation in fat body cells (section: Female bias in ribosomal gene expression in fat body cells leads to sex-biased protein synthesis), and the results show a clear correlation between RP gene expression and biosynthetic activity; even though we did not track every step from transcription to ribosome assembly to polysome loading across all cell types. This would indeed be an excellent direction for future work, including polysome profiling and related assays. Importantly, we did examine the nucleolus (Figure 4), where ribosome assembly occurs, and showed that nucleolar volume scales with RP gene expression. This strongly supports the presence of sex-specific differences in ribosome biogenesis.

Added at line 115:

"Building on the earlier studies noted above, as well as our direct measurements of translation bias in the fat body, nucleolar size, and cell size, we used sex-biased expression of ribosomal proteins as an indicator of sex differences in per-nucleus cell size."

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Second, the interpretation of RP expression as a proxy for cell size seems potentially at odds with the fact that some cells are multi-nucleate. Those cells are big because of multiple nuclei, and so they might not show any increase in ribosome expression per nucleus. presumably for multi-nucleate cells, RP expression if it reflects anything at all would be something to do with cell size PER nucleus.

Response: Yes, this is a very important point, and this is why we chose multinucleated indirect flight muscles for our direct experimental analysis. We show that in indirect flight muscle cells, adult cell size is greatly influenced by the sex-specific number of nuclei per cell. The female muscle cells are larger and have larger nuclei count per cell. Additionally, they also have higher expression of ribosomal protein coding genes. As the latter data are from the single nucleus sequencing atlas, this already demonstrates what this reviewer is asking for: per nucleus, female muscle cells express more ribosome protein coding mRNAs.

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*Third, it is well known that many tissues in Drosophila are polyploid or polytene. I don't know enough about the methodology used to produce the FCA to know whether this is somehow normalized. Otherwise, my hypothesis would be that nuclei showing higher RP expression might just be polyploid or polytene. You might say that this could be controlled by asking if all genes are similary upregulated, but that isn't the case since at least in polytene chromosomes it is well known that only a small number of genes are expressed at a given time, while many are silent. *

Response: Yes, this is an excellent point. As noted above, our study does not distinguish among the different potential causes of sex differences in ribosomal mRNA copy number, as these may vary across cell types. We now explicitly acknowledge it in the discussion (line 327). Importantly, even in the cases when ribosomal gene expression bias primarily reflects differences in DNA content, this still represents a plausible mechanistic route linking ribosomal gene expression to increased nucleolar ribosome biogenesis and, ultimately, larger cell size. This possibility does not alter our main conclusions.

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Overall, I think a lot more foundational work would need to be done in order to allow the inference of cell size from RP expression. In a way, it is a bit unfortunate that they chose to do this work in Drosophila where so many cells are polyploid, although I gather that even in humans some tissues have this issue, for example large neurons in the brain.

Response: We acknowledge that we did not clearly reference some of the foundational work in the literature. To address this, we have expanded the introduction to provide additional background and context. We also clarify that our fat body experiment offers independent support for the relationship between ribosomal gene expression bias, nuclear size bias, and corresponding biases in protein synthesis, thereby reinforcing the use of sex-specific ribosomal gene expression as an indicator of sex-specific cell size. Importantly, we assess this bias only within clusters, not between them. These clusters are derived from gene-expression-based clustering and are therefore relatively homogeneous. For example, as discussed in our response to Reviewer #3, the fat body contains several clusters that correspond to expression-defined subtypes of fat body cells. Our previous terminology may have inadvertently implied that we were using ribosomal gene expression to estimate cell size more broadly, which was not our intention.

As for the choice of the organism, most of the authors are Drosophila researchers and we benefit from the unique, highly replicated data from whole head and whole body of both sexes. Such data is necessary for a non-biased estimation of the differences in nuclear number.

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*Reviewer #1 (Significance (Required)):

The idea that gene regulatory networks could "program" differences in scaling by changing levels of ribosomal protein gene expression is a tremendously important one if it can be established, because it would show a simple way for size scaling to be placed under control of developmental regulatory pathways. My original concern when I first looked at the abstract was going to be that yeah the results are interesting but a mechanism is not provided, but as I read it, that concern went away. showing that RP gene expression, which could be programmed by various driving pathways, can affect allometric scaling, would be extremely impactful and really change how we think about scaling, but putting it into the framework of gene expression networks that control other aspects of developmewnht. it would not be necessary to show which pathways actually drive these expression differences, the fact that they are different would be interesting enough to make everyone want to read this paper. But as discussed above I am not, however, convinced by the evidence presented here. So while I think it would be very significant if true, I am not convinced that the conclusion is well supported. This doesn't mean I have a reason to think it is false, just that its not well supported for the reasons I have given.*

Response: We are grateful to the reviewer for this positive assessment of our findings despite lack of a specific mechanism. We also regret that our initial writing did not clearly situate our work within the foundational literature on the relationship between ribosomal biogenesis and scaling. The key contribution of our study is to demonstrate that sex-biased ribosomal biogenesis plays a role in allometric scaling, providing a basis for future mechanistic exploration. We hope that the revised manuscript now offers clear and compelling support for the conclusion that RP gene expression bias can influence allometric scaling.

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I hasten to point out that I could be entirely wrong, if the missing bits of logic (i.e. that RP expression matches ribosome abundance and that gene expression in the FCA dataset isn't influenced by ploidy of the nucleus). If suitable references can be provided to support these underlying assumptions, then in fact I think these concerns could be answered with very little effort. Otherwise, I think experiments would be needed to support these assumptions, and that might be non-trivial to do in a reasonable time frame. for that reason, in the next question I have put "cannot tell" for the time estimate.

Response: While gene expression in some FCA cell types may indeed be influenced by ploidy, our analysis does not depend on distinguishing among the possible sources of gene expression bias, which may vary across cell types. Rather, our key point is that-regardless of its origin-an increase in ribosomal gene expression is associated with enhanced ribosome biogenesis in the nucleolus and, ultimately, larger cell size. Thus, our main conclusions do not rely on any specific mechanism underlying RP gene expression upregulation. We now include additional references supporting the relationship between RP expression bias and cell size bias. We also strengthen the link between ribosomal gene expression and biosynthetic activity by clarifying its relationship with sex-biased Myc expression and the strong correlation with expression bias of EF1. We now include additional references supporting the relationship between RP expression bias and cell size bias. We also strengthen the link between ribosomal gene expression and biosynthetic activity by clarifying its relationship with sex-biased Myc expression and the strong correlation with expression bias of EF1.

We thank the reviewer for their thoughtful and constructive comments, which have prompted us to clarify both our reasoning and the relevant literature more fully.

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

The authors analyzed the FlyAtlas single-nucleus dataset to identify sex differences in gene expression and cell numbers. This led them to focus on muscles, cardiomyocytes, and fat body cells. They then measured cell and nucleolus size across different tissues and showed that reducing Myc function decreases sex differences in fat body cells. Overall, the manuscript provides a characterization of dimorphic differences in cell and organ size across three tissues.*

Response: This is a nice synopsis of the work.

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Major Comments: The major claims of the manuscript are well supported by the reported experiments and analyses. While Reviewer #2 considered the major claims of the manuscript to be well supported, by the reported experiments and analysesStatistical analyses appear adequate.

Response: We agree, and we are glad that the reviewer found our work well supported.

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*Minor Comments: The following minor issues should be addressed through textual edits:In the Introduction:

"Disruptions in proportionality, whether due to undergrowth or overgrowth, can lead to reduced fitness or diseases such as cancer." Could the authors provide a reference for this statement, particularly for the claim that disruptions in proportion*

Response: We apologize for this omission. The following explanation is now included starting at line 39:

"For example, scaled cell growth is a driver of symmetry in Myc-dependent scaling of bone growth in the skeleton by chondrocyte proliferation (Ota et al. 2007; Zhou et al. 2011). Increased nucleolus size is a well known marker of cancer progression in a histopathological setting (Pianese 1896; Derenzini et al. 1998; Elhamamsy et al. 2022)."

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*The authors state:

"This study offers a comprehensive, cellular-resolution analysis of sexual size dimorphism in a model organism, uncovering how differences in cell number and size contribute to sex-specific body plans."*

The study cannot be considered comprehensive, as not all organs were examined.

Response: Indeed, "comprehensive" is a loaded word and in the revised manuscript we just omitted it.

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*The following sentence from the abstract is unclear:

"By uncovering how a conserved developmental system produces sex-specific proportions through distinct cellular strategies..."*

* What do the authors mean by a conserved developmental system? Do they refer to a commonly used developmental model, or to a developmental system that is evolutionarily conserved?*

Response: We acknowledge that the use of the word 'conserved' was inappropriate, and we have therefore removed it from the statement.

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*Reviewer #2 (Significance (Required)):

The manuscript presents a relevant exploration of sex-specific differences in cell size and cell number in Drosophila males and females. The limitations of the study are clearly acknowledged in the "Limitations" section. The work does not provide mechanistic insight into the causes or functional consequences of the observed differences. Nonetheless, the study extends our understanding of sexual dimorphism and establishes a foundation for future investigations into the autonomous and systemic mechanistic factors that regulate these differences.*

Response: Thank you.

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

The manuscript by Pal and colleagues addresses an important question: the cellular mechanisms underlying sex differences in organ size. By leveraging single-nucleus transcriptomic data from the adult Drosophila Cell Atlas, the authors show that different cell types adopt distinct strategies to achieve sex differences in organ size-either by increasing cell size or by altering cell number. They then focus on three organs-the indirect flight muscles, the heart, and the fat body-and provide supporting evidence for their transcriptomic analyses.*

Response: This is a nice summary of the study. Thank you.

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This study tackles a highly relevant and often overlooked question, as our understanding of the molecular and cellular events driving sex differences remains incomplete. The work presents interesting observations; however, it is largely descriptive, establishing correlations without providing functional evidence or mechanistic insight.

Response: We agree that this is an often overlooked problem that has been difficult to address experimentally without single-cell genomics. Our work aims to help fill this gap. While the paper does contain descriptive elements, we believe such characterization is important at the early stages of developing a new area of inquiry. The study explores a unique dataset and includes experimental validation to support key observations. We also propose how allometry may be shaped by cell division and cell size, drawing on well-established molecular mechanisms. Thus, the reviewer's comment regarding a lack of mechanistic insight likely pertains to the absence of a direct connection to the sex-determination pathway, which is beyond the scope of the current study.

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Below are four main points that should be addressed before publication: 1. Introduction and contextualisation of prior work The introduction does not adequately present the current state of knowledge. Several key studies are missing or insufficiently discussed. In particular, the following works should be included and integrated into the introduction: - PMID: 26710087 - shows that the sex determination gene transformer regulates male-female differences in Drosophila body size. - PMID: 28064166 - describes how differences in Myc gene dosage contribute to sex differences in body size. - PMID: 26887495 - demonstrates that the intrinsic sexual identity of adult stem cells can control sex-biased organ size through sex-biased proliferation. - PMID: 28976974 - reveals that Sxl modulates body growth through both tissue-autonomous and non-autonomous mechanisms. - PMID: 39138201 - shows that transformer drives sex differences in organ size and body weight. Incorporating and discussing these references would provide a more comprehensive and up-to-date framework for the study.

Response: We agree that the literature suggested by the reviewer strengthens the introduction and improves the contextualization of prior work relevant to our study. Although much of it was previously included in the discussion section on cell-autonomous and hormonal regulation, it has now been moved to the introduction, along with the discussion of the papers suggested by the reviewer (beginning at line 58).

"In Drosophila melanogaster, adult females are substantially larger than males (Fig. 1A1), yet both sexes develop from genetically similar zygotes and share most organs and cell types. In wild type flies, sex is determined by the number of X chromosomes in embryos, with XX flies developing as females and X(Y) flies developing as males due to the activation and stable expression of Sex-lethal only in XX flies (Erickson and Quintero 2007). While it is not entirely clear how sexually dimorphic size is regulated, the sex determination pathway is implicated in size regulation. Sex-reversed flies often show a size based on the X chromosome number rather than sexual morphology. Female Sex-lethal contributes to larger female size independently of sexual identity (Cline 1984), and Sex-lethal expression in insulin producing neurons in the brain also impacts body size (Sawala and Gould 2017). Female-specific Transformer protein is produced as a consequence of female-specific Sex-lethal and also contributes to increased female size (Rideout et al. 2015). This size scaling also applies to individual organs. For example, the Drosophila female gut is longer than the male gut due Transformer activity (Hudry et al. 2016). It has also been suggested that Myc dose (it is X-linked) is a regulator of body size (Mathews et al. 2017), although the failed dosage compensation model proposed has not been demonstrated."

And again at line 74:

"These studies show that size is regulated, but they do not address whether scaling is uniform or non-uniform and the mechanism for sexual size differences (SSD). The origins of SSD can, in principle, arise from differences in (i) gene expression, (ii) the presence of sex-specific cell types, (iii) the number of cell-specific nuclei, or (iv) the size (per nucleus) of those cells. Previous research in Drosophila has largely focused on gene expression in sex-specific organs like the gonads (Arbeitman et al. 2002; Parisi et al. 2004; Graveley et al. 2011; Pal et al. 2023), which are governed by a well-characterized sex-determination pathway (Salz and Erickson 2010; Clough and Oliver 2012; Raz et al. 2023) However, whether and how scaling differences in shared, non-sex-specific tissues are achieved via changes in cell size and number remains largely unexamined (Fig. 1A2). These studies show that size is regulated, but they do not address whether scaling is uniform or non-uniform and the mechanism for size differences."

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2. Use of ribosomal gene expression as a proxy for cell size The authors use ribosomal gene expression levels as a proxy for cell size, but this assumption is not adequately justified. The cited references (refs. 20-22) focus on unicellular organisms (bacteria and yeast) or cleavage divisions in frog embryos, which are fundamentally different from adult Drosophila tissues. The authors should provide evidence that ribosome abundance scales with cell size across the distinct adult Drosophila cell types. Given that most adult fly tissues are post-mitotic, it is more likely that ribosomal gene expression reflects protein synthesis activity rather than cell size, particularly in secretory cell types.

Response: Reviewer 1 raised a similar point, and we agree. We recognize that the term "proxy" may have been misleading. We use this measure only in the context of sex bias within homogeneous cell clusters, and not between clusters, even when such clusters share the same cell-type annotation. To avoid overinterpretation, we changed "poxy" to "indicator".

In response to the reviewer's concern, we have expanded our discussion of the relevant supporting literature (additional text starting line 75). We have also directly measured translation in the fat body cells (section: Female bias in ribosomal gene expression in fat body cells leads to sex biased protein synthesis), which clearly demonstrates a correlation between ribosomal protein gene expression and biosynthetic activity. Although, we have not traced the chain of events from expression to ribosome assembly to polysome loading in all cell types, we did examine the nucleolus (Figure 4), where ribosomes are assembled, and we make a strong point that the volume of the nucleolus scales like ribosome protein gene expression. This provides strong evidence for sex-specific ribosome biogenesis contributing to cell size.

Furthermore, the observation that ribosomal gene expression likely reflects protein synthesis activity is not at odds with increased cell size: biosynthesis increases in larger cells (Schmoller and Skotheim 2015). We have added a panel to Figure 4 showing the relationship between ribosomal gene expression bias and the average expression bias of Eukaryotic Elongation Factor 1 (eEF1).

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3. Relationship between Myc and sex-biased Rp expression The proposed link between Myc and sex-biased Rp expression is unclear. Panels D and E of Figure 1 show no consistent relationship: some cell types with strong Rp sex bias exhibit either high or low female Myc bias, or even a male bias. The linear regression in Figure 4I (R = 0.07, p = 0.59) confirms the lack of correlation. The authors should clarify this point and adopt a more cautious interpretation regarding Myc as a potential regulator of sex-biased Rp expression and cell size differences. Experimentally, using Myc hypomorph or heterozygous conditions would be more appropriate than complete knockdown to test its role.

Response: Thank you for noting that the relationship between Myc expression bias and sex-biased RP expression required clarification. This response was prepared in consultation with Myc expert Dr. David Levens.

We demonstrate that both Myc and RP gene expression exhibit an overall female bias in the body. The absence of a strong correlation across cell clusters does not invalidate this conclusion. Myc is a well-established master regulator of ribosome biogenesis, but its quantitative effects are complex. According to recent models of Myc-mediated gene regulation (Nie et al. 2012; Lin et al. 2012), Myc upregulates all actively transcribed genes. Because this regulation is global, the relationship between changes in Myc expression and corresponding changes in ribosomal protein gene expression depends on cell type. Moreover, (Lorenzin et al. 2016) demonstrated that ribosomal protein genes saturate at relatively low levels of Myc, which helps explain why we observe a correlation in head cell clusters-where Myc expression is lower-but not in body clusters.

Importantly, on average, the female-specific Myc expression bias is stronger in body cell clusters than in head cell clusters, consistent with the stronger female bias in ribosomal protein gene expression observed in the head relative to the body.

To make this relationship more transparent, we combined the head and body clusters, which yielded a strong overall correlation (Fig. 4J, replacing the previous Fig. 4H).

To further strengthen the evidence linking ribosomal gene expression to cell size, we also examined the relationship between ribosomal gene expression bias and Elongation Factor 1 (eEF1) expression bias, a key component of protein biosynthesis during the elongation step of translation. The resulting correlation exceeds 0.9 (new Fig. 4H, added as an additional panel in Fig. 4).

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4. Conclusions about fat body cell number I have concerns about drawing conclusions on sex differences in fat body cell number from single-nucleus transcriptomic data for two reasons:

1- Drosophila fat body tissue is heterogeneous, comprising distinct subpopulations (e.g., visceral fat cells, subcuticular fat cells), some of which are sex-specific-such as fat cells associated with the spermathecae in females.

Response: Thank you for giving us the opportunity to clarify our analysis of the FCA data. Our approach does account for subpopulations within the fat body as well as within other cell types. Based on gene expression profiles, we identify three fat body clusters, all of which are reported in Table S3. One small female-specific cluster (

When all fat body clusters are combined into a single supercluster, this supercluster still shows a male bias. We have now clarified this point in the manuscript (line 113). Note that both subclusters of fat body are already shown in Fig. 1C and 1D.

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2- Adult fat body cells can be multinucleated (PMID: 13723227). Apparent sex differences in nucleus number may reflect differences in specific subpopulations or degrees of multinucleation rather than true differences in cell number. To strengthen the conclusions, the analysis should be performed at the level of fat body subpopulations, distinguishing clusters where possible. Additionally, quantifying nuclei relative to actual cell number-as done for muscle tissue-would clarify whether observed sex differences reflect true variation in cell number or differences in nuclear content per cell.

Response: Yes, some cells can be multinucleate. We specifically address this in the context of muscle cells, where multinucleation is prominent, and we also conducted experimental validation in this tissue. As noted above, our analysis is performed at the subpopulation level, since clusters are defined by expression similarity (Leiden resolution 4.0) rather than by annotation.

Because our work relies on single-nucleus data, each nucleus is treated as an individual unit of analysis. Nevertheless, we observe genuine nuclear differences within each cluster. Importantly, the presence of multinucleated cells does not alter our conclusions; it simply represents one form of variation in cell number that can be thought of as a subcomponent of cell/nuclei number.

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Minor corrections/points: 1-The term body size in the title does not accurately reflect the content of the paper. I recommend replacing it with organ size to better align with the study's focus.

Response: Thank you for the suggestion.

----------------------------------------------------------- 2-The term sexual size dimorphism is somewhat inaccurate in this context. Sex differences in size would be more appropriate. The term sexual dimorphism typically refers to traits that exhibit two distinct forms in males and females-such as primary or secondary sexual characteristics like sex organs or sex combs. In contrast, size is a quantitative trait that follows a normal distribution. Although the average female may be larger than the average male, the distributions overlap, making the term dimorphism imprecise.

Response: Thank you for the suggestion.

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3-In Figure 2E, there appears to be an inconsistency between the text, figure legend, and the data presented. The text and legend state that the total volume of dorsal longitudinal flight muscle cells was quantified, whereas the graph indicates measurements of nuclear size. This discrepancy should be clarified.

Response: Thank you for pointing this out. We figured out that Y-axis label in the graph was incorrect and it is now fixed.

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4-The authors proposed: "This increased biosynthetic activity in fat body cells may contribute to cell size differences, but also to the regulation of body size via production of factors that mediate body growth via interorgan communication". Please note that this hypothesis has already been tested functionally in PMID: 39138201 and was shown to be incorrect. Sex differences in body size are completely independent of fat body sexual identity or any intrinsic sex differences within fat cells.

__Response: __We thank the reviewer for the opportunity to discuss why the data shown in PMID 39138201 (Hérault et al. 2024) do not rule out a model in which the fat body contributes to the sex-specific regulation of body size via interorgan communication. The main reason data in Herault et al cannot rule out such a model is that they use wing size as a proxy for body size. This is in contrast to prior studies, such as (Rideout et al. 2015), in which pupal volume was used to directly measure body size and show a non-autonomous effect of sex determination gene transformer on body size. Measuring body size directly is a more precise readout of growth during the larval stages of development, as opposed to using adult wing area which reflects the growth of a single organ. It is also important to note that the diets used to rear flies in Herault and Rideout differ, which is an important consideration as females do not achieve their maximal size without high dietary protein levels (Millington et al. 2021). To ensure all these points are communicated to readers, we added text to this effect in the revised version of our manuscript.

Added at line 254:

"This increased biosynthetic activity in fat body cells may contribute to cell size differences, but also to the regulation of body size via production of factors that mediate body growth via interorgan communication (Colombani et al. 2003; Géminard et al. 2009; Rajan and Perrimon 2012; Sano et al. 2015; Koyama and Mirth 2016). Indeed, one study showed the sexual identity of the fat body influenced pupal volume, which is an accurate readout of larval growth (Rideout et al. 2015; Delanoue et al. 2010). While a recent study suggests that male-female differences in body size were regulated independently of fat body sexual identity (Hérault et al. 2024), this study measured the growth of a single organ, the wing, as a proxy for body size. Additional studies are therefore needed to resolve whether fat body protein synthesis plays an important role in regulating sex differences in body size."

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*5-The authors state: "This demonstrate that Myc plays a key role in regulating the sex difference in nucleolar size." This is an overstatement given the functional data presented. The claim should be toned down to reflect the limited evidence.

**Referee cross-commenting**

I completely agree with the main comments of Reviewer 1, as they address the paper's core.*

Response: We have addressed the comments of Reviewer 1 in the response to reviewer's comments above.

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*Reviewer #3 (Significance (Required)):

The main novelty and strongest aspect of this study is its use of single-nucleus transcriptomic data from the adult Drosophila Cell Atlas to investigate how different cell types adopt distinct strategies to generate sex differences in organ size-either by increasing cell size or by altering cell number. Previous studies have largely focused on specific tissues, whereas this work provides a comprehensive, organism-wide view that encompasses all tissues, enabling direct cross-comparison between organs. This represents a clear advance in the field, primarily from a technical perspective, by leveraging organism-wide single-cell transcriptomics. The main limitations lie in the lack of functional experiments and mechanistic insights. Moreover, the proposed mechanism-differences in Myc gene dosage or expression levels-is not entirely novel, as Myc dosage has previously been implicated in contributing to sex differences in body size (PMID: 28064166).*

Response: We do have some functional testing in the 3 tissues, flight muscle, heart and fat body, however, providing mechanistic insights is beyond the scope of this paper. The paper suggested by the reviewer is an example of one attempt to provide such a mechanism, probably not the only one. We hope that our rich data that we have assembled in this paper provide resources for generating hypotheses and stimulate further research.

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References

Cadart, Clotilde, and Rebecca Heald. 2022. "Scaling of Biosynthesis and Metabolism with Cell Size." Molecular Biology of the Cell 33 (9): pe5. https://doi.org/10.1091/mbc.E21-12-0627.

Diegmiller, Rocky, Caroline A. Doherty, Tomer Stern, Jasmin Imran Alsous, and Stanislav Y. Shvartsman. 2021. "Size Scaling in Collective Cell Growth." Development (Cambridge, England) 148 (18): dev199663. https://doi.org/10.1242/dev.199663.

Gallant, Peter. 2013. "Myc Function in Drosophila." Cold Spring Harbor Perspectives in Medicine 3 (10): a014324. https://doi.org/10.1101/cshperspect.a014324.

Grewal, Savraj S., Ling Li, Amir Orian, Robert N. Eisenman, and Bruce A. Edgar. 2005. "Myc-Dependent Regulation of Ribosomal RNA Synthesis during Drosophila Development." Nature Cell Biology 7 (3): 295-302. https://doi.org/10.1038/ncb1223.

Hérault, Chloé, Thomas Pihl, and Bruno Hudry. 2024. "Cellular Sex throughout the Organism Underlies Somatic Sexual Differentiation." Nature Communications 15 (1): 6925. https://doi.org/10.1038/s41467-024-51228-6.

Lin, Charles Y., Jakob Lovén, Peter B. Rahl, et al. 2012. "Transcriptional Amplification in Tumor Cells with Elevated C-Myc." Cell 151 (1): 56-67. https://doi.org/10.1016/j.cell.2012.08.026.

Lorenzin, Francesca, Uwe Benary, Apoorva Baluapuri, et al. 2016. "Different Promoter Affinities Account for Specificity in MYC-Dependent Gene Regulation." eLife 5 (July): e15161. https://doi.org/10.7554/eLife.15161.

Ma, Tian-Hsiang, Po-Hsiang Chen, Bertrand Chin-Ming Tan, and Szecheng J. Lo. 2018. "Size Scaling of Nucleolus in Caenorhabditis Elegans Embryos." Biomedical Journal 41 (5): 333-36. https://doi.org/10.1016/j.bj.2018.07.003.

Marygold, Steven J., John Roote, Gunter Reuter, et al. 2007. "The Ribosomal Protein Genes and Minute Loci of Drosophila Melanogaster." Genome Biology 8 (10): R216. https://doi.org/10.1186/gb-2007-8-10-r216.

Millington, Jason W., George P. Brownrigg, Charlotte Chao, et al. 2021. "Female-Biased Upregulation of Insulin Pathway Activity Mediates the Sex Difference in Drosophila Body Size Plasticity." eLife 10 (January): e58341. https://doi.org/10.7554/eLife.58341.

Nie, Zuqin, Gangqing Hu, Gang Wei, et al. 2012. "C-Myc Is a Universal Amplifier of Expressed Genes in Lymphocytes and Embryonic Stem Cells." Cell 151 (1): 68-79. https://doi.org/10.1016/j.cell.2012.08.033.

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Schmoller, Kurt M., and Jan M. Skotheim. 2015. "The Biosynthetic Basis of Cell Size Control." Trends in Cell Biology 25 (12): 793-802. https://doi.org/10.1016/j.tcb.2015.10.006.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Pal and colleagues addresses an important question: the cellular mechanisms underlying sex differences in organ size. By leveraging single-nucleus transcriptomic data from the adult Drosophila Cell Atlas, the authors show that different cell types adopt distinct strategies to achieve sex differences in organ size-either by increasing cell size or by altering cell number. They then focus on three organs-the indirect flight muscles, the heart, and the fat body-and provide supporting evidence for their transcriptomic analyses.

This study tackles a highly relevant and often overlooked question, as our understanding of the molecular and cellular events driving sex differences remains incomplete. The work presents interesting observations; however, it is largely descriptive, establishing correlations without providing functional evidence or mechanistic insight.

Below are four main points that should be addressed before publication:

1. Introduction and contextualisation of prior work The introduction does not adequately present the current state of knowledge. Several key studies are missing or insufficiently discussed. In particular, the following works should be included and integrated into the introduction:
   • PMID: 26710087 - shows that the sex determination gene transformer regulates male-female differences in Drosophila body size.
   • PMID: 28064166 - describes how differences in Myc gene dosage contribute to sex differences in body size.
   • PMID: 2688749 - demonstrates that the intrinsic sexual identity of adult stem cells can control sex-biased organ size through sex-biased proliferation.
   • PMID: 28976974 - reveals that Sxl modulates body growth through both tissue-autonomous and non-autonomous mechanisms.
   • PMID: 39138201 - shows that transformer drives sex differences in organ size and body weight. Incorporating and discussing these references would provide a more comprehensive and up-to-date framework for the study.
2. Use of ribosomal gene expression as a proxy for cell size The authors use ribosomal gene expression levels as a proxy for cell size, but this assumption is not adequately justified. The cited references (refs. 20-22) focus on unicellular organisms (bacteria and yeast) or cleavage divisions in frog embryos, which are fundamentally different from adult Drosophila tissues. The authors should provide evidence that ribosome abundance scales with cell size across the distinct adult Drosophila cell types. Given that most adult fly tissues are post-mitotic, it is more likely that ribosomal gene expression reflects protein synthesis activity rather than cell size, particularly in secretory cell types.
3. Relationship between Myc and sex-biased Rp expression The proposed link between Myc and sex-biased Rp expression is unclear. Panels D and E of Figure 1 show no consistent relationship: some cell types with strong Rp sex bias exhibit either high or low female Myc bias, or even a male bias. The linear regression in Figure 4I (R = 0.07, p = 0.59) confirms the lack of correlation. The authors should clarify this point and adopt a more cautious interpretation regarding Myc as a potential regulator of sex-biased Rp expression and cell size differences. Experimentally, using Myc hypomorph or heterozygous conditions would be more appropriate than complete knockdown to test its role.
4. Conclusions about fat body cell number I have concerns about drawing conclusions on sex differences in fat body cell number from single-nucleus transcriptomic data for two reasons:

1) Drosophila fat body tissue is heterogeneous, comprising distinct subpopulations (e.g., visceral fat cells, subcuticular fat cells), some of which are sex-specific-such as fat cells associated with the spermathecae in females.

2) Adult fat body cells can be multinucleated (PMID: 13723227). Apparent sex differences in nucleus number may reflect differences in specific subpopulations or degrees of multinucleation rather than true differences in cell number. To strengthen the conclusions, the analysis should be performed at the level of fat body subpopulations, distinguishing clusters where possible. Additionally, quantifying nuclei relative to actual cell number-as done for muscle tissue-would clarify whether observed sex differences reflect true variation in cell number or differences in nuclear content per cell.

Minor corrections/points:

1. The term body size in the title does not accurately reflect the content of the paper. I recommend replacing it with organ size to better align with the study's focus.
2. The term sexual size dimorphism is somewhat inaccurate in this context. Sex differences in size would be more appropriate. The term sexual dimorphism typically refers to traits that exhibit two distinct forms in males and females-such as primary or secondary sexual characteristics like sex organs or sex combs. In contrast, size is a quantitative trait that follows a normal distribution. Although the average female may be larger than the average male, the distributions overlap, making the term dimorphism imprecise.
3. In Figure 2E, there appears to be an inconsistency between the text, figure legend, and the data presented. The text and legend state that the total volume of dorsal longitudinal flight muscle cells was quantified, whereas the graph indicates measurements of nuclear size. This discrepancy should be clarified.
4. The authors proposed: "This increased biosynthetic activity in fat body cells may contribute to cell size differences, but also to the regulation of body size via production of factors that mediate body growth via interorgan communication". Please note that this hypothesis has already been tested functionally in PMID: 39138201 and was shown to be incorrect. Sex differences in body size are completely independent of fat body sexual identity or any intrinsic sex differences within fat cells.
5. The authors state: "This demonstrate that Myc plays a key role in regulating the sex difference in nucleolar size." This is an overstatement given the functional data presented. The claim should be toned down to reflect the limited evidence.

Referee cross-commenting

I completely agree with the main comments of Reviewer 1, as they address the paper's core.

Significance

The main novelty and strongest aspect of this study is its use of single-nucleus transcriptomic data from the adult Drosophila Cell Atlas to investigate how different cell types adopt distinct strategies to generate sex differences in organ size-either by increasing cell size or by altering cell number. Previous studies have largely focused on specific tissues, whereas this work provides a comprehensive, organism-wide view that encompasses all tissues, enabling direct cross-comparison between organs. This represents a clear advance in the field, primarily from a technical perspective, by leveraging organism-wide single-cell transcriptomics. The main limitations lie in the lack of functional experiments and mechanistic insights. Moreover, the proposed mechanism-differences in Myc gene dosage or expression levels-is not entirely novel, as Myc dosage has previously been implicated in contributing to sex differences in body size (PMID: 28064166).

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Referee #2

Evidence, reproducibility and clarity

The authors analyzed the FlyAtlas single-nucleus dataset to identify sex differences in gene expression and cell numbers. This led them to focus on muscles, cardiomyocytes, and fat body cells. They then measured cell and nucleolus size across different tissues and showed that reducing Myc function decreases sex differences in fat body cells. Overall, the manuscript provides a characterization of dimorphic differences in cell and organ size across three tissues.

Major Comments:

The major claims of the manuscript are well supported by the reported experiments and analyses. Statistical analyses appear adequate.

Minor Comments:

The following minor issues should be addressed through textual edits:In the Introduction:

"Disruptions in proportionality, whether due to undergrowth or overgrowth, can lead to reduced fitness or diseases such as cancer."

Could the authors provide a reference for this statement, particularly for the claim that disruptions in proportionality can lead to cancer?

The authors state:

"This study offers a comprehensive, cellular-resolution analysis of sexual size dimorphism in a model organism, uncovering how differences in cell number and size contribute to sex-specific body plans."

The study cannot be considered comprehensive, as not all organs were examined.

The following sentence from the abstract is unclear:

"By uncovering how a conserved developmental system produces sex-specific proportions through distinct cellular strategies..."

What do the authors mean by a conserved developmental system? Do they refer to a commonly used developmental model, or to a developmental system that is evolutionarily conserved?

Significance

The manuscript presents a relevant exploration of sex-specific differences in cell size and cell number in Drosophila males and females. The limitations of the study are clearly acknowledged in the "Limitations" section. The work does not provide mechanistic insight into the causes or functional consequences of the observed differences. Nonetheless, the study extends our understanding of sexual dimorphism and establishes a foundation for future investigations into the autonomous and systemic mechanistic factors that regulate these differences.

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Referee #1

Evidence, reproducibility and clarity

This paper addresses the interesting question of how cell size may scale with organ size in different tissues. The approach is to mine data from the fly single cell atlas (FCA) which despite its name is a databse of gene expression levels in single isolated nuclei. Using this data, they infer cell size based on ribosomal protein gene expression, and based on this approach infer that there are tissue and sex specific differences in scaling, some of which may be driven by differences in ribosomal protein gene expression.

I think the idea of mining this database is a clever one, however there a number of concerns about whether the existing data can really be used to draw the conclusions that are stated.

One concern has to do with the assumption that RP (ribosome protein) expression is a proxy for cell size. It is well established that ribosome abundance sclse with cell size, but is there reason to believe that ribosome nuclear gene EXPRESSION correlates with ribosome abundance? I'm not saying that this can't be true, but it seems like a big assumption that needs to be justified with some data. Maybe this is well known in the Drosophila literature, but in that case the relevant literature really needs to be cited.

Second, the interpretation of RP expression as a proxy for cell size seems potentially at odds with the fact that some cells are multi-nucleate. those cells are big because of multiple nuclei, and so they might not show any increase in ribosome expression per nucleus. presumably for a multi-nucleate cells, RP expression if it reflects anythnig at all would be something to do with cell size PER nucleus.

Third, it is well known that many tissues in Drosophila are polyploid or polytene. I don't know enough about the methodology used to produce the FCA to know whether this is somehow normalized. Otherwise, my hypothesis would be that nuclei showing higher RP expression might just be polyploid or polytene. You might say that this could be controlled by asking if all genes are similary upregulated, but that isn't the case since at least in polytene chromosomes it is well known that only a small number of genes are expressed at a given time, while many are silent.

Overall, I think a lot more foundational work would need to be done in order to allow the inference of cell size from RP expression. In a way, it is a bit unfortunate that they chose to do this work in Drosophila where so many cells are polyploid, although I gather that even in humans some tissues have this issue, for example large neurons in the brain.

Significance

The idea that gene regulatory networks could "program" differences in scaling by changing levels of ribosomal protein gene expression is a tremendously important one if it can be established, because it would show a simple way for size scaling to be placed under control of developmental regulatory pathways. My original concern when I first looked at the abstract was going to be that yeah the results are interesting but a mechanism is not provided, but as I read it, that concern went away. showing that RP gene expression, which could be programmed by various driving pathways, can affect allometric scaling, would be extremely impactful and really change how we think about scaling, but putting it into the framework of gene expression networks that control other aspects of developmewnht. it would not be necessary to show which pathways actually drive these expression differences, the fact that they are different would be interesting enough to make everyone want to read this paper. But as discussed above I am not, however, convinced by the evidence presented here. So while I think it would be very significant if true, I am not convinced that the conclusion is well supported. This doesn't mean I have a reason to think it is false, just that its not well supported for the reasons I have given.

I hasten to point out that I could be entirely wrong, if the missing bits of logic (i.e. that RP expression matches ribosome abundance and that gene expression in the FCA dataset isn't influenced by ploidy of the nucleus). If suitable references can be provided to support these underlying assumptions, then in fact I think these concerns could be answered with very little effort. Otherwise, I think experiments would be needed to support these assumptions, and that might be non-trivial to do in a reasonable time frame. for that reason, in the next question I have put "cannot tell" for the time estimate.

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Reply to the reviewers

Manuscript number: RC-2025-03091

Corresponding author(s): Chia-Tsen, Tsai, Liuh-Yow Chen

1. General Statements [optional]

We thank the reviewers for their valuable time and constructive feedback on our study, which ultimately improved our manuscript. Herein, we provide a detailed response to each of the reviewers' comments, supported by new data that have been integrated into both the main text and the supplementary figures.

2. Point-by-point description of the revisions

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

Summary This manuscript builds upon the authors' prior findings that targeting COUP-TF2 to TRF1 induces ALT-associated phenotypes and G2-mediated synthesis in telomerase-immortalised BJT human fibroblasts. In this study, the authors show that telomere-coupled COUP-TF2 promotes H3K9me3 enrichment in these cells, and that this effect is blocked by TRIM28 depletion. Furthermore, TRIM28 depletion also suppresses the formation of ALT phenotypes in VA13 ALT cells. Given that TRIM28 has been implicated in regulating H3K9me3 deposition via SETDB1, and has been reported to co-purify with TR2 and TR4 (though not previously in the context of ALT telomeres), these findings add mechanistic depth to how heterochromatin regulators contribute to ALT activity. Overall, the manuscript's conclusions are generally supported by the presented data, but several aspects require clarification or additional experimental validation.

The authors report a modest reduction in telomeric H3K9me3 following COUP-TF2 and TR4 depletion in U-2 OS and VA13 cells (Figure 1B). To strengthen the claim that these orphan receptors specifically regulate H3K9me3, the authors should 1) Assess additional heterochromatic histone marks (e.g., H4K20me3) at telomeres, 2) Normalize telomeric signals to both parental histone levels and input, and 3) Evaluate whether global H3K9me3 levels also decrease upon receptor depletion

Response: We appreciate the reviewer's suggestion. To address the concern regarding specificity, we assessed H3K27me3 and H4K20me3 levels upon COUP-TF2/TR4 depletion and found no significant changes (Supplementary Fig. 1C). Furthermore, we reprocessed the telomeric ChIP data, normalizing to both input DNA and parental histone levels (Figure 1B). This refined analysis reinforces our original conclusion. Finally, Western blot analysis showed no significant changes in global H3 or H3K9me3 levels upon COUP-TF2/TR4 depletion (Figure 1A). Altogether, these results further support the specificity of COUP-TF2/TR4 for H3K9me3 at telomeres. We have revised the main text (page 3) and updated Figure 1A, 1B, and Supplementary Figure 1C for these changes.

Most experiments explore chromatin changes in telomerase-positive BJT fibroblasts (Figure 2, Figure 4D). It remains unclear whether similar manipulations in ALT cells yield consistent effects, which would give a broader context for ALT phenotype induction. Are ALT phenotypes similarly induced in ALT cells? Does altered chromatin status affect telomere length or telomerase recruitment/activity? Can these pathways drive ALT phenotypes in non-immortalised cells?

Response: We appreciate the reviewer's suggestion and have explored chromatin changes in telomerase-negative BJ and IMR90 primary fibroblasts (Supplementary Fig. 2C, D). Consistent to the result in BJ-telomerase cells, we found that VP64-TRF1 decreased telomeric H3, H4, and H3K9me3 levels, whereas KRAB-TRF1 increased these marks. Moreover, expression of either VP64-TRF1 or KRAB-TRF1 was sufficient to induce APB formation and ATDs in BJ and IMR90 cells. These results indicate that the chromatin changes at telomeres can drive ALT phenotypes in both primary and telomerase-immortalized fibroblast cells.

    Additionally, regarding whether chromatin alteration affects telomere length or telomere regulation, we have explored telomere length changes in BJT cells expressing vector, TRF1, KRAB-TRF1 or VP64-TRF1. The result of telomere restriction fragment (TRF) assay showed that the cells of all conditions maintained static telomere lengths through 30 days in culture (data shown below), suggesting that the chromatin alterations may not impact telomerase recruitment or activity. As this result is beyond the scope of current study, this data is only shown here in the rebuttal letter for a reference and is not included in the revised manuscript.

    Moreover, according to the reviewer's suggestion, we also carried out VP64-TRF1 or KRAB-TRF1 expression experiments in WI38-VA13/2RA cells that express high TERRA and have altered chromatin structures. Our data revealed that VP64-TRF1 suppresses telomere H3K9me3 and ALT activity, while KRAB-TRF1 increases both (Supplementary Figure 2E), suggesting an association of heterochromatin state with ALT activation in WI38-VA13/2RA cells.

    The observation that VP64-TRF1 reduces ALT activity in WI38-2RA/VA13 cells contrasts with findings in BJT cells. It is worth noting that studies from the Azzalian and Linger groups demonstrated that experimentally induced TERRA expression promotes ALT activity in ALT and non-ALT cells (PMID: 36122232, PMID: 40624280). Therefore, we propose that TERRA upregulation by VP64-TRF1 may contribute to the ALT induction observed in BJT cells (Supplementary Figure 2A, B), whereas the ability of VP64-TRF1 to suppress ALT activity in WI38-2RA/VA13 cells could be attributed to the reduction of telomere H3K9me3 and heterochromatin loss. Importantly, KRAB-TRF1 concurrently enhanced histone H3, H4, and H3K9me3 occupancy and ATL activity in both human fibroblasts and ALT cells. Altogether, these results support the notion that heterochromatin formation triggers ALT.

    We also examined TRIM28 recruitment to telomeres by telomere-ChIP and found that COUP-TF2LBD-TRF1 promotes TRIM28 telomere enrichment in BJ, IMR90 and U2OS, similar to BJT cells (Supplementary Fig. 5A-D).  Moreover, in ALT cell lines WI38-2RA/VA13, U2OS, and Saos-2, depletion of COUP-TF2 or TR4 reduced TRIM28 telomeric association (Figure 4A, B). Together, the data from human fibroblasts and ALT cells supports a role of orphan NRs in recruiting TRIM28 to ALT telomeres.

We acknowledge the reviewer's suggestions, which allow us to clarify and strengthen the conclusions. The corresponding data are presented in Figure 4A-B and Supplementary Figure 2B-D and 5E-F, and the main text has been modified on page 4-6 in the revised manuscript.

When referring to Figure 3G, the authors state that that telomeric H3K9me3 was abolished upon depleting TRIM28 from the U2OS and WI38-VA13/2RA cells. Abolished is a strong word for a 50% decrease, and this sentence should be revised. The reduction appears greater than that seen with COUP-TF2/TR4 depletion. Are the effects additive? If so, might TRIM28 act, at least in part, independently of COUP-TF2/TR4?

Response: We appreciate the reviewer's comments. We have revised the manuscript on page 5, replacing "abolished" with "significantly reduced" to better describe the effect of TRIM28 depletion on telomeric H3K9me3. To further investigate the interplay between TRIM28 and orphan NRs in regulating telomeric H3K9me3, we conducted single and combined knockdown experiments in U2OS and WI38-VA13/2RA cells, followed by telomere-ChIP analysis (Supplementary Figures 4D, E). Our results showed that single depletion of either orphan NRs or TRIM28 lead to a similar decrease in telomeric H3K9me3, and that combined knockdown do not result in any further reduction. These findings support an epistatic interaction between orphan NRs and TRIM28 in the regulation of telomeric H3K9me3. We have expanded on this interpretation in the main text (page 6) and included the relevant data in Supplementary Figures 4D, E.

VA13 cells consistently exhibit stronger effects than U-2 OS (e.g., Figures 1 and 3). This discrepancy could be linked to the high content of variant repeats in VA13 cells. The authors should assess whether variant repeat content underlies the differential response. Repeating key experiments in additional ALT lines with varied repeat compositions would be informative.

Response: We appreciate the reviewer's suggestion and have extended our analyses to two additional ALT osteosarcoma cell lines, SAOS-2 and G292. In both lines, depletion of orphan NRs resulted in a consistent decrease in telomeric H3K9me3 levels (Supplementary Figures 1A, B). We also examined the contribution of TRIM28 to telomeric H3K9me3 in these cells. siRNA-mediated depletion of TRIM28 in SAOS-2 and G292 cells similarly caused a significant reduction in telomeric H3K9me3 and ALT phenotypes (Supplementary Figure 4A-C). Together, these results from 4 ALT cell lines confirm that orphan NRs and TRIM28 promote telomeric H3K9me3 formation in ALT cells. We have modified the main text on page 3 and 5-6 for these results.

In line with the previous point, it would be useful to show whether TRIM28 telomeric enrichment is affected by COUP-TF2/TR4 depletion in U2OS cells (Figure 4C). To improve confidence in these findings, the authors should perform telomeric ChIP assays, especially with the COUP-TF2^LBDΔAF2-TRF1 mutant construct.

Response: Following the reviewer's suggestion, we performed telomere-ChIP assays to assess TRIM28 enrichment at telomeres upon expression of COUP-TF2LBD-TRF1 and its ΔAF2 mutant in U2OS cells. Consistent with our immunofluorescence results, telomere-ChIP revealed that COUP-TF2LBD-TRF1 expression promotes TRIM28 telomere enrichment, while the AF2 deletion mutant failed to recruit TRIM28 (Supplementary Figure 5D). We have modified the main text on page 6 for this result.

The immunoprecipitation experiments showing TRIM28 association with orphan receptors should include benzonase treatment to rule out DNA-mediated co-association (Figure 4F-G).

Response: We appreciate the reviewer's suggestion. To address the possibility of DNA-mediated interactions, we pre-incubated cell lysates with benzonase prior to Co-IP (Page 7). This treatment did not disrupt the association between TRIM28 and COUP-TF2 or TR4 in WI38-VA13/2RA and BJT cells (Supplementary Figures 5E-G), indicating a DNA-independent interaction. We have modified the main text on page 7 for this result.

The study would benefit from a direct assessment of whether COUP-TF2LBDΔAF2-TRF1 fails to induce ALT phenotypes in BJTfibroblasts.

Response: We thank the reviewer for this suggestion. As the role of the COUP-TF2 AF2 domain in ALT induction in BJT fibroblasts has recently been thoroughly investigated and published by our group (PMID: 38752489), we have directed the current study towards a more detailed mechanistic question. Specifically, we have carried out experiments to further demonstrate that COUP-TF2 recruits TRIM28 to telomeres via its AF2 domain in both human fibroblasts and ALT cells (Supplementary Figures 5A-D). On Page 6, we have modified the main text for these results and included a citation to our previous publication to provide the necessary background.

The experiments performed in Figure 5E-H lack a vector-only + siCtrl control.• In Figure 5E, the observation that APB formation is restored in siTRIM28 + Vector-treated cells is unexpected. The authors should address this finding and clarify whether this reflects biological noise or a compensatory effect.

Response: We thank the reviewer for this suggestion. We have repeated the experiments with a revised design, ensuring a consistent vector background across all groups (Vector + siCtrl, Vector + siTRIM28, TRIM28 WT + siTRIM28, and TRIM28 ΔRBCC + siTRIM28) (Figure 5E-H). This improved design confirms that expression of wild-type TRIM28, but not TRIM28 ΔRBCC, restores APB formation, ATDS, ssTeloC, and telomeric H3K9me3 levels in TRIM28-depleted cells. The updated dataset also resolves the previous unexpected increase in APB formation in the siTRIM28 + Vector condition, which is now excluded. We have modified the main text accordingly on page 8.

Reviewer #1 (Significance (Required)):

This work offers valuable mechanistic insight into how COUP-TF2 and TRIM28 coordinate to regulate heterochromatin deposition and ALT phenotype formation. It adds to the growing understanding of chromatin-mediated telomere regulation. What remains unclear is how important this interaction is for ALT maintenance, as H3K9me3 is only moderately altered upon TRIM28 depletion in ALT cells. Depletion of TRIM28 has been shown previously to induce APB formation and telomere elongation in U-2 OS ALT cells (Wang et al., 2021), the opposite to what the authors observed here in VA13 cells (Figure 5E-H). Clarifying whether these differences are variant repeat-dependent, or reflect intrinsic features of specific ALT cell lines, would substantially elevate the study's impact.

Response: We appreciate the reviewer's recognition of the significance of our work in elucidating the molecular basis of ALT regulation through COUP-TF2-TRIM28-mediated heterochromatin formation. In response to the reviewer's insightful comment regarding the importance of this interaction for ALT maintenance, we have expanded our study. We now include data from three additional primary human fibroblasts and a total of four ALT cancer cell lines (Figure 4, Supplementary Figure 4). These new data further strengthen the conclusion that TRIM28 promotes telomeric H3K9me3 and ALT-associated features. Furthermore, our rescue experiments support the model that the ALT-promoting function of TRIM28 in both fibroblasts and ALT cell lines is mediated through its physical interaction with COUP-TF2 (Supplementary Figure 5). We believe these results provide a solid foundation for demonstrating a cooperative role of COUP-TF2 and TRIM28 in ALT maintenance, and address the reviewer's concern regarding the generalizability of our findings.

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

Summary This manuscript investigates the role of orphan nuclear receptors (ORs), specifically COUP-TF2 and TR4, in promoting H3K9me3 enrichment at ALT telomeres via recruitment of TRIM28 (KAP1). The authors propose that the AF2 domain of COUP-TF2, located in its ligand-binding domain (LBD), is sufficient to recruit TRIM28 to telomeres. This, in turn, promotes heterochromatinization and induces hallmarks of the Alternative Lengthening of Telomeres (ALT) pathway, including APB formation and telomeric DNA synthesis outside of S-phase. This study addresses one important and unresolved question in the field: by what mechanism is the heterochromatic state established at ALT telomeres? Another timely question, not addressed here is: how is heterochromatin (specifically H3K9me3) functionally linked to ALT? The findings are potentially novel and mechanistically insightful. However, key elements of the study, particularly the central tethering experiments, require stronger quantification and clarity. Additional mechanistic tests and literature adjustments would also improve the manuscript.

Major Concerns

Central TRF1-COUP-TF2-LBD result lacks quantification and clarity: the tethering of COUP-TF2's LBD to telomeres via TRF1 is a core result of the paper. This experiment demonstrates that this domain is sufficient to induce weak H3K9me3 enrichment and ALT features (APBs and ATDS). However, the supporting ALT data are presented only in Supplementary Figures S1A and S1B, and are not quantified. These data should be quantified with appropriate statistics and moved to a main figure.

Response: The current study builds upon our recent publication (PMID: 38752489), which comprehensively analyzed ALT induction (APBs, ATDS, C-circles, T-SCEs) by orphan NR-TRF1 expression (COUP-TF1, COUP-TF2, TR2, and TR4; full-length and LBD) in various human fibroblast cell lines. To avoid potential duplicate publication concerns, particularly regarding APB and ATDS results for COUP-TF2LBD-TRF1 in BJT cells, we have put the data with revised quantification results in Supplementary Figure 1D-E. We will follow the reviewer's suggestion and move this data to the main figures if the editors agree.

Furthermore, the broader functional implication is not explored. Does this tethering induce a fully functional ALT pathway? For example, can telomerase knockout cells expressing TRF1-COUP-TF2-LBD maintain long-term proliferation? Such evidence would significantly strengthen the impact of the study.

Response: While COUP-TF2LBD-TRF1 expression rapidly induces key ALT phenotypes, we acknowledge that this alone is insufficient to directly promote telomere lengthening and long-term proliferation of primary fibroblasts, as discussed in Gaela et al., 2024 (PMID: 38752489). However, our ongoing, unpublished studies indicate that COUP-TF2LBD-TRF1 can drive immortalization of primary BJ fibroblasts expressing SV40LT by promoting ALT-mediated telomere elongation (Attached Figure A-C; additional data not shown). These findings suggest that COUP-TF2 may cooperate with additional genetic or epigenetic alterations to facilitate ALT development. We appreciate the reviewer's recognition of this critical aspect. As our immortalization study is still in progress and will be the subject of a separate manuscript, we hope the reviewer understands that the data shown in this letter will not be included in the revised manuscript.

Chromatin manipulation experiments lead to ambiguous conclusions: the authors propose that telomeric heterochromatin promotes ALT activity, but their own experiments (e.g., Figure 2) show that both heterochromatin-inducing (KRAB-TRF1) and euchromatin-inducing (VP64-TRF1) tethering can trigger ALT-like features. This makes it difficult to conclude that heterochromatin is specifically required.

To clarify:

-Did the authors express TRF1-VP64 in an ALT cell line? According to their model, this should suppress ALT activity.

-More broadly, do chromatin alterations per se (regardless of direction) trigger ALT features? Clarifying these points is important for interpretation.

Response: In response to the reviewer's suggestion, we expressed VP64-TRF1 and KRAB-TRF1 in WI38-2RA/VA13 cells to investigate telomere chromatin changes and ALT activity. Our data indeed revealed that VP64-TRF1 suppresses telomere H3K9me3 and ALT activity, while KRAB-TRF1 increases both (Supplementary Figure 2E), suggesting that heterochromatin triggers ALT activation.

The observation that VP64-TRF1 reduces ALT activity in WI38-2RA/VA13 cells contrasts with findings in BJT cells. Of note, studies from the Azzalian and Lingner groups demonstrated that experimentally induced TERRA expression promotes ALT activity in ALT and non-ALT cells (PMID: 36122232, PMID: 40624280). Therefore, we propose that TERRA upregulation may contribute to the ALT induction observed in BJT cells (Figure 2A, Supplementary Figure 2A, B). Given the high basal TERRA expression, expression of VP64-TRF1 and KRAB-TRF1 did not result in a consistent change in TERRA levels (Supplementary Figure 2F). Thus, the ability of VP64-TRF1 to suppress ALT activity in WI38-2RA/VA13 cells could be attributed to the reduction of telomere H3K9me3 and heterochromatin loss. Altogether, our results support the hypothesis that heterochromatin formation, rather than euchromatin triggers ALT.

We thank the reviewer's insightful comments, which have allowed us to resolve the ambiguity of our results and strengthen the notion that heterochromatin formation promotes ALT. We think that the heterochromatin features and high TERRA expression represent two independent, coexisting mechanisms within ALT cancer cells to guarantee ALT activation. We have modified the main text on page 4-5 accordingly.

TERRA downregulation contradicts current models: while TERRA upregulation is often observed in ALT cells and is thought to contribute to replication stress and recombination at telomeres, the authors show that TRF1-KAP1 expression induces ALT features while TERRA is downregulated. This observation is not addressed in the manuscript. The authors should at least discuss this discrepancy and propose whether this reflects a cell line-specific phenomenon or a decoupling between TERRA levels and ALT induction in this context.

Response: We thank the reviewer for the comments. As mentioned above (Major Concerns 2), heterochromatin formation and TERRA expression are two mechanisms that can independently promote ALT. Unlike ALT cell lines that have high TERRA levels, human fibroblasts BJ cells have low TERRA that does not induce ALT phenotypes. Thus, the effect of KRAB-TRF1 on ALT induction in BJ cells could be attributed to the heterochromatin formation, but not reduction of TERRA. We have modified the main text on page 5 to clarify the result.

Minor Comments

Introduction (p. 3): The authors cite Episkopou et al. as showing increased H3K9me3 at ALT telomeres. This is incorrect; that paper suggests the opposite. The first study to clearly demonstrate H3K9me3 enrichment at ALT telomeres is Cubiles et al., 2018 and should be cited instead. Results (p. 5, first paragraph): The manuscript should cite Déjardin and Kingston, 2009 as the first to report COUP-TF2 and TR4 localization at ALT telomeres. The studies by Conomos et al., 2012 and Gaela et al., 2024 build on this prior evidence. Please also include this citation in the bibliography.

Response: We appreciate the reviewer's careful reading and for pointing out these errors. The citation errors on pages 2 and 3 have now been corrected.Broader relevance of TRIM28-OR interaction: TRIM28 is a complex protein with roles in SUMOylation, heterochromatin formation, and transcriptional initiation/elongation regulation.

The authors should explore whether similar COUP-TF2/TRIM28 interactions occur at other genomic loci. Public ChIP-seq data for COUP-TF2, TR4, and TRIM28 could be mined to investigate whether these factors co-occupy regulatory regions elsewhere in the genome, and how this relates to gene expression states.

Response: We appreciate the reviewer's insightful suggestion regarding a potential genome-wild functional interaction between TRIM28 and COUP-TF2. To address this, we analyzed public ENCODE ChIP-seq data from K562 cells (TRIM28: ENCSR000BRW; COUP-TF2: ENCSR000BRS). This analysis revealed 3,326 co-binding sites for TRIM28 and COUP-TF2 (Attached Figure A). Interestingly, these co-binding sites were preferentially located within gene bodies (70.7%) and promoter regions (4.3%) (Attached Figures B-D), suggesting a potential cooperative role in gene regulation that aligns with our observation of physical interaction. While the finding is intriguing, a full exploration is beyond the scope of this manuscript, which focuses on ALT telomere regulation. We consider this is an important insight and have briefly noted it in the discussion (p. 9), although the corresponding analyses are not included in the revised manuscript.

Reviewer #2 (Significance (Required)):

This work contributes mechanistic insight into how heterochromatin is established at ALT telomeres-an important and timely question in telomere biology and cancer research. It offers a noncanonical recruitment mechanism for TRIM28, independent of KRAB-ZNFs, and highlights the functional role of orphan nuclear receptors in telomeric chromatin regulation. The study has potential implications for understanding ALT regulation and for identifying new intervention points in ALT-positive cancers. The work is conceptually interesting, but the conclusions are currently limited by insufficient quantification, some interpretative ambiguities, and a few overlooked references. Addressing the concerns listed above would significantly enhance the rigor and impact of the manuscript.

Response: We appreciate the reviewer's recognition of the significance of our work in elucidating the molecular basis of ALT regulation through COUP-TF2-TRIM28-mediated heterochromatin formation. We also thank the reviewer for the valuable feedback, which has significantly strengthened our manuscript.

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Referee #2

Evidence, reproducibility and clarity

Summary

This manuscript investigates the role of orphan nuclear receptors (ORs), specifically COUP-TF2 and TR4, in promoting H3K9me3 enrichment at ALT telomeres via recruitment of TRIM28 (KAP1). The authors propose that the AF2 domain of COUP-TF2, located in its ligand-binding domain (LBD), is sufficient to recruit TRIM28 to telomeres. This, in turn, promotes heterochromatinization and induces hallmarks of the Alternative Lengthening of Telomeres (ALT) pathway, including APB formation and telomeric DNA synthesis outside of S-phase. This study addresses one important and unresolved question in the field: by what mechanism is the heterochromatic state established at ALT telomeres? Another timely question, not addressed here is: how is heterochromatin (specifically H3K9me3) functionally linked to ALT? The findings are potentially novel and mechanistically insightful. However, key elements of the study, particularly the central tethering experiments, require stronger quantification and clarity. Additional mechanistic tests and literature adjustments would also improve the manuscript.

Major Concerns

1. Central TRF1-COUP-TF2-LBD result lacks quantification and clarity: the tethering of COUP-TF2's LBD to telomeres via TRF1 is a core result of the paper. This experiment demonstrates that this domain is sufficient to induce weak H3K9me3 enrichment and ALT features (APBs and ATDS). However, the supporting ALT data are presented only in Supplementary Figures S1A and S1B, and are not quantified. These data should be quantified with appropriate statistics and moved to a main figure. Furthermore, the broader functional implication is not explored. Does this tethering induce a fully functional ALT pathway? For example, can telomerase knockout cells expressing TRF1-COUP-TF2-LBD maintain long-term proliferation? Such evidence would significantly strengthen the impact of the study.
2. Chromatin manipulation experiments lead to ambiguous conclusions: the authors propose that telomeric heterochromatin promotes ALT activity, but their own experiments (e.g., Figure 2) show that both heterochromatin-inducing (KRAB-TRF1) and euchromatin-inducing (VP64-TRF1) tethering can trigger ALT-like features. This makes it difficult to conclude that heterochromatin is specifically required. To clarify:
3. Did the authors express TRF1-VP64 in an ALT cell line? According to their model, this should suppress ALT activity.
4. More broadly, do chromatin alterations per se (regardless of direction) trigger ALT features? Clarifying these points is important for interpretation.
5. TERRA downregulation contradicts current models: while TERRA upregulation is often observed in ALT cells and is thought to contribute to replication stress and recombination at telomeres, the authors show that TRF1-KAP1 expression induces ALT features while TERRA is downregulated. This observation is not addressed in the manuscript. The authors should at least discuss this discrepancy and propose whether this reflects a cell line-specific phenomenon or a decoupling between TERRA levels and ALT induction in this context.

Minor Comments

Introduction (p. 3): The authors cite Episkopou et al. as showing increased H3K9me3 at ALT telomeres. This is incorrect; that paper suggests the opposite. The first study to clearly demonstrate H3K9me3 enrichment at ALT telomeres is Cubiles et al., 2018 and should be cited instead. Results (p. 5, first paragraph): The manuscript should cite Déjardin and Kingston, 2009 as the first to report COUP-TF2 and TR4 localization at ALT telomeres. The studies by Conomos et al., 2012 and Gaela et al., 2024 build on this prior evidence. Please also include this citation in the bibliography. Broader relevance of TRIM28-OR interaction: TRIM28 is a complex protein with roles in SUMOylation, heterochromatin formation, and transcriptional initiation/elongation regulation. The authors should explore whether similar COUP-TF2/TRIM28 interactions occur at other genomic loci. Public ChIP-seq data for COUP-TF2, TR4, and TRIM28 could be mined to investigate whether these factors co-occupy regulatory regions elsewhere in the genome, and how this relates to gene expression states.

Significance

This work contributes mechanistic insight into how heterochromatin is established at ALT telomeres-an important and timely question in telomere biology and cancer research. It offers a noncanonical recruitment mechanism for TRIM28, independent of KRAB-ZNFs, and highlights the functional role of orphan nuclear receptors in telomeric chromatin regulation. The study has potential implications for understanding ALT regulation and for identifying new intervention points in ALT-positive cancers.

The work is conceptually interesting, but the conclusions are currently limited by insufficient quantification, some interpretative ambiguities, and a few overlooked references. Addressing the concerns listed above would significantly enhance the rigor and impact of the manuscript.

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript builds upon the authors' prior findings that targeting COUP-TF2 to TRF1 induces ALT-associated phenotypes and G2-mediated synthesis in telomerase-immortalised BJT human fibroblasts. In this study, the authors show that telomere-coupled COUP-TF2 promotes H3K9me3 enrichment in these cells, and that this effect is blocked by TRIM28 depletion. Furthermore, TRIM28 depletion also suppresses the formation of ALT phenotypes in VA13 ALT cells. Given that TRIM28 has been implicated in regulating H3K9me3 deposition via SETDB1, and has been reported to co-purify with TR2 and TR4 (though not previously in the context of ALT telomeres), these findings add mechanistic depth to how heterochromatin regulators contribute to ALT activity. Overall, the manuscript's conclusions are generally supported by the presented data, but several aspects require clarification or additional experimental validation.

• The authors report a modest reduction in telomeric H3K9me3 following COUP-TF2 and TR4 depletion in U-2 OS and VA13 cells (Figure 1B). To strengthen the claim that these orphan receptors specifically regulate H3K9me3, the authors should 1) Assess additional heterochromatic histone marks (e.g., H4K20me3) at telomeres, 2) Normalize telomeric signals to both parental histone levels and input, and 3) Evaluate whether global H3K9me3 levels also decrease upon receptor depletion
• Most experiments explore chromatin changes in telomerase-positive BJT fibroblasts (Figure 2, Figure 4D). It remains unclear whether similar manipulations in ALT cells yield consistent effects, which would give a broader context for ALT phenotype induction. Are ALT phenotypes similarly induced in ALT cells? Does altered chromatin status affect telomere length or telomerase recruitment/activity? Can these pathways drive ALT phenotypes in non-immortalised cells?
• When referring to Figure 3G, the authors state that that telomeric H3K9me3 was abolished upon depleting TRIM28 from the U2OS and WI38-VA13/2RA cells. Abolished is a strong word for a 50% decrease, and this sentence should be revised. The reduction appears greater than that seen with COUP-TF2/TR4 depletion. Are the effects additive? If so, might TRIM28 act, at least in part, independently of COUP-TF2/TR4?
• VA13 cells consistently exhibit stronger effects than U-2 OS (e.g., Figures 1 and 3). This discrepancy could be linked to the high content of variant repeats in VA13 cells. The authors should assess whether variant repeat content underlies the differential response. Repeating key experiments in additional ALT lines with varied repeat compositions would be informative.
• In line with the previous point, it would be useful to show whether TRIM28 telomeric enrichment is affected by COUP-TF2/TR4 depletion in U-2 OS cells (Figure 4C). To improve confidence in these findings, the authors should perform telomeric ChIP assays, especially with the COUP-TF2^LBDΔAF2-TRF1 mutant construct.
• The immunoprecipitation experiments showing TRIM28 association with orphan receptors should include benzonase treatment to rule out DNA-mediated co-association (Figure 4F-G).
• The study would benefit from a direct assessment of whether COUP-TF2LBDΔAF2-TRF1 fails to induce ALT phenotypes in BJT fibroblasts.
• The experiments performed in Figure 5E-H lack a vector-only + siCtrl control.
• In Figure 5E, the observation that APB formation is restored in siTRIM28 + Vector-treated cells is unexpected. The authors should address this finding and clarify whether this reflects biological noise or a compensatory effect.

Significance

This work offers valuable mechanistic insight into how COUP-TF2 and TRIM28 coordinate to regulate heterochromatin deposition and ALT phenotype formation. It adds to the growing understanding of chromatin-mediated telomere regulation. What remains unclear is how important this interaction is for ALT maintenance, as H3K9me3 is only moderately altered upon TRIM28 depletion in ALT cells. Depletion of TRIM28 has been shown previously to induce APB formation and telomere elongation in U-2 OS ALT cells (Wang et al., 2021), the opposite to what the authors observed here in VA13 cells (Figure 5E-H). Clarifying whether these differences are variant repeat-dependent, or reflect intrinsic features of specific ALT cell lines, would substantially elevate the study's impact.

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Reply to the reviewers

1. General Statements

In this study, we mechanistically define a new molecular interaction linking two of the cell's major morphological regulatory pathways-the Rho GTPase and Hippo signaling networks. These two major signaling pathways are both required for life across huge swaths of the tree of life. They are required for the dynamic organization and reorganization of proteins, lipids, and genetic material that occurs in essential cellular processes such as division, motility and differentiation. For decades these pathways have been almost exclusively studied independently, however, they are known to act in concert in cancer to drive cytoskeletal remodeling and morphological changes that promote proliferation and metastasis. However, mechanistic insight into how they are coordinated is lacking.

Our data reveal a mechanistic model where coordination is mediated by the RhoA GTPase-activating protein ARHGAP18, which forms molecular interactions with both the tumor suppressor Merlin (NF2) and the transcriptional co-regulator YAP (YAP1). Using a combination of state-of-the-art super-resolution microscopy (STORM, SORA-confocal) in cultured human cells, biochemical pulldown assays with purified proteins, and analyses of tissue-derived samples, we characterize ARHGAP18's function from the molecular to the tissue level in both native and cancer model systems.

Together, these findings establish a previously unrecognized molecular connection between the RhoA and Hippo pathways and culminate in a working model that integrates our current results with prior work from our group and decades of prior studies. This model provides a new conceptual framework for understanding how RhoA and Hippo signaling are coordinated to regulate cell morphology and tumor progression in human cells.

In this substantially revised manuscript, we have addressed all comments from the expert reviewers described point-by-point below. A shared major comment from the reviewers was the request for direct evidence of the proposed mechanistic model. To address these constructive comments, we've added new experiments, new quantification, new text, new control data, and have added two expert authors, adding super-resolution mouse tissue imaging data for the endogenous study of ARHGAP18 in its native condition. We believe that these additions greatly enhance the manuscript and collectively address the overall message from the reviewer's collective comments.

2. Point-by-point description of the revisions

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

This manuscript describes a dual mechanism by which ARHGAP18 regulates the actin cytoskeleton. The authors propose that in addition to the known role for ARHGAP18 in regulating Rho GTPases, it also affects the cytoskeleton through regulation of the Hippo pathway transcriptional regulator YAP. ARHGAP18 knockout Jeg3 cells are were generated and show a clear loss of basal stress fiber like F-actin bundles. The authors further characterize the effects of ARHGAP18 knockout and overexpression. It is also discovered that ARHGAP18 binds to the Hippo pathway regulator Merlin and to YAP. Ultimately it is concluded that ARHGAP18 regulates the F-actin cytoskeleton through dual regulation of RHO GTPases and of YAP. While the phenotype of the ARHGAP18 knockout and the association of ARHGAP18 with Merlin and YAP is interesting, I found the authors conclusion that these phenotypes are due to ARHGAP18 regulation of both RHO and YAP to be based on largely correlative evidence and sometimes lacking in controls or tests for significance. In addition the authors often make overly strong conclusions based on the experimental evidence. In some instances, the rationale for how the experimental results support the conclusion is insufficiently articulated, making evaluation challenging. In general although the authors have some interesting observations, more definitive experiments with proper controls and statistical tests for significance and reproducibility are needed to justify their overall conclusions.

• *

*We appreciate the reviewers' constructive comments and have added substantial new data and quantifications to address their concerns. We have focused these new data on directly testing the proposed mechanisms, adding controls, and performing quantitative analysis with statistical testing. Additionally, we have edited our language to make our rationale clearer and to present our conclusions as a more moderate assessment of our experimental results. Below we respond to the specific comments made by the reviewer, followed by a list of additional editorial changes we've made based on the reviewer's overarching comments on clarity and rationale. *

Specific Comments

1) The authors make a big point about the effects of ARHGAP18 on myosin light chain phosphorylation. However, this result is not quantified and tested for statistical significance and reproducibility.

*We thank the reviewer for their comments on our western blotting quantification, which in the original submission version had quantification of RhoA downstream signaling of pCofilin/ Cofilin and pLIMK/ LIMK. We had withheld the pMLC and MLC quantification as the result was previously published with quantification, reproducibility, and statistical significance by our group in our prior manuscript on ARHGAP18 published in Elife in 2024 (Fig. 4E of *

https://doi.org/10.7554/eLife.83526 ). However, these prior results lacked the new overexpression data. We recognize the need to add these data to this manuscript as requested by the reviewer.

• *

*To address the reviewer's comment, we have added quantification of pMLC/MLC (Fig. 1F) *

2) Along similar lines in Figure 2C they state that overexpression of ARHGAP18 causes cells to invade over the top of their neighbors. This might be true and interesting, but only a single cell is shown and there is no quantification or controls for simply overexpressing something in that cell. The authors also conclude from this image that the overexpression phenotype is independent of its GAP activity on Rho. It is not clear how this conclusion is made based on the data. It would seem like a more definitive experiment would be to see if a similar phenotype was induced by an ARHGAP18 mutant deficient in GAP activity.

Based on the reviewer's comment, we recognize the qualitative statements made in Figure 2C (now Figure 3) should've been made more quantitative. We have added the control of Jeg 3 WT cells expressed with empty vector flag to show that WT cells do not invade over the top of each other (Fig. 3F). Additionally, we have added the quantification found in Fig. 3E, which shows the % invasive/ non-invasive cells between WT and ARHGAP18 overexpression cells. We have clarified our conclusions to make clear that these data do not directly test if the invasive phenotype derives from a Rho-independent mechanism. The text now states the following conclusion alongside others, which can be seen in our tracked changes:

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"These data support the conclusion that ARHGAP18 acts to regulate basal and junctional actin. However, it was not clear whether this activity occurred through a Rho-independent or a Rho-dependent mechanism."

• *

We have added new data of cells expressing an ARHGAP18 mutant deficient in GAP activity, which is explained in detail in the following response below.

3) In Figure 3 the authors compare gene expression profiles of ARHGAP18 knockout cells to wild-type cells. They see lots of differences in focal adhesion and cytoskeletal proteins and conclude that this supports their conclusion that ARHGAP18 is not just acting through RHO. The rationale for this in not clear. In addition, they observe changes in expression profiles consistent with changes in YAP activity. They conclude that the effects are direct. This very well might be true. However RHO is a potent regulator of YAP activity and the results seem quite consistent with ARHGAP18 acting through RHO to affect YAP.

• *

We thank the reviewer for their comment and believe the revised manuscript now presents direct evidence to support the conclusions made through the editing text and the incorporation of new data.

• *

First, the reviewer highlighted that we were not clear in our rationale and explanation of the conclusions made from our RNAseq data in the new Figure 4 (Previously Figure 3). We agree with the reviewer that the RNAseq data alone is not sufficient rationale for the conclusion that ARHGAP18 is acting through YAP directly. In the revised manuscript, the conclusion is now made based on the combination of our multi-faceted investigation of the relationship between ARHGAP18 and YAP (most importantly, new Figure 5). It's important for us to argue that our RNAseq analysis is much more robust and specific than simply reporting a descriptive assay seeing lots of differences in cytoskeletal proteins. We recruited an outside RNAseq expert collaborator; Dr. Yongho Bae, to perform state-of-the-art IPA analysis and a grueling manual curation of the top hit genes to identify the predominant signaling pathways linking the loss of ARHGAP18 to known YAP translational products. We've provided a supplemental table listing each citation supporting the identified YAP pathway associations from this manual curation. We also have added a new discussion paragraph on RNAseq data to clarify our specific RNAseq data results and analysis. In the revised manuscript, we have moderated our language in the results text regarding the RNAseq data to reflect the reviewer's suggestion:

• *

"Our RNAseq data alone could not independently confirm if the alterations to transcriptional signaling and expression of actin cytoskeleton proteins were through a Rho-dependent or Rho-independent mechanism."

• *

• *

Second, in this comment and the above, the reviewer highlights the need for a new experiment to directly test the Rho Independent effects of ARHGAP18, which we now provide in the new Figure 5. In this new data, we've applied an experimental design suggested by reviewer 2 regarding the same concern. In short, we've produced and expressed a point mutant variant ARHGAP18(R365A), which abolishes the Rho GAP activity while maintaining the remainder of the protein intact. This construct allows us to directly test the effects of ARHGAP18 independent from its RhoA GAP activity. We find that the GAP-deficient ARHGAP18 is able to fully rescue basal focal adhesions, indicating that the basal actin phenotype is at least in part regulated through a Rho-independent mechanism.

• *

• *

*We believe the revised manuscript, when taken in totality, provides the definitive proof requested by the reviewer. Specifically, the combination of Figure 5, where we show new data using the ARHGAP18(R365A) variant, and the result that ARHGAP18 forms a stable complex with YAP (Fig. 6G) or Merlin (Fig.6A), is supportive of direct Rho-independent molecular interactions between YAP, Merlin, and ARHGAP18. *

4) In Figure 4A showing Merlin binding to ARHGAP18 there is no control for the amount of Merlin sticking to the column as was done in Figure 4F for binding experiments with YAP. This makes it difficult to determine the significance of the observed binding.

We have performed the requested control experiment and added the results to Figure 6A.

5) The images in Figure 4C showing YAP being maintained in the nucleus more in ARHGAP18 knockout cells compared to wild-type. However the images only show a few cells and YAP localization can be highly variable depending on where you look in a field. Images with more cells and some sort of quantification would bolster this result.

We have provided quantification (Figure 6D) of what was originally Figure 4C (now Figure 6C).

Reviewer #1 (Significance (Required)):

While the phenotype of the ARHGAP18 knockout and the association of ARHGAP18 with Merlin and YAP is interesting, I found the authors conclusion that these phenotypes are due to ARHGAP18 regulation of both RHO and YAP to be based on largely correlative evidence and sometimes lacking in controls or tests for significance. In addition the authors often make overly strong conclusions based on the experimental evidence. In some instances, the rationale for how the experimental results support the conclusion is insufficiently articulated, making evaluation challenging. In general although the authors have some interesting observations, more definitive experiments with proper controls and statistical tests for significance and reproducibility are needed to justify their overall conclusions.

In the above comments, we detail the specific definitive experiments, proper controls, and statistical tests for significance, requested by the reviewer, which we believe greatly strengthen our manuscript.

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

This manuscript investigates the Rho effector, ARHGAP18 in Jegs cells, a trophoblastic cell line. It presents a number of new pieces of data, which increase our understanding of the importance of this GAP on cell function and explains at a molecular level previous results of other workers in the field. ARHGAP18 was originally given the name "conundrum' and continues to stand apart from the majority of other GAP proteins and their functions. Hence the data here is significant and of high standard.

The data is clear, and the images are of high quality and extremely impressive in their resolution. It is significant and adds a further layer to our understanding of the regulation of cell migration, particularly in the formation and resolution of microvilli.

• *

We appreciate the reviewer's comments and supportive insights.

The data is based on the use of the cell line Jeg3. Even the authors previous publication in eLife is based only on this cell line. They need to show the conclusions are general and not specific to this line of cells. As an extension of this, is the ARHGAP18 function shown here only in transformed cells? Does the same mechanisms operate in normal cells, which respond to activation to proliferate or migrate?

• *

• We respectfully point out that the critical experiments of the prior eLife publication were validated in DLD-1 colorectal cells and not Jeg-3 cells alone (Figure 1-figure supplement 2). Our newly independent lab, established just over a year ago, is unable to perform a full expansion of the manuscript using untransformed cells, however, we agree with the reviewer's perspective and wish to address the comment to the best of our current capability. To answer the reviewers' suggestions, we have recruited Dr. Christine Schaner Tooley, an expert in mouse model system studies. In the revised manuscript, we've added new Super-Resolution SORA confocal images of endogenous ARHGAP18's localization in the intact intestinal villi tissue, and apical junctions of WT mice (Fig.1A-C). These data indicate that endogenous ARHGAP18 is enriched (but not exclusively localized) at the apical plasma membranes of normal WT epithelial cells. This localization, where both Merlin and Ezrin are present at apical membrane/ junctions under normal conditions, is a major component of the working model proposed in Fig. 7. These data also indicate that ARHGAP18 is capable of entering the nucleus in WT cells, another critical aspect of our proposed model. Collectively, our DLD-1 studies published previously and or new studies using WT mice tissue samples support the conclusion that at least some of ARHGAP18's functions described in this manuscript are not limited to Jeg3 cells.*

In endothelial cells, Lovelace et al 2017 showed localization to microtubules and that depletion of ARHGAP18 resulted in microtubule instability. The authors may like to comment on the differences. Is this a cell type difference or RhoA versus RhoC difference?

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In our previous publication (Lombardo Elife), we validated the finding that ARHGAP18 forms a complex with microtubules, as we detected tubulin in the ARHGAP18 pulldown experiment (Figure 1- Source Data). However, our data indicate that in Jeg3 cells ARHGAP18 does not localize to the same microtubule associated spheres observed in the Lovelace publication. We now comment on the shared conclusions and differences between this manuscript and the Lovelace et al 2017 in the discussion section.

• *

"In endothelial cells, ARHGAP18 has been reported to localize microtubules and plays a role in maintaining proper microtubule stability (Lovelace et al., 2017). In our epithelial cell culture models and WT mouse intestine, we have been unable to detect ARHGAP18 at microtubules suggesting ARHGAP18 may have additional functions is various cell types."

On pages 7,9 they conclude that MLC and basal and junctional actin are regulated through a GAP independent mechanism. The best way to show this is with overexpression of a GAP mutant.

We appreciate the reviewer's insight and have produced and expressed a GAP mutant, ARHGAP18(R365A), in our cells, directly testing our conclusion that ARHGAP18 has a GAP-independent function. These data are now presented in revised Figure 5 and explained further in response to reviewer #1.

There is a huge amount of data presented in Figure 3, but their 2 genes which they focus on, LOP1 and CORO1A, are discussed but no actual data presented in support.

We now validate the CORO1A by qPCR in Figure 4J.

• *

Reviewer #2 (Significance (Required)):

The data is significant and adds a further layer to our understanding of the regulation of cell migration, particularly in the formation and resolution of microvilli. This manuscript will be of significance to an basic science audience in the field of RhoGTPases and cell migration.

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

The study by Murray et al explores the effects of ARHGAP18 on the actin cytoskeleton, Rho effector kinases, non-muscle myosin, and transcription. Using super resolution microscopy, they show that in ARHGAP18 KO cells there is a mixed and unexpected cytoskeleton phenotype where myosin phosphorylation appears to be increased, but actin is disorganised with reduced stress fibres, diminished focal adhesions and augmented invasiveness. They conclude that the underlying mechanisms are likely independent from RhoA. Next, they perform RNAseq using the KO cells and identify an array of dysregulated genes, including those that play crucial roles in microvilli (related to previously published findings). Analysis of the data identify gene expression changes that are relevant for altered focal adhesion (integrins). Further analysis reveals that a large cohort of the dysregulated genes are YAP targets. They then show that in ARHGAP18 KO cells YAP nuclear localization, as detected by immunostaining, is augmented; and demonstrate that immobilized ARHGAP18 protein can bind the Hippo regulator merlin as well as YAP itself.

Major comments:

1, The premise of the study (that ARHGAP18 is a RhoA effector or may acts independently of RhoA) remains not proven.

We have added new evidence of direct RhoA independent activity for ARHGAP18 described in the above comments. Specifically, we've added data using a RhoA-GAP dead variant of ARHGAP18 in Figure 5, which we believe addresses this comment.

• *

At several places (including in the title) the authors refer to ARHGAP18 as a Rho effector, which would suggest that it is downstream form Rho, but the basis for this is not clear. In fact, their own previous study suggested that ARHGAP is a RhoA regulator, rather than an effector. In general, the connection of the described effects to RhoA remains unclear, and not addressed in this study. The authors seem to go back and forth in their conclusions regarding the connection between ARHGAP18 and RhoA. For example, the first section of results is finished by stating (line 194): "These data support the conclusion that ARHGAP18 acts to regulate basal and junctional actin through Rho-independent mechanism". But the next section starts by stating (line 198): "We hypothesized that the invasive and cytoskeletal phenotypes observed at the basal surface of cells devoid of ARHGAP18 may be a result of changes in regulation at the transcriptional level either directly through RhoA signaling or through an additional mechanism specific to ARHGAP18". The paper would be strengthened by adding data that show whether the effects are indeed downstream, from RhoA or RhoA independent. If there is no sufficient demonstration that ARHGAP18 is downstream of RhoA and is an effector, this needs to be stated explicitly, and the wording should be changed.

*We now provide new data in Figure 5, which directly tests the RhoA independent functions of ARHGAP18 as recommended by the reviewer. Our understanding of the term effector is 'a molecule that activates, controls, or inactivates a process or action.' Based on this understanding, we used the term to convey ARHGAP18's functional role within the feedback loop, rather than to imply that it acts exclusively downstream. *

• *

We seek to clarify our perspective with the reviewer's assertion that we go "back and forth" as to if ARHGAP18 functions in a Rho Dependent or Rho Independent manner. It was our intent to propose a model where ARHGAP 18 acts in two separate circuits that regulate cell signaling. The first circuit involves ARHGAP18's canonical RhoA GAP activity, which involves ERMs and LOK/SLK, and is limited to the apical plasma membrane. This first signaling circuit was characterized in our prior Elife manuscript (Lombardo et al., 2024) and in an earlier JCB manuscript (Zaman and Lombardo et al., 2021). In this newly revised manuscript, we provide a partial mechanistic characterization of the second circuit, which we freely admit is much more complex and will likely require additional study to fully characterize.

• *

As both circuits operate as signaling feedback loops, we find the terms 'upstream' and 'downstream' to be of limited value, and we attempt to avoid their use when possible. We retain their use only when referring to the Hippo and ROCK signaling cascades, where these designations are well established. We suggest that the conceptual inconsistencies of Conundrum/ARHGAP18 may have arisen from the tendency to view it in strictly binary terms as upstream or downstream. Here, we propose a third possibility that ARHGAP18 functions as both, participating in a negative feedback loop.

• *

*We have edited and added data testing if the effects are Rho independent and discussion text in response to the reviewer's comments and clarify the molecular function of ARHGAP18.

"Additionally, focal adhesions and basal actin bundles are restored to WT levels when the ARHGAP18(R365A) GAP-ablated mutant is expressed in ARHGAP18 KO cells (Fig. 5A, B). These results represent the strongest argument that ARHGAP18 functions in additional pathways to RhoA/C alone. Our data suggests that at least one of the alternative pathways is through ARHGAP18's interaction with YAP and Merlin. From these data we conclude that ARHGAP18 has important functions in both RhoA signaling through both its GAP activity and in Hippo signaling through its GAP independent binding partners. "*

• *

• *

The study is descriptive and contains a series of observations that are not connected. Because of this, the study's conclusions are not well supported, and key mechanistic insight is limited. The study feels like a set of separate observations, that remain incompletely worked out and have some preliminary feel to them. The model in the last figure also seems to contain hypotheses based on the observations, several of which remains to be proven.

• *

*We present our revised manuscript, in which we've more clearly outlined our rationale and conclusions, as detailed in the above responses, to emphasize the overall connectivity of the study. We have also updated the title of Figure 7 to read "__Theoretical __Model of ARHGAP18's coordination of RhoA and Hippo signaling pathways in Human epithelial cells." To make it clear that we are presenting a working model, which has elements that will require additional investigation. Throughout the manuscript, we highlight the unknown elements that remain to be tested or other outstanding questions. Thus, we do not aim to characterize this complex signaling coordination completely. Instead, this manuscript represents the 3rd iteration in our systematic advances to describe this entirely new signaling pathway. We agree that, despite three separate manuscripts (this one included) to date, this work represents an early stage in understanding the system, many additional studies will be needed to characterize this signaling system fully. Figure 7 is presented as a working model that results from a thoughtful combination of our collective data and that of other researchers, derived from numerous species across decades of study. We firmly believe that proposing such integrative models is valuable for advancing the field. We also recognize the importance of clearly indicating which aspects remain hypothetical. We now explicitly note in several places within the discussion which components of the model will require further validation and experimental confirmation. For example, regarding our theoretical mechanism in Figure 7 we state: *

"Validation of the direct mechanism by which YAP/TAZ transcriptional changes drive basal actin changes in ARHGAP18 KO cells will require further investigation based on predictions from RNAseq results."

• *

Addressing any possible connection between key effects of ARHGAP18 KO (changes in actin, focal adhesion, integrins, Yap and merlin binding) could strengthen the manuscript. One such specific question is the whether the changes in integrin expression (RNAseq) are indeed connected to the actin alterations and reduction ion focal adhesions (Fig 1). Staining for these integrins to show they are indeed altered, and/or manipulating any of them to reproduce changes could provide and exciting addition.

• *

*We attempted to stain cells for Integrins by purchasing three separate antibodies. However, despite extensive optimization and careful selection of the specific integrins using our RNAseq results we were unable to get any of these antibodies to work in any cell type or condition. We believe that there is a technical challenge to staining for integrins due to their transmembrane and extracellular components, which we were unable to overcome. As an attempt to address the reviewers comment, we alternatively stained cells for paxillin which directly binds the cytoplasmic tails of integrins (Fig. 3&5). *

Some of the experimental findings are not convincing or lack controls. Fig 1: some of the western blots are not convincing or poor quality. [...] On the same figure, the quality of LIM kinase blots is poor. [...] The signal is weak, and the blot does not appear to support the quantification. The last condition (expression of flag-ARHGAP18) results in a large drop in pLIMK and pcofilin on the blot, which is not reflected by the graph. Addition of *a better blot and the use of strong positive or negative control would boost confidence in these data. *

• *

In response to this and other reviewers' comments, we have added new western data and quantification to Figure 1. We now focus on MLC/pMLC data as we believe these data highlight the potential Rho-independent mechanism of ARHGAP18, and we were able to greatly improve the quality of the blots through careful optimization. We hope the reviewer finds these blots and quantifications (Fig. 1E and F) more convincing.

*We note that phospho-specific Western blotting presents considerably greater technical challenges than conventional blotting. We believe that the appearance of an attractive looking blot does not always correlate to quality or reproducibility and have focused on taking extraordinarily careful steps in the blotting of our phospho-specific antibodies, which at times comes at the cost of the blot's attractiveness in appearance. For example, all phospho-specific antibodies are run using two color fluorescent markers to blot against both the total protein and the phospho-protein on the same blot. This approach often leads to blots that have reduced signal to noise compared to chemiluminescent Westerns. Additionally, we use phospho-specific blocking buffer reagents which do not contain phosphate-based buffers or agents that attract non-specific phospho-staining signals. These blocking buffers are not as effective as non-fat milk in pbs at blocking the background signal, however, they are ultimately cleaner for phospho-specific primary antibodies. We use carefully optimized protocols, from cell treatment to lysis, transfer, and antibody incubation, including methods developed by laboratories where the corresponding author of the manuscript was trained. Nonetheless, despite these efforts, we have now removed the LIMK and cofilin data because we deemed them unnecessary for the main conclusions of this manuscript and were unable to improve their quality to satisfy the reviewer. *

The changes in pMLC on the western blots are very small, and for any conclusion, these studies require quantification. Further, the expression levels of Flag-ARHGAP18 needs to be shown to support the statement that the protein is expressed, and indeed overexpressed under these conditions (vs just re-expressed).

In continuation of the above comment, we have made significant effort to improve the quality of our pMLC western blots and now provide quantification in Figure 1. We also now provide the Flag-ARHGAP18 signal as requested by the reviewer.

Fig 4: the differences in YAP nuclear localization under the various conditions are not well visible. Quantitation of nuclear/cytosolic signal ratio should be provided. Please provide a rationale and more context for using serum starvation and re-addition. What is the expected effect? Serum removal and addition is referred to as nutrient removal and re-addition, but this is inaccurate, as it does not equal nutrient removal, since serum contains a variety of other important components, e.g. growth factors too.

We have provided new quantification of the nuclear/cytosolic signal ratio in Figure 6D. We have explained our rational for the study through the following new text:

"Merlin is activated and localized to junctions upon signaling, promoting growth and proliferation; among these signals is the availability of growth factors and other components of serum (Bretscher et al., 2002). We hypothesized that since ARHGAP18 formed a complex with Merlin that ARHGAP18's localization may localize to junctions under conditions which promote Merlin activation."

• *

We have altered our use of "nutrient removal" to "serum removal"

The binding between ARHGAP18 and merlin is interesting, but a key limitation is the use of expressed proteins. Can the binding be shown for the endogenous proteins (IP, colocalization). Another important unaddressed question is the relevance of this binding, and the relation of this to altered YAP nuclear localization.

• *

*Our data in Fig. 6G shows binding of a resin bound human ARHGAP18 to endogenous YAP from human cells as suggested by the reviewer. In Fig. 6A, we have selected to use GFP-Merlin as Merlin shares approximately 60% sequence identity with Ezrin, Radixin, and Moesin (ERMs). Their similarity is such that Merlin was named for Moesin-Ezrin-Radixin-Like Protein. In our experience, nearly all Merlin or ERM antibodies have some cross-contaminating signal. Thus, a major concern is that if we were to blot for endogenous Merlin in the pull-down experiment, we may see a band that could in fact be ERMs. To avoid this, we tagged Merlin with GFP to ensure that the product pulled down by ARHGAP18 was Merlin, not an ERM. Regarding the ARHGAP18-resin bound column, our homemade ARHGAP18 antibody is polyclonal. We have extensive experience in pulldown assays and have found that the binding of a polyclonal antibody to the bait protein can produce less accurate results, as the binding site for the antibody is unknown and can sterically hinder attachment of target proteins like Merlin. In our experience, attachment to a flag-tag, which is expressed after a flexible linker at the N- or C-terminus, allows us to overcome this limitation, which we've used in this manuscript. *

Minor comments:

Introduction line 99: "When localized to the nucleus, YAP/TAZ promotes the activation of cytoskeletal transcription factors associated with cell proliferation and actin polymerization" Please clarify what you mean by this statement, that is inaccurate in its present for. Did you mean effects on transcription factors that control cytoskeletal proteins, or do you mean that Yap/Taz affect these proteins? Please also provide reference for this.

We've altered the sentence as suggested by the reviewer, which now reads the following:

"When localized to the nucleus, YAP/TAZ promotes transcriptional changes associated with cell proliferation and actin polymerization."

• *

*The full mechanism for how YAP/TAZ promotes proliferation and actin polymerization is a currently debated issue. We do not think introducing the various current proposed models is required for this manuscript, and we simply intend to convey that when in the nucleus, YAP/TAZ promotes transcriptional changes that drive actin polymerization and cell proliferation. *

-What is the cell confluence in these experiments? For epithelial cells confluence affects actin structure. Please comment on similarity of confluency across experimental conditions?

• *

All cellular experiments are paired where WT and ARHGAP18 KO cells are plated at the same time under identical conditions. For imaging, we plate all cells onto glass coverslips in a 6 well dish so that each condition is literally in the same cell culture plate and gets identical treatment. In our prior Elife paper studying ARHGAP18, we characterized that ARHGAP18 KO cells and WT cells divide at a similar rate and have similar proliferation characteristics. The epithelial cell cultures are maintained for experiments around 70-80% confluency. For the focal adhesion staining experiments, the confluency is slightly lower, between 50-60% to capture the focal adhesions towards the leading edge. We have added the following new text to further describe these methods: "Cell cultures for experiments were maintained at 70%-80% confluency. For focal adhesion experiments, the cell cultures were maintained at 50%-60% confluency."

-Fig 2 legend: please indicate that the protein detected was non-muscle myosin heavy chain (distinct from the light chain detected in Fig 1).

• *

We have altered original Figure 2 (new Figure 3) legend.

-Line 339-340: please check the syntax of this sentence -Western blot quantification: the comparison of experiments with samples run on different gels/blots requires careful normalization and experimental consistency. Please describe how this was achieved.

• *

We have added the following new text to further describe these methods:

"For blots which required quantification of antibodies that were only rabbit primaries (e.g., pMLC/MLC antibodies listed above), samples were loaded onto a single gel and transferred onto a single membrane at the same time. After transfer, the membrane was cut in half and subsequent steps were done in parallel. All quantified blots were checked for equal loading using either anti-tubulin as a housekeeping protein or total protein as detected by Coomassie staining"

Reviewer #3 (Significance (Required)):

Rho signalling is a central regulator of an array of normal and pathological cell functions, and our understanding of the context dependent regulation of this key pathway remains very incomplete. Therefore, new knowledge on the role of specific regulators, such as ARHGAP18, is of interest to a very broad range of researchers. A further exciting aspect of this protein, that despite indications by many studies that it acts as a GAP (inhibitor) for Rho proteins, there are findings in the literature that suggest that its manipulation can affect actin in unexpected (opposite) manner. These point to possible Rho-independent roles, and warranted further in-depth exploration.

One of the strength of the study is that it explores possible roles of ARHGAP18 beyond RhoA and describes some new and interesting observations, which advance our knowledge. The authors use some excellent tools (e.g. ARHGAP KO cells and re-expression) and approaches (e.g. super resolution microscopy to analyze actin changes, RNAseq and bioinformatics to find genes that may be downstream from ARHGAP18). A key limitation of the study however, is that it is not clear whether the observed findings are indeed independent from RhoA. Further limitation is that potential causal relationships between the described findings are not studied, and therefore the findings are in some cases overinterpreted, and limited mechanistic insights are provided. In some cases the exclusive use of expressed proteins is also a limitation. Finally, some of the experiments also need improvement.

Reviewer expertise: RhoA signalling, guanine nucleotide exchange factors, epithelial biology, cell migration, intercellular junctions.

In the above comments, we detail the new experimental data addressing reviewer 3's listed key limitations. We've added new data using the Rho GAP deficient ARHGAP18(R365A) variant which allows for the direct characterization of ARHGAP18's Rho independent activity. We have introduced new data in WT cells studying endogenous proteins to address the limitations from expressed proteins. Finally, we have moderated our language to address overinterpretation. Collectively, we believe that our revised manuscript addresses the constructive reviewer's comments.

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Referee #3

Evidence, reproducibility and clarity

The study by Murray et al explores the effects of ARHGAP18 on the actin cytoskeleton, Rho effector kinases, non-muscle myosin, and transcription. Using super resolution microscopy, they show that in ARHGAP18 KO cells there is a mixed and unexpected cytoskeleton phenotype where myosin phosphorylation appears to be increased, but actin is disorganised with reduced stress fibres, diminished focal adhesions and augmented invasiveness. They conclude that the underlying mechanisms are likely independent from RhoA. Next, they perform RNAseq using the KO cells and identify an array of dysregulated genes, including those that play crucial roles in microvilli (related to previously published findings). Analysis of the data identify gene expression changes that are relevant for altered focal adhesion (integrins). Further analysis reveals that a large cohort of the dysregulated genes are YAP targets. They then show that in ARHGAP18 KO cells YAP nuclear localization, as detected by immunostaining, is augmented; and demonstrate that immobilized ARHGAP18 protein can bind the Hippo regulator merlin as well as YAP itself.

Major comments:

1. The premise of the study (that ARHGAP18 is a RhoA effector or may acts independently of RhoA) remains not proven. At several places (including in the title) the authors refer to ARHGAP18 as a Rho effector, which would suggest that it is downstream form Rho, but the basis for this is not clear. In fact, their own previous study suggested that ARHGAP is a RhoA regulator, rather than an effector. In general, the connection of the described effects to RhoA remains unclear, and not addressed in this study. The authors seem to go back and forth in their conclusions regarding the connection between ARHGAP18 and RhoA. For example, the first section of results is finished by stating (line 194): "These data support the conclusion that ARHGAP18 acts to regulate basal and junctional actin through Rho-independent mechanism". But the next section starts by stating (line 198): "We hypothesized that the invasive and cytoskeletal phenotypes observed at the basal surface of cells devoid of ARHGAP18 may be a result of changes in regulation at the transcriptional level either directly through RhoA signaling or through an additional mechanism specific to ARHGAP18". The paper would be strengthened by adding data that show whether the effects are indeed downstream, from RhoA or RhoA independent. If there is no sufficient demonstration that ARHGAP18 is downstream of RhoA and is an effector, this needs to be stated explicitly and the wording should be changed.
2. The study is descriptive and contains a series of observations that are not connected. Because of this, the study's conclusions are not well supported, and key mechanistic insight is limited. The study feels like a set of separate observations, that remain incompletely worked out and have some preliminary feel to them. The model in the last figure also seems to contain hypotheses based on the observations, several of which remains to be proven. Addressing any possible connection between key effects of ARHGAP18 KO (changes in actin, focal adhesion, integrins, Yap and merlin binding) could strengthen the manuscript. One such specific question is the whether the changes in integrin expression (RNAseq) are indeed connected to the actin alterations and reduction ion focal adhesions (Fig 1). Staining for these integrins to show they are indeed altered, and/or manipulating any of them to reproduce changes could provide and exciting addition.
3. Some of the experimental findings are not convincing or lack controls.

Fig 1: some of the western blots are not convincing or poor quality. The changes in pMLC on the western blots are very small, and for any conclusion, these studies require quantification. Further, the expression levels of Flag-ARHGAP18 needs to be shown to support the statement that the protein is expressed, and indeed overexpressed under these conditions (vs just re-expressed). On the same figure, the quality of LIM kinase blots is poor. The signal is weak, and the blot does not appear to support the quantification. The last condition (expression of flag-ARHGAP18) results in a large drop in pLIMK and pcofilin on the blot, which is not reflected by the graph. Addition of a better blot and the use of a strong positive or negative control would boost confidence in these data.

Fig 4: the differences in YAP nuclear localization under the various conditions are not well visible. Quantitation of nuclear/cytosolic signal ratio should be provided. 4. Please provide a rationale and more context for using serum starvation and re-addition. What is the expected effect? Serum removal and addition is referred to as nutrient removal and re-addition, but this is inaccurate, as it does not equal nutrient removal, since serum contains a variety of other important components, e.g. growth factors too. 5. The binding between ARHGAP18 and merlin is interesting, but a key limitation is the use of expressed proteins. Can the binding be shown for the endogenous proteins (IP, colocalization). Another important unaddressed question is the relevance of this binding, and the relation of this to altered YAP nuclear localization.

Minor comments:

• Introduction line 99: "When localized to the nucleus, YAP/TAZ promotes the activation of cytoskeletal transcription factors associated with cell proliferation and actin polymerization" Please clarify what you mean by this statement, that is inaccurate in its present for. Did you mean effects on transcription factors that control cytoskeletal proteins, or do you mean that Yap/Taz affect these proteins? Please also provide reference for this.
• What is the cell confluence in these experiments? For epithelial cells confluence affects actin structure. Please comment on similarity of confluency across experimental conditions?
• Fig 2 legend: please indicate that the protein detected was non-muscle myosin heavy chain (distinct from the light chain detected in Fig 1).
• Line 339-340: please check the syntax of this sentence
• Western blot quantification: the comparison of experiments with samples run on different gels/blots requires careful normalization and experimental consistency. Please describe how this was achieved.

Significance

Rho signalling is a central regulator of an array of normal and pathological cell functions, and our understanding of the context dependent regulation of this key pathway remains very incomplete. Therefore, new knowledge on the role of specific regulators, such as ARHGAP18, is of interest to a very broad range of researchers. A further exciting aspect of this protein, that despite indications by many studies that it acts as a GAP (inhibitor) for Rho proteins, there are findings in the literature that suggest that its manipulation can affect actin in unexpected (opposite) manner. These point to possible Rho-independent roles, and warranted further in-depth exploration. One of the strength of the study is that it explores possible roles of ARHGAP18 beyond RhoA and describes some new and interesting observations, which advance our knowledge. The authors use some excellent tools (e.g. ARHGAP KO cells and re-expression) and approaches (e.g. super resolution microscopy to analyze actin changes, RNAseq and bioinformatics to find genes that may be downstream from ARHGAP18). A key limitation of the study however, is that it is not clear whether the observed findings are indeed independent from RhoA. Further limitation is that potential causal relationships between the described findings are not studied, and therefore the findings are in some cases overinterpreted, and limited mechanistic insights are provided. In some cases the exclusive use of expressed proteins is also a limitation. Finally, some of the experiments also need improvement.<br /> Reviewer expertise: RhoA signalling, guanine nucleotide exchange factors, epithelial biology, cell migration, intercellular junctions.

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Referee #2

Evidence, reproducibility and clarity

This manuscript investigates the Rho effector, ARHGAP18 in Jegs cells, a trophoblastic cell line. It presents a number of new pieces of data, which increase our understanding of the importance of this GAP on cell function and explains at a molecular level previous results of other workers in the field. ARHGAP18 was originally given the name "conundrum' and continues to stand apart from the majority of other GAP proteins and their functions. Hence the data here is significant and of high standard.

The data is clear, and the images are of high quality and extremely impressive in their resolution. It is significant and adds a further layer to our understanding of the regulation of cell migration, particularly in the formation and resolution of microvilli.

The data is based on the use of the cell line Jeg3. Even the authors previous publication in eLife is based only on this cell line. They need to show the conclusions are general and not specific to this line of cells. As an extension of this, is the ARHGAP18 function shown here only in transformed cells? Does the same mechanisms operate in normal cells, which respond to activation to proliferate or migrate? In endothelial cells, Lovelace et al 2017 showed localisation to microtubules and that depletion of ARHGAP18 resulted in microtubule instability. The authors may like to comment on the differences. Is this a cell type difference or RhoA versus RhoC difference?

On pages 7,9 they conclude that MLC and basal and junctional actin are regulated through a GAP independent mechanism. The best way to show this is with overexpression of a GAP mutant.

There is a huge amount of data presented in Figure 3, but their 2 genes which they focus on, LOP1 and CORO1A, are discussed but no actual data presented in support.

Significance

The data is significant and adds a further layer to our understanding of the regulation of cell migration, particularly in the formation and resolution of microvilli.

This manuscript will be of significance to an basic science audience in the field of RhoGTPases and cell migration.

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Referee #1

Evidence, reproducibility and clarity

This manuscript describes a dual mechanism by which ARHGAP18 regulates the actin cytoskeleton. The authors propose that in addition to the known role for ARHGAP18 in regulating Rho GTPases, it also affects the cytoskeleton through regulation of the Hippo pathway transcriptional regulator YAP. ARHGAP18 knockout Jeg3 cells are were generated and show a clear loss of basal stress fiber like F-actin bundles. The authors further characterize the effects of ARHGAP18 knockout and overexpression. It is also discovered that ARHGAP18 binds to the Hippo pathway regulator Merlin and to YAP. Ultimately it is concluded that ARHGAP18 regulates the F-actin cytoskeleton through dual regulation of RHO GTPases and of YAP. While the phenotype of the ARHGAP18 knockout and the association of ARHGAP18 with Merlin and YAP is interesting, I found the authors conclusion that these phenotypes are due to ARHGAP18 regulation of both RHO and YAP to be based on largely correlative evidence and sometimes lacking in controls or tests for significance. In addition the authors often make overly strong conclusions based on the experimental evidence. In some instances, the rationale for how the experimental results support the conclusion is insufficiently articulated, making evaluation challenging. In general although the authors have some interesting observations, more definitive experiments with proper controls and statistical tests for significance and reproducibility are needed to justify their overall conclusions.

Specific Comments

1) The authors make a big point about the effects of ARHGAP18 on myosin light chain phosphorylation. However this result is not quantified and tested for statistical significance and reproducibility.

2) Along similar lines in Figure 2C they state that overexpression of ARHGAP18 causes cells to invade over the top of their neighbors. This might be true and interesting, but only a single cell is shown and there is no quantification or controls for simply overexpressing something in that cell. The authors also conclude from this image that the overexpression phenotype is independent of its GAP activity on Rho. It is not clear how this conclusion is made based on the data. It would seem like a more definitive experiment would be to see if a similar phenotype was induced by an ARHGAP18 mutant deficient in GAP activity.

3) In Figure 3 the authors compare gene expression profiles of ARHGAP18 knockout cells to wild-type cells. They see lots of differences in focal adhesion and cytoskeletal proteins and conclude that this supports their conclusion that ARHGAP18 is not just acting through RHO. The rationale for this in not clear. In addition, they observe changes in expression profiles consistent with changes in YAP activity. They conclude that the effects are direct. This very well might be true. However RHO is a potent regulator of YAP activity and the results seem quite consistent with ARHGAP18 acting through RHO to affect YAP.

4) In Figure 4A showing Merlin binding to ARHGAP18 there is no control for the amount of Merlin sticking to the column as was done in Figure 4F for binding experiments with YAP. This makes it difficult to determine the significance of the observed binding.

5) The images in Figure 4C showing YAP being maintained in the nucleus more in ARHGAP18 knockout cells compared to wild-type. However the images only show a few cells and YAP localization can be highly variable depending on where you look in a field. Images with more cells and some sort of quantification would bolster this result.

Significance

While the phenotype of the ARHGAP18 knockout and the association of ARHGAP18 with Merlin and YAP is interesting, I found the authors conclusion that these phenotypes are due to ARHGAP18 regulation of both RHO and YAP to be based on largely correlative evidence and sometimes lacking in controls or tests for significance. In addition the authors often make overly strong conclusions based on the experimental evidence. In some instances, the rationale for how the experimental results support the conclusion is insufficiently articulated, making evaluation challenging. In general although the authors have some interesting observations, more definitive experiments with proper controls and statistical tests for significance and reproducibility are needed to justify their overall conclusions.

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Reply to the reviewers

Dear editor and reviewers,

We sincerely thank you for your thoughtful comments and constructive suggestions, which have greatly improved the quality and clarity of our manuscript. In response, we have implemented all requested changes, which are highlighted in yellow throughout the revised text, and updated several figures accordingly. Furthermore, we have performed all additional experiments recommended by the reviewers and incorporated the new data into the manuscript. To enhance clarity, we have also included a schematic representation of our proposed model in an additional figure, providing a concise visual summary of our findings.

We hope that these revisions fully address all concerns raised by the reviewers and meet all the expectations for publication.

Below, we answer the reviewers point by point (in blue).

---

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

In this paper, the authors address the important question of the role of centrosomes during neuronal development. They use Drosophila as an in vivo model. The field is somewhat unclear on the role and importance of centrosomes during neuronal development, although the current data would suggest they are dispensable for axon specification and growth. Early studies in cultured mammalian neurons showed that centrosomes are active and that their microtubules can be cut and transported into the neurites. But a study then showed that centrosomes in these cultured neurons are deactivated relatively early during neuronal development in vitro and that ablating centrosomes even when they are active had no obvious effect on axon specification and growth. Consistent with this, a study in Drosophila provided evidence that centrosomes were not active or necessary in different types of neurons. More recently, a study showed that centrosomal microtubules are dispensable for axon specification and growth in mice in vivo but are required for neuronal migration in the cerebral cortex. However, another study has linked the generation of acetylated microtubules at centrosomes with axon development. In this current study, the authors examine the effect of centrosome loss on various motor and sensory neurons and muscles mainly by examining mutants in essential centriole duplication genes. They associate axonal routing and morphology defects with centrosome loss and provide some evidence that centrosomes could still be active in the developing neurons. Overall, they conclude that centrosomes are active during at least early neuronal development and that this activity is important for proper axonal morphology and routing.

While I think this study addressing a very interesting and important question, I think as it stands the data is not sufficient to be conclusive on a role for centrosomes during neuronal development. My biggest concern is that most phenotypes have not yet been shown to be cell autonomous, as whole animal mutants have been analysed rather than analysing the effect of cell-specific depletion, and the evidence for active centrosomes needs to be strengthened. If the authors can provide stronger evidence for a role of centrosomes in axonal development then the paper will certainly be of interest to a broad readership.

We thank the reviewer for the clear and concise summary and fully agree that our study addresses a critical gap in understanding. Centrosomes have long been implicated in morphogenesis, yet their precise contribution to nervous system development has remained unclear. Our findings provide compelling evidence that centrosomes are indispensable for proper nervous system formation and that their absence also triggers muscular defects, highlighting their broader role in tissue organization.

We acknowledge that the original manuscript lacked some key details; therefore, we have now strengthened our conclusions with additional experiments. Specifically, we demonstrate that these effects are cell-autonomous by using two independent RNAi lines targeted to a subset of motor neurons. Furthermore, we present new data showing that neuronal centrosomes remain active during the early stages of axonal development, emphasising their functional relevance in morphogenesis. All new experiments, figures, and corresponding text revisions are detailed below.

Major comments 1) The sas-6 transallelic combination shows only 17% embryonic lethality compared to 50% embryonic lethality with sas-4 mutants. Given that both mutants should result in the same degree of centrosome loss (this should be quantified in sas-6 mutants) it would suggest that either sas-4 has other roles away from centrosomes or that the sas-4 mutant chromosome used in the experiment has other mutations that affect viability. The effect of picking up "second-site lethal" mutations on mutant chromosomes is common and so I would not be surprised if this is the reason for the difference in phenotypes. This can be addressed either by "cleaning up" the sas-4 mutant chromosome by backcrossing to wild-type lines, allowing recombination to occur and replace the potential second site mutations, or by using transallelic combinations of sas-4, as they did for sas-6. The "easier" option may just be to analyse all the phenotypes with the sas-6 transallelic combination.

We appreciate this comment, as it brought to light an issue with the CRISPR line Sas-6-Δa. Upon reanalysing all the data, we determined that this line is embryonic lethal both in homozygosis and when combined with the deficiency uncovering the genomic region, Df(3R)BSC794. In contrast, Sas-6-Δb homozygotes are viable. The inconsistency between these results raised concerns about whether the Δa and Δb Sas-6 mutants carry deletions confined to the Sas-6 coding region. Although this would not hinder our cell biology analysis, it could represent a problem in viability tests. To address this, we repeated all analyses using Sas-6-Δb homozygotes and Sas-6-Δb combined with Df(3R)BSC794. These new results are more consistent and indicate that approximately 50% of Sas-6/Def individuals hatch as adults. Fig. 3 was redone and the manuscript text changed in view of these results.

2) Using "whole animal" mutants for assessing neuronal morphology is risky due to non-cell-autonomous effects. The authors have carried out some phenotypic analysis of neurons depleted of Sas-4 by cell-specific RNAi, but I feel they need to do this for all of their analysis. This includes embryonic lethality measures, quantification of centrosome numbers, and all axonal phenotypes in Sas-4 RNAi neurons. It would also be prudent to use 2 distinct RNAi lines to help ensure any phenotypes are not off-target effects (and this may help clarify why the authors see some additional phenotypes with RNAi). Indeed, there are relatively weak phenotypes in muscles when using RNAi compared to the mutants and these potential non-cell-autonomous effects could then have a knock-on effect on neuronal morphology. If the authors were concerned that RNAi is not very efficient (explaining any potential weaker phenotypes than in mutants) the authors could examine the effectiveness of RNAi lines by analysing protein depletion by western blotting or mRNA depletion by rt-qPCR (although this has to be done in a different cell type due to the difficulty in obtaining a neuronal extract).

We have now added a new panel to supplementary Figure 1, showing how the expression of a different Sas-4 RNAi line (2) induces similar nervous system phenotypes when expressed only in aCC, pCC and RP2 pioneer neurons (Sup. Fig. 1 M-O).

3) When analysing centriole presence or absence it is a good idea to stain with two different centriole markers e.g. Asl and Plp. This helps rule out unspecific staining. It is clear from the images that similar sized foci can be observed outside of the cells (see Figure 5A for example), so clearly some of the foci that appear to be within the cells may also be unspecific staining.

In a new supplementary figure, we now show that Asl and Plp colocalize and quantify the number of times we find this colocalization in neurons (Supl. Fig 3). In addition, and we apologise for the confusion, but the reason why there are foci outside the marked cells is because these are wholemount embryonic stainings and the anti-Plp antibody marks all centrosomes in all cells in the embryo.

4) The evidence for active centrosomes is not that convincing. Acetylated tubulin is associated with stable MTs, which are not normally organised by "active" centrosomes that nucleate dynamic microtubules. Moreover, it is plausible that centriole foci happen to overlap with the acetylated tubulin staining by chance. This would explain why not all centrosomes colocalise with acetylated tubulin signal. The authors could better test centrosome activity by performing live imaging with EB1-GFP. If centrosomes are active, it is very easy to observe the many comets produced by the centrosomes.

We appreciate the reviewer’s comment and agree that acetylated tubulin alone is not an ideal marker for centrosome activity. To address this, we performed live imaging of aCC neurons expressing EB1-GFP together with Asl-Tomato. This was technically challenging because we were imaging only two neurons per segment in live embryos, under significant limitations in fluorescence detection and timing. Despite these constraints, we were able to clearly observe EB1 comets emerging from the centrosome and moving toward the cell periphery, providing direct evidence of microtubule nucleation from centrosomes in neurons.

Importantly, we complemented this with a microtubule depolymerization/polymerization assay, which provides unequivocal evidence that polymerization initiates at the centrosome. After depolymerization, we observed microtubule regrowth from the centrosome, confirming its role as an active microtubule-organizing centre in these neurons. Together, we hope that these results are enough to demonstrate that neuronal centrosomes are functionally active during early axonal development. These experiments are presented in Figure 6 and corresponding text in the manuscript.

5) If the authors believe that centrosomes have a role in axon pathfinding in sensory neurons, they should show that these centrosomes are active, at least during early stages (again using EB1-GFP imaging).

We appreciate the reviewer’s suggestion and agree that EB1-GFP imaging would be the most direct way to assess centrosome activity in sensory neurons. However, performing time-lapse imaging in these neurons is technically very demanding due to their location and accessibility in live embryos, and we did not attempt this approach. Instead, we now provide new evidence showing that sensory neuron centrosomes colocalize with both α-tubulin and γ-tubulin. This strongly supports that these centrosomes are associated with microtubule nucleation machinery and are as likely as motor neuron centrosomes to be active during early stages of axon development. These new data have been included in the revised manuscript (see Figure 5 and corresponding text).

6) The authors mention in the discussion that "increased JNK activity, can result in axonal wiggliness (Karkali et al, 2023)". I therefore wonder whether centrosome loss may induce JNK activation (the stress response), as this would then indicate an indirect effect of centrosome loss on axonal structure rather than a direct influence of centrosome-generated microtubules. The authors could assess whether the DNK-JNK pathway is activated in neurons lacking centrosomes by expression UAS-Puc-GFP and quantifying the nuclear signal.

In a new supplementary figure, we now show by using a reporter for JNK signalling, as requested, that Sas-4 neurons do not activate the JNK pathway (Supl. Fig 4).

7) In Figure 5, the authors claim that they find "a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". I don't think this is a strong correlation. The difference in centriole number between embryos with no defects and those with defects is very small. In contrast, the difference between centriole numbers in control (no defects) and mutant (no defects) is very large. So, there does not appear to be a strong correlation between centrosome number and phenotype.

We agree and we have corrected this sentence to better explain the results.

Minor comments

1) I don't understand Figure 3C - why do the % of surviving homozygotes and heterozygotes add up to 100%? Should the grey boxes not relate to dead and the white to surviving?

Thank you for pointing this out. Figures 1B and 3C represent only the surviving individuals. The grey boxes correspond to surviving homozygotes, and the white boxes correspond to surviving heterozygotes. The percentages add up to 100% only at embryonic stages because all embryos reach late embryonic stages. The grey and white boxes reflect the proportion of these two genotypes among the survivors, not the total number of embryos including those that died. We have changed the text to convey this.

2) "In mouse fibroblasts, myoblasts and endothelial cells, centrosome orientation is important for nuclear positioning and cell migration(Chang et al, 2015; Gomes et al, 2005; Kushner et al, 2014)." Do you mean "centrosome position"?

Yes, text changed, thank you for spotting it.

3) In the introduction, the authors mention Meka et al. when saying the centrosomal microtubules are important for axonal development, but they should also discuss the counter argument from Vinopal et al., 2023 (Neuron) that showed how centrosomes were required for neuronal migration but not axon growth, which was instead mediated by Golgi-derived microtubules.

Done, thank you very much.

4) Lines 228-230 - repeated sentence

Corrected, thank you very much.

5) Additionally, we did not detect centrioles in the quadrant opposite the axon exit point (Fig. 2B n=75) - this data is not in Fig 2B

Correct, it is in figure 4B, thank you very much.

6) "This significant decrease in the humber of centrioles further supports the critical role of Sas-4 in pioneer neurons of the ventral nerve cord (VNC) during Drosophila embryogenesis". It rather highlights that Sas-4 is required for centriole formation in these neurons. Also, humber = number.

We agree, and have changed the text, thank you very much.

7) Result title: Non-ciliated sensory neurons have centrioles. This is kind of obvious. A better title may be "axon phenotypes correlate with centriole numbers in sensory neurons" but unfortunately i don't think there is good evidence for this (See major point above).

We agree and we have changed. We now believe we have strong evidence to support it. We hope the additional data presented in the revision convincingly demonstrate this point.

Reviewer #1 (Significance (Required)):

As mentioned above, the advance will be important if more evidence is provided. In this case, the paper will be interesting to a broad readership. But currently the paper is limited by the lack of evidence for centrosome function and activity in the neurons.

We hope that reviewer 1, now considers that the manuscript is not limited anymore and that it shows convincing evidence for centrosome function and activity in embryonic neurons.

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

Summary: In this manuscript, Gonzalez et al. examine the potential function of centrosomes in the neurons and muscle cells of Drosophila embryos. By studying various mutant and RNAi lines in which centriole duplication has been disrupted, they conclude that the loss of centrioles disrupts axonal pathfinding and muscle integrity.

Major points: 1. Throughout the manuscript, the phenotypes presented are often quite subtle. For this reason, I would really recommend that these experiments are scored blind. Perhaps the authors did this, but I didn't see any mention of this.

All our phenotypic analyses are performed blind. We apologize for not having originally included this information in the Methods section; it has now been added. Embryos are stained using colorimetric methods (DAB) to label the nervous system, while balancer chromosomes are marked with a fluorescent antibody. This approach allows us to assess and quantify phenotypes using white light without knowing whether the embryos are homozygous mutants or heterozygous, which can only be detected by changing the channels to fluorescence.

1. The authors conclude that neurons have active centrioles that function as centrosomes (Figure 6), but the data here is confusing. The authors state that in these cells they observe acetylated MTs extending from the centrosomes and these colocalised with g-tubulin. But the authors don't show the overlap between centrosomes, g-tubulin and MTs, as they stain for these separately. This is problematic, as it was not clear from these images that the majority of the MTs really are extending from the centrosome: the centrosome may just associate or be close by to these MT cables (Figure 6A,B). Moreover, the authors show that only a fraction of the centrosomes in these cells associate with g-tubulin, so presumably in cells where the centrosomes lack g-tubulin they would not expect the centrosomes to be associated with the MTs-but they do not show that this is the case. Perhaps the authors can't test this, but an alternative would be to show that these MT arrays are absent in Sas-4 mutants. This would give more confidence that these MTs arise from the centrosomes.

We agree that the initial data based on acetylated microtubules and γ-tubulin colocalization were not sufficient to conclude that microtubules originate from the centrosome, as these markers can only suggest association. To address this, we have now included additional experiments that provide direct evidence of centrosome activity.

First, we performed live imaging of aCC neurons expressing EB1-GFP together with Asl-Tomato. Despite the technical challenges of imaging only two neurons per segment in live embryos under strict fluorescence and timing constraints, we were able to clearly observe EB1 comets emerging from the centrosome and moving toward the cell periphery. This demonstrates active microtubule nucleation from centrosomes rather than mere proximity to microtubule bundles.

Second, we carried out a microtubule depolymerization/polymerization assay, which provides unequivocal evidence that polymerization initiates at the centrosome. After depolymerization, microtubules regrew from the centrosome, confirming its role as an active microtubule-organizing center. These experiments go beyond colocalization and directly address the concern that centrosomes might simply be adjacent to microtubule cables.

Regarding the suggestion to use Sas-4 mutants, while we did not perform this experiment, the regrowth assay combined with EB1 imaging strongly supports that these microtubules originate from the centrosome. All new data are presented in Figure 6 and the corresponding text in the revised manuscript.

1. The authors show that muscle cell integrity is compromised by centriole-loss (Figure 2). This is very surprising as it is widely believed that centrosomes are non-functional in muscle cells, and the MTs are instead organised around the nuclear envelope. I'm not aware of the situation in Drosophila muscle cells, but the authors should ideally try to examine if the centrioles are functioning as centrosomes in these cells. At the very least they should discuss how they think centriole-loss is influencing the muscle integrity when it is widely believed they are inactive in these cells.

We do not claim that centrosomes are active in muscle cells at these developmental stages. The observed muscle defects could result from earlier processes such as cell division, migration, or muscle fusion. We agree that this is an intriguing observation; however, pursuing this question further would go beyond the scope of the current manuscript. As requested by the reviewer, we have now expanded the discussion to consider how centriole loss might impact muscle integrity.

Regardless of the strength of the supporting data, I think the authors should tone down their conclusions. The title and abstract led me to believe that centriole loss would cause significant problems in axonal pathfinding and muscle integrity. In all the mutant specimens examined (and certainly the low magnification views shown in Figure 1D'-F', Figure 1I'-K' and Figure 2D'-F') the mutants look very similar to the WT. Many readers may not get past the title and abstract, so the authors should make it clearer that these defects are very subtle.

We have changed the text to convey this idea.

Minor points: 1. In Figures 4 and 5, CP309 staining is relied on to identify centrioles, but there is quite a background of non-specific dots, making it hard to be certain what is a centriole and what isn't. For example, in Figure 5D' there are lots of dots within some of the cells - are any of these centrioles? How can the authors be certain which dot is a centriole in some of the cells shown in Figure 5C'? Is it possible to use a second marker and only count as centrioles dots that are recognised by both antibodies?

We thank the reviewer for this suggestion and agree that using a second marker improves confidence in centriole identification. In a new supplementary figure (Supplementary Fig. 3), we now show that Asl and Plp colocalize in neurons and provide a quantification of the frequency of this colocalization. This dual labelling confirms the identity of centrioles and addresses the concern about non-specific background.

We also apologize for any confusion regarding the presence of foci outside the marked cells. These images are whole-mount embryonic stainings, and the anti-Plp antibody labels all centrosomes in all cells of the embryo, which explains the additional foci observed.

In the abstract that authors state that traditionally centrosomes have been considered to be non-essential in terminally differentiated cells. I don't think this is correct. In the standard "textbook" view of a cell, the centrosome is normally positioned in the centre of the cell organising an extensive array of MTs that are thought play an important role in organising intracellular transport, the positioning and movement of organelles and the maintenance and establishment of cell polarity. I don't think it is only recent evidence that suggests they play vital roles in terminally differentiated cells.

We thank the reviewer for this correction and we have changed the text accordingly.

1. Line 162 the authors state that in the RNAi knockdown lines they observe several additional phenotypes, but then in the same sentence (Line 164) they say that these defects were also observed in the original mutant and mutant/Df lines.

We apologise for this confusion, we have rearranged the sentence for clearance.

The sentences in Line281-287 don't reference any of the Figures, so it seems the authors are just stating these results without presenting any data (e.g. "Significantly, we also found a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". If they've tested this correlation, they should show it.

We have rearranged the sentences for better understanding.

In Figure 7 I did not understand how the authors measured tortuosity (wiggliness) and could see no description in the methods. This is important as, again the defect seems quite subtle, but perhaps I am not understanding which bits of the axon are being measures. Is it just the small bit of the axons close to the asterixis that is being measured, or the whole FasII track?

We have now added another quantification and additional descriptions in the methods section.

Reviewer #2 (Significance (Required)):

The potential function of centrosomes in axonal outgrowth is quite controversial, so this study is potentially of considerable interest.

However, several aspects of the data presented here were confusing or not terribly convincing. In its present state, I don't think the main conclusions are strongly enough supported by the data.

We hope that reviewer 2, now considers that the manuscript is not confusing anymore and that it shows convincing evidence for centrosome function and activity in embryonic neurons.

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

The manuscript of González et al. entitled "Centriole Loss in Embryonic Development Disrupts Axonal Pathfinding and Muscle Integrity" deals with the role of centrosomes in shaping axonal morphology. To this aim the AA analysed Drosophila Sas-4 mutants that are reported to develop until adult stage without centrioles. Remarkably, the AA observe that 50% of the homozygous mutant embryos fail to hatch as larvae. The present observations suggest that centrosome loss results in axonemal shaping defects and muscle developmental abnormalities. Finally, the AA show the presence of functional centrosomes in neurons. In my opinion, the manuscript is interesting because shows unexpected findings. However, to justify these new findings the AA are required to improve some experimental observations.

We thank the reviewer for his summary of our work and for considering it interesting. We have taken into account all the comments and believe that these have helped improve our manuscript.

Major: Abstract- It is unclear in which phenotypic condition the observations of centrosome loss or centrosome presence have been found. Please better explain. l.36. embryos, larvae, adult, from Sas4 or controls? If mutants, the observations are very interesting since Sas4 would be without centrioles. Indeed, Basto et al., show that chemosensory neurons do not develop an axoneme in the absence of centrioles, but extend dendrites toward the sensory bristle.

We have made clear which refer to wild-type and which are Centriole Loss (CL) conditions. CL conditions refer to mutant and downregulation conditions, whereas targeted downregulation refers to RNAi downregulation only in neurons.

I do not think appropriate the use of "centriole" in the main title since the centrioles would be localized by true centriolar antigens rather than by centrosomal antigens. This problem occurs throughout the text and some figures where the AA image centrioles by centrosomal material. In Gig. 5A only the AA properly look at Asl localization. The other pictures of presumptive centrioles or centriole quantification report CP309 dots. This localization does not unequivocally reveal centrioles, since CP309 is essentially required for centrosome-mediated Mt nucleation. There are differentiated Drosophila tissues in which centrioles are present, but inactivated, and unable to recruit pericentriolar material. Mt are nucleated by ncMTOCs that contain centrosomal material and gamma-tubulin. Thus, the centrosomal antigens do not colocalize with centrioles.

We have changed centrioles to centrosomes in the title and most sections in the manuscript. We have also included an extra control, showing that Asl and Plp colocalize and quantify the number of times we find this colocalization in neurons (Supl. Fig 3). Asl is a reliable and widely used marker for centrioles, as it localizes specifically to the centriole structure (Varmark H, Llamazares S, Rebollo E, Lange B, Reina J, Schwarz H, Gonzalez C. Asterless is a centriolar protein required for centrosome function and embryo development in Drosophila. Curr Biol. 2007 Oct 23;17(20):1735-45. doi: 10.1016/j.cub.2007.09.031. PMID: 17935995.)

Minor: l. 58. The early arrest is mainly due to a checkpoint control. In double mutant for Sas4 and P53 the embryos survive longer, even if their further development is asrrested.

We thank the reviewer for this comment, and we have changed the text accordingly.

1. Previous works, also quoted by the AA, reported that in mature neurons the centrosome are inactivated, whereas the present manuscript describes functional centrosomes in Drosophila motor and peripheral nervous system. This is an intriguing observations that needs a better explanation in Discussion section.

We thank the reviewer for this comment, and we have changed the discussion accordingly.

l.143-145. I understand that 50% of the Sas4 embryos that reach the adult stage have centrioles. Is it correct? But if it is so, how the AA explain the absence of centrioles in sensory neurons of adult flies as reported by Basto et al. ?

According to our results they have less centrioles than controls already at embryonic stages. In addition, as reported in Basto et al. they continue losing centrioles during larval stages and metamorphosis, which explains why centrioles are not detected at adult stages.

l.215. It is unclear for me why the AA analyse Sas6 flies, unless explain the mutant phenotype.

To strengthen our conclusions with Sas-4 and exclude the possibility that the observed phenotypes arise from a centrosome-independent function of Sas-4. For this reason, we have taken additional steps to confirm that the effects are specifically due to centrosome loss and we used Sas-6 mutants as one of these.

l.221. How the centrioles have been quantified? What antibody, the AA used.

We have quantified centrosomes using antibodies agains Plp (CP309) and Asl-YFP expression.

l.244. and Fig 4C,D. I see high background with CP309. As reported previously I think better to use antibodies against centriolar proteins, such as Sas6, Ana1, Asl, or Sas4 ( if centrioles are present in 50% of mutants as the AA claim, the antibody could be also useful). In addition, I can see some CP309 spots in Fig 4E,F. Are they centrioles?

Indeed, as we report, Sas-4 mutant embryos are not totally devoid of centrosomes. In addition, and we apologise for the confusion, but the reason why there are foci outside the marked cells in control embryos is because these are wholemount embryonic stainings and the anti-Plp antibody marks all centrosomes in all cells in the embryo, not just in the neurons.

l.270 and Fig. 5A and Fig.5 C-E. Why the AA localize Cp309 and not Asl (Fig. 5A) to detect centrioles?

In a new supplementary figure, we now show that Asl and Plp colocalize and quantify the number of times we find this colocalization in neurons (Supl. Fig 3). So, we can use CP309 in neurons to the same effect as Asl-

L295-296. I cannot see Mts, but only a diffuse staining. I am expecting to see distinct Mt bundles.

In figure 5 it is now easier to see the MT bundles in the new experiment in Fig. 5F-I , where we performed MT depolymerisation/repolymerisation: Nevertheless, we need to stress out that we are doing these analyses in wholemount embryonic stainings.

326-327. How the AA explain this different lethality, even if both the proteins are involved in centriole assembly?

We have now redone all the viability and mutant phenotype analysis using Sas-6 CRISPR mutant over the Deficiency, which is a better way to access the phenotype.

335-337. In my opinion the quoted publications are not relevant.

We believe that these references back up our hypothesis because:

• Metzger et al 2012 stress the importance of nuclear position in muscle development in Drosophila
• Loh et al 2023, relate centrosomes with nuclear migration in Drosophila
• Tillery et al 2018, is a review describing MTs in muscle development in Drosophila.

358-359. Does maternal contribution persist after gastrulation?

While bulk degradation occurs by midblastula transition, some stable maternal products persist beyond gastrulation. In our case, if centrioles are formed due to the maternal contribution, they will only be diluted by cell division, which explains why we can detect centrioles at late embryonic stages.

l.366. This is an intriguing point, but as previously observed I have some problem with centriole localization. References. Please uniform Journal abbreviations and control page numbers.

I hope we have clarified this problem with the new experiments showing MT repolarization from the centrosomes in neurons.

Reviewer #3 (Significance (Required)):

The manuscript is potentially interesting for peoples working of cell and molecular biology, and development. However, the paper needs an additional working to be suitable for publication.

We hope that reviewer 3, considers that the additional work and revision make this manuscript suitable for publication.

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

The manuscript of González et al. entitled "Centriole Loss in Embryonic Development Disrupts Axonal Pathfinding and Muscle Integrity" deals with the role of centrosomes in shaping axonal morphology. To this aim the AA analysed Drosophila Sas-4 mutants that are reported to develop until adult stage without centrioles. Remarkably, the AA observe that 50% of the homozygous mutant embryos fail to hatch as larvae. The present observations suggest that centrosome loss results in axonemal shaping defects and muscle developmental abnormalities. Finally, the AA show the presence of functional centrosomes in neurons. In my opinion, the manuscript is interesting because shows unexpected findings. However, to justify these new findings the AA are required to improve some experimental observations.

Major:

Abstract- It is unclear in which phenotypic condition the observations of centrosome loss or centrosome presence have been found. Please better explain. l.36. embryos, larvae, adult, from Sas4 or controls? If mutants, the observations are very interesting since Sas4 would be without centrioles. Indeed, Basto et al., show that chemosensory neurons do not develop an axoneme in the absence of centrioles, but extend dendrites toward the sensory bristle.

I do not think appropriate the use of "centriole" in the main title since the centrioles would be localized by true centriolar antigens rather than by centrosomal antigens. This problem occurs throughout the text and some figures where the AA image centrioles by centrosomal material. In Gig. 5A only the AA properly look at Asl localization. The other pictures of presumptive centrioles or centriole quantification report CP309 dots. This localization does not unequivocally reveal centrioles, since CP309 is essentially required for centrosome-mediated Mt nucleation. There are differentiated Drosophila tissues in which centrioles are present, but inactivated, and unable to recruit pericentriolar material. Mt are nucleated by ncMTOCs that contain centrosomal material and gamma-tubulin. Thus, the centrosomal antigens do not colocalize with centrioles.

Minor:

l. 58. The early arrest is mainly due to a checkpoint control. In double mutant for Sas4 and P53 the embryos survive longer, even if their further development is asrrested.

l. 102. Previous works, also quoted by the AA, reported that in mature neurons the centrosome are inactivated, whereas the present manuscript describes functional centrosomes in Drosophila motor and peripheral nervous system. This is an intriguing observations that needs a better explanation in Discussion section.

l.143-145. I understand that 50% of the Sas4 embryos that reach the adult stage have centrioles. Is it correct? But if it is so, how the AA explain the absence of centrioles in sensory neurons of adult flies as reported by Basto et al. ?

l.215. It is unclear for me why the AA analyse Sas6 flies, unless explain the mutant phenotype.

l.221. How the centrioles have been quantified? What antibody, the AA used.

l.244. and Fig 4C,D. I see high background with CP309. As reported previously I think better to use antibodies against centriolar proteins, such as Sas6, Ana1, Asl, or Sas4 ( if centrioles are present in 50% of mutants as the AA claim, the antibody could be also useful). In addition, I can see some CP309 spots in Fig 4E,F. Are they centrioles?

l.270 and Fig. 5A and Fig.5 C-E. Why the AA localize Cp309 and not Asl (Fig. 5A) to detect centrioles?

L295-296. I cannot see Mts, but only a diffuse staining. I am expecting to see distinct Mt bundles.

L. 326-327. How the AA explain this different lethality, even if both the proteins are involved in centriole assembly?

l. 335-337. In my opinion the quoted publications are not relevant.

l. 358-359. Does maternal contribution persist after gastrulation?

l.366. This is an intriguing point, but as previously observed I have some problem with centriole localization.

References. Please uniform Journal abbreviations and control page numbers.

Significance

The manuscript is potentially interesting for peoples working of cell and molecular biology, and development. However, the paper needs an additional working to be suitable for publication.

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: In this manuscript, Gonzalez et al. examine the potential function of centrosomes in the neurons and muscle cells of Drosophila embryos. By studying various mutant and RNAi lines in which centriole duplication has been disrupted, they conclude that the loss of centrioles disrupts axonal pathfinding and muscle integrity.

Major points:

1. Throughout the manuscript, the phenotypes presented are often quite subtle. For this reason, I would really recommend that these experiments are scored blind. Perhaps the authors did this, but I didn't see any mention of this.
2. The authors conclude that neurons have active centrioles that function as centrosomes (Figure 6), but the data here is confusing. The authors state that in these cells they observe acetylated MTs extending from the centrosomes and these colocalised with g-tubulin. But the authors don't show the overlap between centrosomes, g-tubulin and MTs, as they stain for these separately. This is problematic, as it was not clear from these images that the majority of the MTs really are extending from the centrosome: the centrosome may just associate or be close by to these MT cables (Figure 6A,B). Moreover, the authors show that only a fraction of the centrosomes in these cells associate with g-tubulin, so presumably in cells where the centrosomes lack g-tubulin they would not expect the centrosomes to be associated with the MTs-but they do not show that this is the case. Perhaps the authors can't test this, but an alternative would be to show that these MT arrays are absent in Sas-4 mutants. This would give more confidence that these MTs arise from the centrosomes.
3. The authors show that muscle cell integrity is compromised by centriole-loss (Figure 2). This is very surprising as it is widely believed that centrosomes are non-functional in muscle cells, and the MTs are instead organised around the nuclear envelope. I'm not aware of the situation in Drosophila muscle cells, but the authors should ideally try to examine if the centrioles are functioning as centrosomes in these cells. At the very least they should discuss how they think centriole-loss is influencing the muscle integrity when it is widely believed they are inactive in these cells.
4. Regardless of the strength of the supporting data, I think the authors should tone down their conclusions. The title and abstract led me to believe that centriole loss would cause significant problems in axonal pathfinding and muscle integrity. In all the mutant specimens examined (and certainly the low magnification views shown in Figure 1D'-F', Figure 1I'-K' and Figure 2D'-F') the mutants look very similar to the WT. Many readers may not get past the title and abstract, so the authors should make it clearer that these defects are very subtle.

Minor points:

1. In Figures 4 and 5, CP309 staining is relied on to identify centrioles, but there is quite a background of non-specific dots, making it hard to be certain what is a centriole and what isn't. For example, in Figure 5D' there are lots of dots within some of the cells - are any of these centrioles? How can the authors be certain which dot is a centriole in some of the cells shown in Figure 5C'? Is it possible to use a second marker and only count as centrioles dots that are recognised by both antibodies?
2. In the abstract that authors state that traditionally centrosomes have been considered to be non-essential in terminally differentiated cells. I don't think this is correct. In the standard "textbook" view of a cell, the centrosome is normally positioned in the centre of the cell organising an extensive array of MTs that are thought play an important role in organising intracellular transport, the positioning and movement of organelles and the maintenance and establishment of cell polarity. I don't think it is only recent evidence that suggests they play vital roles in terminally differentiated cells.
3. Line 162 the authors state that in the RNAi knockdown lines they observe several additional phenotypes, but then in the same sentence (Line 164) they say that these defects were also observed in the original mutant and mutant/Df lines.
4. The sentences in Line281-287 don't reference any of the Figures, so it seems the authors are just stating these results without presenting any data (e.g. "Significantly, we also found a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". If they've tested this correlation, they should show it.
5. In Figure 7 I did not understand how the authors measured tortuosity (wiggliness) and could see no description in the methods. This is important as, again the defect seems quite subtle, but perhaps I am not understanding which bits of the axon are being measures. Is it just the small bit of the axons close to the asterixis that is being measured, or the whole FasII track?

Significance

The potential function of centrosomes in axonal outgrowth is quite controversial, so this study is potentially of considerable interest.

However, several aspects of the data presented here were confusing or not terribly convincing. In its present state, I don't think the main conclusions are strongly enough supported by the data.

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

In this paper, the authors address the important question of the role of centrosomes during neuronal development. They use Drosophila as an in vivo model. The field is somewhat unclear on the role and importance of centrosomes during neuronal development, although the current data would suggest they are dispensable for axon specification and growth. Early studies in cultured mammalian neurons showed that centrosomes are active and that their microtubules can be cut and transported into the neurites. But a study then showed that centrosomes in these cultured neurons are deactivated relatively early during neuronal development in vitro and that ablating centrosomes even when they are active had no obvious effect on axon specification and growth. Consistent with this, a study in Drosophila provided evidence that centrosomes were not active or necessary in different types of neurons. More recently, a study showed that centrosomal microtubules are dispensable for axon specification and growth in mice in vivo but are required for neuronal migration in the cerebral cortex. However, another study has linked the generation of acetylated microtubules at centrosomes with axon development. In this current study, the authors examine the effect of centrosome loss on various motor and sensory neurons and muscles mainly by examining mutants in essential centriole duplication genes. They associate axonal routing and morphology defects with centrosome loss and provide some evidence that centrosomes could still be active in the developing neurons. Overall, they conclude that centrosomes are active during at least early neuronal development and that this activity is important for proper axonal morphology and routing.

While I think this study addressing a very interesting and important question, I think as it stands the data is not sufficient to be conclusive on a role for centrosomes during neuronal development. My biggest concern is that most phenotypes have not yet been shown to be cell autonomous, as whole animal mutants have been analysed rather than analysing the effect of cell-specific depletion, and the evidence for active centrosomes needs to be strengthened. If the authors can provide stronger evidence for a role of centrosomes in axonal development then the paper will certainly be of interest to a broad readership.

Major comments

1. The sas-6 transallelic combination shows only 17% embryonic lethality compared to 50% embryonic lethality with sas-4 mutants. Given that both mutants should result in the same degree of centrosome loss (this should be quantified in sas-6 mutants) it would suggest that either sas-4 has other roles away from centrosomes or that the sas-4 mutant chromosome used in the experiment has other mutations that affect viability. The effect of picking up "second-site lethal" mutations on mutant chromosomes is common and so I would not be surprised if this is the reason for the difference in phenotypes. This can be addressed either by "cleaning up" the sas-4 mutant chromosome by backcrossing to wild-type lines, allowing recombination to occur and replace the potential second site mutations, or by using transallelic combinations of sas-4, as they did for sas-6. The "easier" option may just be to analyse all the phenotypes with the sas-6 transallelic combination.
2. Using "whole animal" mutants for assessing neuronal morphology is risky due to non-cell-autonomous effects. The authors have carried out some phenotypic analysis of neurons depleted of Sas-4 by cell-specific RNAi, but I feel they need to do this for all of their analysis. This includes embryonic lethality measures, quantification of centrosome numbers, and all axonal phenotypes in Sas-4 RNAi neurons. It would also be prudent to use 2 distinct RNAi lines to help ensure any phenotypes are not off-target effects (and this may help clarify why the authors see some additional phenotypes with RNAi). Indeed, there are relatively weak phenotypes in muscles when using RNAi compared to the mutants and these potential non-cell-autonomous effects could then have a knock-on effect on neuronal morphology. If the authors were concerned that RNAi is not very efficient (explaining any potential weaker phenotypes than in mutants) the authors could examine the effectiveness of RNAi lines by analysing protein depletion by western blotting or mRNA depletion by rt-qPCR (although this has to be done in a different cell type due to the difficulty in obtaining a neuronal extract).
3. When analysing centriole presence or absence it is a good idea to stain with two different centriole markers e.g. Asl and Plp. This helps rule out unspecific staining. It is clear from the images that similar sized foci can be observed outside of the cells (see Figure 5A for example), so clearly some of the foci that appear to be within the cells may also be unspecific staining.
4. The evidence for active centrosomes is not that convincing. Acetylated tubulin is associated with stable MTs, which are not normally organised by "active" centrosomes that nucleate dynamic microtubules. Moreover, it is plausible that centriole foci happen to overlap with the acetylated tubulin staining by chance. This would explain why not all centrosomes colocalise with acetylated tubulin signal. The authors could better test centrosome activity by performing live imaging with EB1-GFP. If centrosomes are active, it is very easy to observe the many comets produced by the centrosomes.
5. If the authors believe that centrosomes have a role in axon pathfinding in sensory neurons, they should show that these centrosomes are active, at least during early stages (again using EB1-GFP imaging).
6. The authors mention in the discussion that "increased JNK activity, can result in axonal wiggliness (Karkali et al, 2023)". I therefore wonder whether centrosome loss may induce JNK activation (the stress response), as this would then indicate an indirect effect of centrosome loss on axonal structure rather than a direct influence of centrosome-generated microtubules. The authors could assess whether the DNK-JNK pathway is activated in neurons lacking centrosomes by expression UAS-Puc-GFP and quantifying the nuclear signal.
7. In Figure 5, the authors claim that they find "a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". I don't think this is a strong correlation. The difference in centriole number between embryos with no defects and those with defects is very small. In contrast, the difference between centriole numbers in control (no defects) and mutant (no defects) is very large. So, there does not appear to be a strong correlation between centrosome number and phenotype.

Minor comments

1. I don't understand Figure 3C - why do the % of surviving homozygotes and heterozygotes add up to 100%? Should the grey boxes not relate to dead and the white to surviving?
2. "In mouse fibroblasts, myoblasts and endothelial cells, centrosome orientation is important for nuclear positioning and cell migration(Chang et al, 2015; Gomes et al, 2005; Kushner et al, 2014)." Do you mean "centrosome position"?
3. In the introduction, the authors mention Meka et al. when saying the centrosomal microtubules are important for axonal development, but they should also discuss the counter argument from Vinopal et al., 2023 (Neuron) that showed how centrosomes were required for neuronal migration but not axon growth, which was instead mediated by Golgi-derived microtubules.
4. Lines 228-230 - repeated sentence
5. Additionally, we did not detect centrioles in the quadrant opposite the axon exit point (Fig. 2B n=75) - this data is not in Fig 2B
6. "This significant decrease in the humber of centrioles further supports the critical role of Sas-4 in pioneer neurons of the ventral nerve cord (VNC) during Drosophila embryogenesis". It rather highlights that Sas-4 is required for centriole formation in these neurons. Also, humber = number.
7. Result title: Non-ciliated sensory neurons have centrioles. This is kind of obvious. A better title may be "axon phenotypes correlate with centriole numbers in sensory neurons" but unfortunately i don't think there is good evidence for this (See major point above).

Significance

As mentioned above, the advance will be important if more evidence is provided. In this case, the paper will be interesting to a broad readership. But currently the paper is limited by the lack of evidence for centrosome function and activity in the neurons.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

A previous study by Komada et al. demonstrated that MAP7 is expressed in both Sertoli and germ cells, and that Map7 gene-trap mutant mice display disrupted microtubule bundle formation in Sertoli cells, accompanied by defects in spermatid manchettes and germ cell loss. In the current study, Kikuchi et al. investigated the role of MAP7 in the formation of the Sertoli cell apical domain during the first wave of spermatogenesis. They generated a GFP-tagged MAP7 mouse line and demonstrated that the endogenous MAP7 protein localizes to the apical microtubules in Sertoli cells and to the manchette microtubules in step 9-11 spermatids. They also generated a new Map7 knockout (KO) mouse line in a genetic background distinct from the one used in the previous study. Focusing on stages before the emergence of step 9-11 spermatids, the authors aimed to isolate defects caused by the function of MAP7 in Sertoli cells. They report that loss of MAP7 impairs Sertoli cell polarity and apical domain formation, accompanied by the microtubule remodeling defect. Using the GFP-tagged MAP7 line, they performed immunoprecipitation-mass spectrometry and identified several MAP7-interacting proteins in the testis, including MYH9. They further observed that MAP7 deletion alters the distribution of MYH9. Single-cell RNA sequencing revealed that the loss of MAP7 in Sertoli cells resulted in slight transcriptomic shifts but had no significant impact on their functional differentiation. Single-cell RNA sequencing analysis also showed delayed meiotic progression in the MAP7-deficient testis. Overall, while the study provides some interesting discoveries of early Sertoli cell defects in MAP7-deficient testes, some conclusions are premature and not fully supported by the presented data. The mechanistic investigations remain limited in depth.

Response: We thank the reviewer for this insightful summary. We agree that some of our initial interpretations were speculative and have revised the relevant sections to more accurately reflect the limitations of the current data. We also acknowledge that further mechanistic studies will be important to strengthen our conclusions, and we have outlined these plans in the individual responses below.

Major comments:

• Although the infertility phenotype of the Map7 gene-trap mutant mice has been reported previously, it remains essential to assess fertility in this newly generated MAP7 knockout line. While the authors present testis size and histological differences between WT and KO mice (Extended Fig. 2e and 2f), there is no corresponding description or interpretation in the main text regarding fertility outcomes.

Response: We thank the reviewer for raising this point. Although we had presented the differences in testis size and histology between wild-type and Map7-/- mice, we agree that a description of the corresponding fertility outcomes was missing from the main text. We have now revised the relevant part of the Results section as follows: “Consistent with observations in Map7 gene-trap mice, Map7-/- males exhibited reduced testis size and spermatogenic defects (Supplemental Fig. 2E, F). Notably, the cauda epididymis of Map7-/- males contained no mature spermatozoa (Supplemental Fig. 2F), indicating male infertility.” (page 5, line 33–page 6, line 2)

• In Figure 2C, the authors identified Sertoli cells, spermatogonia cells, and spermatocytes using SEM, based on their cell morphology and adhesion to the basement membrane. Given that the loss of MAP7 disrupts the polarity and architecture of Sertoli cells, the position of germ cells will be affected, making this identification criterion less reliable.

Response: We appreciate the reviewer’s comment. While the reviewer notes that cell identification was based on cell morphology and adhesion to the basement membrane, we clarify that nuclear morphology was also considered, as described in the original manuscript. Specifically, germ cells have spherical nuclei, whereas Sertoli cell nuclei are irregularly shaped (representative segmentation results can be provided as an additional Supplemental Figure upon request). Round spermatids at P21 can be distinguished from spermatocytes by their smaller nuclear size. In addition, spermatogonia remain attached to the basement membrane even in Map7-/- testes, as confirmed by GFRα1-positive spermatogonial stem cells (Figure 6A). Together, these features ensure reliable identification of each cell type, independent of the altered polarity observed in Map7-deficient Sertoli cells.

• In Figure 2e, the number of Sox9-positive Sertoli cells in MAP7 knockout mice appears higher than that in the control at P17. Quantification of total Sox9-positive cells should be done to determine whether MAP7 deletion increases Sertoli cell numbers.

Response: As suggested by the reviewer, we will quantify the density of SOX9-positive Sertoli cells per unit area of seminiferous tubule at P10 and P17 in Map7+/- and Map7-/- testes, and include the results in the revised manuscript.

• To determine whether MAP7's role in regulating Sertoli cell polarity relies on germ cells, the authors treated mice with busulfan at P28 to delete germ cells, a stage after Sertoli cell polarity defect has developed in MAP7 knockout mice. This data is insufficient to support the conclusion that MAP7 regulates Sertoli cell polarity independently of the presence of germ cells. Germ cell deletion should be done before the Sertoli cell defect develops to address this question.

Response: We appreciate the reviewer’s thoughtful comment regarding the interpretation of the busulfan experiments. While depletion of germ cells at P28 enabled us to assess Sertoli cell polarity in the absence of postnatal spermatogonia, these experiments do not definitively determine whether MAP7 regulates Sertoli cell polarity independently of germ cells. Neonatal germ-cell depletion would more directly test germ cell–independent effects; however, systemic busulfan administration at early developmental stages is highly toxic, often causing bone marrow failure and multi-organ damage, which precludes survival and confounds analysis of testis-specific effects. Although germ cell ablation could, in principle, be achieved using transgenic approaches that exploit the natural resistance of mice to diphtheria toxin (DTX) (reviewed in Smith et al., Andrology, 2015), these strategies require multiple transgenes and show minor variability in efficiency, making them impractical for our current experiments. Generating the necessary genetic combinations would require considerable time. We therefore plan to pursue alternative genetic approaches in future work.

In the revised manuscript, we have modified the relevant section to more accurately reflect the limitations of the current experiments, as follows: “Busulfan was administered at P28, and testes were analyzed 6 weeks later, after complete elimination of germ cell lineages. Following treatment, Map7+/- mice showed testis-to-body weight ratios comparable to untreated Map7-/- mice (Supplemental Fig. 3D), and hematoxylin-eosin (HE) staining confirmed germ cell depletion (Fig. 2F; Supplemental Fig. 3E). In Map7+/- testes, most Sertoli nuclei remained basally positioned, indicating that once apical–basal polarity is established, it is stably maintained even in the absence of germ cells. In contrast, Map7-/- Sertoli nuclei were frequently misoriented toward the lumen under the same conditions (Fig. 2F; Supplemental Fig. 3E), suggesting that polarity defects in Map7-deficient Sertoli cells occur independently of germ cell presence.” (page 7, lines 20–28)

In addition, we have added the following sentences to the Discussion section to highlight the implication of these findings: “In addition, even after germ cell depletion by busulfan treatment, Map7-deficient Sertoli cells failed to reestablish basal nuclear positioning, indicating that loss of MAP7 causes an intrinsic polarity defect. These findings suggest that MAP7 acts as a cell-autonomous regulator of Sertoli cell polarity, rather than mediating effects indirectly through germ cell–Sertoli cell interactions.” (page 15, lines17–21)

• The resolution of the SEM images in Figure 3c is insufficient to evaluate tight and adherens junctions clearly. As such, these images do not convincingly support the claim that adherens junctions are absent in the KO testes.

Response: We thank the reviewer for this insightful comment. Tight junctions can be reliably identified in SEM images as dense intercellular structures accompanied by endoplasmic reticulum aligned along the cell boundaries. The region immediately apical to the tight junctions likely corresponds to adherens junctions, which are also associated with the endoplasmic reticulum. Unlike tight junctions, these regions exhibit wider intercellular spaces, consistent with the looser membrane apposition characteristic of adherens junctions, although they cannot be unambiguously distinguished from gap junctions or desmosomes based on morphology alone. In the original figure, 2× binning reduced image resolution, which may have contributed to the reviewer’s concern.

In the revised manuscript, we have re-acquired the SEM images in high-resolution mode, focusing on the relevant regions. The new high-resolution images have replaced the original panels in revised Figure 3C, providing clearer visualization of junctional structures at P10 and P21 in Map7+/- and Map7-/- testes. The original Figure 3C images have been moved to Supplemental Figure 4B for reference.

The corresponding section in the Results has been revised as follows in the updated manuscript: “We then performed SEM to examine the effects of Map7 KO. In P21 Map7+/- testes, electron-dense regions along the basal side of Sertoli–Sertoli junctions corresponded to tight junctions closely associated with the endoplasmic reticulum, consistent with previous reports (Luaces et al. 2023) (Fig. 3C; Supplemental Fig. 4B). The region immediately apical to the tight junctions likely represents adherens junctions, which were also associated with the endoplasmic reticulum. Unlike tight junctions, these regions displayed wider intercellular spaces, reflecting the looser membrane apposition typical of adherens junctions, though they could not be definitively distinguished from gap junctions or desmosomes based on morphology alone (Fig. 3C; Supplemental Fig. 4B). At P10, both Map7+/- and Map7-/- testes lacked clearly defined tight junctions and adherens junction–like structures (Fig. 3C; Supplemental Fig. 4B). In P21 Map7-/- mice, Sertoli cells formed expanded basal tight junctions but failed to establish adherens junction–like structures (Fig. 3C; Supplemental Fig. 4B).” (page 8, line 34–page 9, line 12)

• GFP-tagged reporter mice and HeLa cells were used for immunoprecipitation-mass spectrometry to identify proteins that interact with MAP7. Given that the authors aimed to elucidate the mechanism by which MAP7 regulates Sertoli cell cytoskeleton organization, the rationale for including HeLa cells is unclear and should be better justified or reconsidered.

Response: We thank the reviewer for this comment. MAP7-egfpKI HeLa cells were used as a complementary system to identify MAP7-associated proteins, providing sufficient material and a controlled environment for robust detection. By comparing IP-MS results from MAP7-egfpKI HeLa cells and P17–P20 Map7-egfpKI testes, we can distinguish proteins that are specific to polarized Sertoli cells: proteins detected exclusively in P17–P20 testes may be involved in Sertoli cell polarization, whereas proteins detected in both systems likely represent general MAP7-associated factors that are not specific to Sertoli cell polarity.

This rationale has been clarified in the revised manuscript by adding the following sentence to the Results section: “MAP7-egfpKI HeLa cells were used as a complementary system, providing sufficient material and a controlled environment for robust detection of MAP7-associated proteins. Comparison of IP-MS results between MAP7-egfpKI HeLa cells and P17–P20 Map7-egfpKI testes allows identification of MAP7-associated proteins that are specific to polarized Sertoli cells, whereas proteins detected in both systems likely represent general MAP7-associated proteins.” (page 9 lines 27-32)

• The authors observed that MYH9, one of the MAP7-interacting proteins, does not colocalize with ectopic microtubule and F-actin structures in MAP7 KO testes and concluded that MAP7 facilitates the integration of microtubules and F-actin via interaction with NMII heavy chains. This conclusion is speculative and not adequately supported by the presented data.

Response: We thank the reviewer for this insightful comment. We agree that our initial conclusion was speculative and have revised the relevant section to more accurately reflect the limitations of the current data. The revised text now reads as follows: “These findings indicate that MYH9 localization at the luminal interface depends on MAP7, and suggest that MAP7 helps coordinate microtubules and F-actin, potentially via its association with NMII heavy chains.” (page 10, lines 13–15)

To further elucidate this mechanism, we will perform biochemical domain-mapping to define the MAP7 region responsible for MYH9 complex formation. We have already established a series of human MAP7 deletion mutants (as reported previously, EMBO Rep., 2018) and will conduct co-immunoprecipitation assays in HEK293 cells to identify the specific MAP7 domain required for complex formation with MYH9. Based on these results, we plan to use AlphaFold3 to predict the three-dimensional structure of the MAP7–MYH9 complex. These analyses will help clarify how MAP7 associates with the actomyosin network and provide additional mechanistic insights that complement our in vivo observations of MYH9 mislocalization in Map7-/- testes.

• The authors used Spearman correlation coefficients to analyze six Sertoli cell clusters and generated a minimum spanning tree to infer differentiation trajectories. However, details on the method used for constructing the tree are lacking. Moreover, relying solely on Spearman correlation to define differentiation topology is oversimplified.

Response: We appreciate the reviewer’s valuable feedback. We agree that Spearman correlation alone is insufficient to infer differentiation topology. In response, we reanalyzed the data using Monocle3, which implements branch-aware pseudotime inference to capture both cluster continuity and differentiation directionality. This reanalysis provides a more accurate reconstruction of differentiation trajectories among the six Sertoli cell clusters. Although the overall trajectories appeared different and a higher proportion of Map7-/- Sertoli cells exhibited very low pseudotime values, comparison of the control and Map7-/- trajectories revealed that the average node degree was nearly identical, indicating that the local graph structure—reflecting the connectivity among neighboring cells—was largely preserved. The numbers of branch points and the graph diameter differed slightly, likely due to differences in sample size (311 control vs. 434 Map7-/- Sertoli cells) and distribution bias rather than major topological changes. Accordingly, Figures 5C and 5D have been replaced with the updated Monocle3-based trajectory analysis, and the corresponding text in the Results section and figure legend have been revised as follows:

“To reconstruct differentiation trajectories among the six Sertoli cell clusters, we reanalyzed the datasets using Monocle3, which incorporates branch-aware pseudotime inference. Cluster C1 was selected as the root based on shared specificity and entropy scores, consistent with its metabolically active and transcriptionally diverse profile (Fig. 5B, C; Supplemental Fig. 7). While the overall trajectories appeared altered, the proportion of Map7-/- Sertoli cells with very low pseudotime values was only modestly increased (Fig. 5D). Comparison with controls showed that the average node degree was nearly identical (Fig. 5C), indicating that the local graph structure, reflecting connectivity among neighboring cells, remained largely intact. Minor differences in branch points and graph diameter likely reflect inherent variability in the data rather than major topological changes (Supplemental Fig. 6B). Consistent with this, the relative proportions of the six clusters showed only modest shifts, suggesting that the overall architecture of Sertoli cell differentiation is largely preserved in the absence of MAP7.” (page 11, lines 7-18)

“(C) Control and Map7-/- Sertoli cells were visualized separately using UMAPs constructed in Seurat. Using the same datasets, pseudotime trajectories were inferred with Monocle3. For root selection, shared_score (cluster overlap), specificity_score (cluster uniqueness), and entropy_score (transcriptional diversity) were computed, resulting in cluster 1 being selected as the root. The numbers of nodes, edges, branch points, average degree, and diameter of each trajectory are shown below the corresponding UMAPs. (D) Parallel comparison of pseudotime distributions between control and Map7-/- populations.” (page 30, lines 5-12)

Minor comments:

• Several extended data figures are redundant with main figures and do not provide additional value (e.g., Fig. 2d vs. Extended Data Fig. 3a; Fig. 2f vs. Extended Data Fig. 3d; Fig. 2C vs. Extended Data Fig. 4b; Fig. 3d vs. Extended Data Fig. 4c). The authors should consolidate or remove duplicates.

Response: Regarding the concerns about redundancy between main and Supplemental figures, we would like to clarify the rationale for retaining certain Supplemental figures.

Fig. 2D vs. Supplemental Fig. 3A: Due to space limitations in the main figure, only the merged three-color image was shown. We believe that the single-color grayscale images in Supplemental Fig. 3A provide additional clarity, allowing easier visualization of SOX9-positive Sertoli cell distribution and differences in F-actin structure.

Fig. 2F vs. Supplemental Fig. 3E: In the main figure, only the high-magnification image was shown due to space constraints. The lower-magnification image in Supplemental Fig. 3E demonstrates that the selected field was not chosen arbitrarily, providing context for the observed structures. In addition, Supplemental Fig. 3E includes both low- and high-magnification images of age-matched busulfan (-) testes as a control for the busulfan (+) condition, further supporting the validity of the comparison.

For the above-mentioned cases (Fig. 2D vs. Supplemental. 3A; Fig. 2F vs. Supplemental Fig. 3E), as well as other potentially overlapping figures (e.g., Fig. 3D vs. Supplemental Fig. 4C), we believe that the additional single-channel and lower-magnification images provide important context that cannot be fully conveyed in the main figures due to space limitations. Nevertheless, to address the reviewer’s concern, we will (i) clearly state the purpose of each Supplemental figure in the corresponding legends, and (ii) re-evaluate all figures to consolidate or remove any truly redundant panels. Our goal is to ensure that all figures collectively convey the data in the most concise and informative manner.

• Figure citations in the main text do not consistently match figure content. For example, on page 7 (lines 5-6), the text refers to Extended Data Fig. 4a for SOX9 staining. Yet, it is the extended Data Fig. 3a that contains the relevant data. Similarly, the reference to Extended Data Fig. 4b and 4c on page 7 (lines 7-8) for adult defects is inaccurate.

Response: We thank the reviewer for drawing attention to these inconsistencies. We have carefully checked all figure citations throughout the main text and corrected them so that they consistently match the figure content. The revised manuscript reflects these corrections.

• In Figure 2e, percentages of Sertoli cells across three layers are shown. The figure legend should specify which layer(s) show statistically significant differences between WT and KO.

Response: We are grateful to the reviewer for highlighting this point. Statistical comparisons were performed between Map7+/- and Map7-/- mice within each corresponding layer at P17. Statistical significance was assessed using Student’s t-test, and all three layers showed significant differences between Map7+/- and Map7-/- (P < 2.20 × 10⁻⁴). The figure legend has been revised accordingly as follows: “Statistical comparisons between Map7+/- and Map7-/- mice were performed for each corresponding layer at P17 using Student’s t-test. All three layers showed significant differences between Map7+/- and Map7-/- mice (*, P<2.20 × 10⁻⁴).” (page 28, lines 5-8)

• The current color scheme for F-actin and TUBB3 in Figure 3 lacks sufficient contrast. Adjusting to more distinguishable colors would improve readability.

Response: Response: We thank the reviewer for this helpful suggestion. In the original merged images, four channels (DNA, TUBB3, F-actin, and β-catenin) were displayed together, which reduced contrast between cytoskeletal signals. To improve clarity, we generated new merged images showing only TUBB3 and F-actin, allowing better visual distinction between these components. In addition, β-catenin and DNA are now displayed together as a separate merged image (β-catenin in yellow and DNA in blue) in the final column, highlighting the altered localization of β-catenin in Map7-/- testes.

• Since multiple scale bars with different units are present within the same figures, adding units directly above or beside each scale bar would improve readability.

Response: We thank the reviewer for the suggestion. Following this recommendation, we have added units directly above each scale bar in all figures to improve readability.

• It is recommended to directly mark Sertoli cells, spermatogonia, and spermatocytes on the SEM images in Figure 2C for clearer visualization.

Response: We thank the reviewer for the suggestion. We will follow this recommendation by performing segmentation and directly marking Sertoli cells, spermatogonia, and spermatocytes on the SEM images in Figure 2C to improve visualization.

• The quantification of Sertoli cell positioning shown in Fig. 2C is already described in the main text and is unnecessary in the figure.

Response: We appreciate the reviewer’s comment regarding the quantification of Sertoli cell positioning. Although the results are described in the main text, we believe that the visual presentation in Figure 2C is essential for conveying the spatial distribution pattern in an intuitive and comparative manner. To address the concern about redundancy, we have slightly revised the figure legend (page 27, lines 28–29) to clarify that this panel provides a visual summary of the quantitative data described in the text, thereby improving clarity without unnecessary duplication.

_Referee cross-commenting_

I concur with Reviewer 2 that the Map7-eGFP mouse model is a valuable tool for the research community. I also agree that performing MAP7-MYH9 double immunofluorescence staining to demonstrate their colocalization would further strengthen the authors' conclusions regarding their interaction. My overall assessment of the manuscript remains unchanged: the study represents an incremental advance that extends previous findings on MAP7 function but provides limited new mechanistic insight.

Reviewer #1 (Significance):

This study investigates the role of the microtubule-associated protein MAP7 in Sertoli cell polarity and apical domain formation during early stages of spermatogenesis. Using GFP-tagged and MAP7 knockout mouse models, the authors show that MAP7 localizes to apical microtubules and is required for Sertoli cell cytoskeletal organization and germ cell development. While the study identifies early Sertoli cell defects and candidate MAP7-interacting proteins, the mechanistic insights remain limited, and several conclusions require stronger experimental support. Overall, the discovery represents an incremental advance that extends prior findings on MAP7 function, providing additional but modest insights into the role of MAP7 in cytoskeletal regulation in male reproduction.

Response: We thank the reviewer for their constructive comments and thoughtful evaluation of our manuscript. We appreciate the positive feedback regarding the value of the Map7-egfpKI mouse model for the research community. We also thank the reviewer for the suggestion to perform MAP7–MYH9 double immunofluorescence staining to demonstrate colocalization, which we agree will further strengthen the mechanistic support.

We would like to clarify that several aspects of our findings represent novel contributions within a field where the mechanisms of microtubule remodeling during apical domain formation have remained largely unresolved. In particular, our study provides evidence that MAP7 is asymmetrically enriched at the apical microtubule network in Sertoli cells and contributes to the directional organization of these microtubules—an aspect of Sertoli cell polarity that has not been previously characterized. Our results further indicate that dynamic microtubule turnover, rather than stabilization alone, is required for proper apical domain formation, addressing a gap in current understanding of how microtubules are reorganized during early polarity establishment. In addition, the data support a role for MAP7 in coordinating microtubule and actomyosin organization, suggesting a scaffolding function that links these cytoskeletal systems. We also observe that Sertoli cell polarity can be functionally separated from cell identity and that disruptions in apical domain architecture precede delays in germ cell developmental progression. Taken together, these observations provide mechanistic insight that expands upon previous studies of MAP7 function at the cellular level.

The conclusions are supported by multiple, complementary lines of evidence, including knockout and Map7-egfpKI mouse models, high-resolution electron microscopy, immunoprecipitation–mass spectrometry, and single-cell RNA sequencing. While we agree that further experiments, such as MAP7–MYH9 double staining, will strengthen the mechanistic framework, we will also perform complementary biochemical analyses to provide additional insight. Specifically, we plan to conduct domain-mapping experiments to identify the MAP7 region required for MYH9 complex formation, coupled with co-immunoprecipitation assays in cultured cells to validate this association.

Although generating new mutant mouse lines is not feasible within the scope of this revision, and no in vitro system fully recapitulates Sertoli cell polarization, these complementary approaches will provide further mechanistic support. We believe that these planned experiments, together with the current dataset, will clarify the underlying mechanisms and reinforce the significance of our findings, while appropriately acknowledging the current limits of experimental evidence.

Reviewer #2 (Evidence, reproducibility and clarity):

In this manuscript the authors evaluate the role of Microtubule Associated Protein 7 (MAP7) in postnatal Sertoli cell development. The authors build two novel transgenic mouse lines (Map7-eGFP, Map7 knockout) which will be useful tools to the community. The transgenic mouse lines are used in paired advanced sequencing experiments and advanced imaging experiments to determine how Sertoli cell MAP7 is involved in the first wave of spermatogenesis. The authors identify MAP7 as an important regulator of Sertoli cell polarity and junction formation with loss of MAP7 disrupting intracellular microtubule and F-actin arrangement and Sertoli cell morphology. These structural issues impact the first wave of spermatogenesis causing a meiotic delay that limits round spermatid numbers. The authors also identify possible binding partners for MAP7, key among those MYH9.

The authors did a great job building a complex multi-modal project that addressed the question of MAP7 function from many angles. The is an excellent balance of using many advanced methods while still keeping the project narrowed, to use only tools to address the real questions. The lack of quality testing on the germ cells outside of TUNEL is disappointing, but the Conclusion section implies that this sort of work is being done currently so the omission in this manuscript is acceptable. However, there is an issue with the imaging portion of the work on MYH9. The conclusions from the MYH9 data is currently overstated, super-resolution imaging of Map7 knockouts with microtubule and F-actin stains, and imaging that uses MYH9 with either Map7-eGFP or anti-MAP7 are also needed to both support the MAP7-MYH9 interaction normally and lack of interaction with failure of MYH9 to localize to microtubules and F-actin in knockouts. Since a Leica SP8 was used for the imaging, using either Leica LIGHTNING or just higher magnification will likely be the easiest solution.

Response: We sincerely appreciate the reviewer’s thorough and positive evaluation of our study. We are encouraged that the reviewer recognized the overall strength of our multi-modal approach and the scientific value of the Map7-egfp knock-in and Map7 knockout genome-edited mouse models that we generated. We also thank the reviewer for highlighting the balance between methodological breadth and focused, hypothesis-driven investigation in our work.

Regarding the reviewer’s valuable comments on the imaging data, we have addressed them as follows. We improved the cytoskeletal imaging data as described in response to the reviewer’s minor comments. Specifically, in the revised Figure 3B, we replaced the original images with higher-resolution confocal images to provide a clearer view of cytoskeletal organization. In addition, following Reviewer #1’s suggestion, we modified the panel layout to enlarge each field and enhance the contrast between TUBB3 and F-actin channels, allowing better visualization of their altered localization in Map7-/- testes.

We agree that super-resolution imaging comparing control and Map7-/- testes stained for TUBB3 and F-actin would further strengthen the analysis. If the current resolution is still considered insufficient, we plan to perform additional imaging using a Carl Zeiss Airyscan or Leica Stellaris 5 system to further improve spatial resolution and confirm the observed cytoskeletal phenotypes. Finally, we will perform co-imaging of MYH9 with MAP7 to validate their spatial relationship under normal conditions, complementing the existing data obtained from Map7-/- testes.

This manuscript is nicely organized with almost all of the results spelled out very clearly and almost always paired with figures that make compelling and convincing support for the conclusions. There are minor revision suggestions for improving the manuscript listed below. These include synching up Figure and Supplemental Figure reference mismatches. There are also many minor, but important, details that need to be added to the Methods section including many catalog numbers and some references.

- Some of the imaging, especially Fig4F could benefit and be more convincing with super-resolution imaging in the 150nm range (SIM, Airyscan, LIGHTNING, SoRa) possibly even just imaging with a higher magnification objective (60x or 100x)

Response: We appreciate the reviewer’s suggestion to improve the resolution of the imaging data. In addition to revising Figure 3B as described above, we have also replaced the images in Figure 4F with higher-resolution confocal images to provide a clearer view of MYH9 localization relative to microtubules and F-actin. These revised images highlight that MYH9 specifically accumulates at apical regions where microtubules and F-actin intersect, forming the apical ES, but is not localized to the basal ES-associated F-actin structures. To retain spatial context and allow readers to appreciate the overall distribution pattern, the original lower-magnification images from Figure 4F have been moved to Supplemental Figure 5.

- SuppFig1D: Please add context in the legend to the meaning of the Yellow Stars and "O->U" labels. The latter would seem to be to indicate the Ovarian and Uterine sides of the image

Response: In response to this comment, we revised the figure legend to clarify the annotations. The legend now states: “O, ovary side; U, uterus side. Asterisks indicate secretory cells that lack planar cell polarity.”

- Pg6Line7: up to P23 or up to P35?

Response: We appreciate the reviewer’s attention to this detail. The text has been revised for clarity as follows: “To examine the temporal dynamics of Sertoli cell polarity establishment, we analyzed seminiferous tubule morphology across the first wave of spermatogenesis, from postnatal day (P)10 to P35. To specifically assess the role of MAP7 in Sertoli cells while minimizing contributions from germ cells, our analysis focused on stages up to P23, before MAP7 expression becomes detectable in step 9–11 spermatids (Fig. 1), to exclude potential secondary effects resulting from MAP7 loss in germ cells.” (page 6, lines 5-10)

- SuppFig4B: Does SuppFig4B reference back to Fig3B or Fig3C? If the latter please update this in the legend.

- Pg7Line21-23: Is SuppFig3D,E meant to be referenced and not SuppFig5A,B?

- Pg8Line22-25: Is SuppFig4A meant to be reference and not SuppFig5?

- Pg8Line34-Pg9Line: Is SuppFig4B meant to be reference and not SuppFig5B?

Response: We appreciate the reviewer’s careful reading. All mismatches in Supplemental figure references have been corrected, ensuring that each reference in the text now accurately corresponds to the appropriate data.

- Pg9Line28-33: Would the authors be willing to rework this figure to include images that more closely match the reported findings? The current version does not strongly support the idea that MYH9 fails to localize to microtubule and F-actin domains in Map7 knockout P17 seminiferous tubules. This could also just be a matter of acquiring these images at a higher magnification or with a lower-end (150nm range) super-resolution system (SIM, Airyscan, LIGHTNING, SoRa etc)

Response: Following the reviewer’s recommendation, we replaced the images in Figure 4F with higher-resolution confocal images to better visualize MYH9 localization relative to microtubules and F-actin in Map7+/- and Map7-/- testes. These revised images demonstrate that MYH9 specifically accumulates at apical regions where microtubules and F-actin intersect, but not at the basal ES-associated F-actin structures. To preserve spatial context, the original low-magnification images have been moved to Supplemental Figure 5. If additional resolution is required, we are prepared to acquire further images using an Airyscan or Stellaris 5 system.

- SuppFig7A: The legend notes these are P23 samples but the image label says 8W. Please update this to whichever is the correct age.

Response: We thank the reviewer for pointing out this discrepancy. The figure legend for Supplemental Figure 7A (now revised as Supplemental Figure 8A) has been corrected to indicate that the samples are from 8-week-old mice, consistent with the image label.

- Pg16Line4-5: Please include in the text the vendor and catalog number for the C57BL/6 mice

Response: The text now specifies: “C57BL/6NJcl mice were purchased from CLEA Japan (Tokyo, Japan)” (page 17, line 4). CLEA Japan does not assign catalog numbers to mouse strains.

- Pg16Line18-19: Please include in the text the catalog number for the DMEM

- Pg16Line19-20: Please include in the text the vendor and catalog number for the FBS

- Pg16Line20: Please include in the text the vendor and catalog number for the Pen-Strep

Response: We have added vendor and catalog information as follows: “Wild-type and MAP7-EGFPKI HeLa cells were cultured in Dulbecco’s Modified Eagle Medium (DMEM, 043-30085; Fujifilm Wako Pure Chemical, Osaka, Japan) supplemented with 10% fetal bovine serum (FBS, 35-015-CV; Corning, Corning, NY, USA) and penicillin–streptomycin (26253-84; Nacalai, Kyoto, Japan) at 37 °C in a humidified atmosphere containing 5% CO₂ 18.” (page 17, lines 18-22)

- Pg17Line6-12: Thank you for including organized and detailed information about the primers, please also define the PCR protocol used including temperatures, timing, and cycles for Map7 knockout genotyping

- Pg17Line20-27: Thank you for including organized and detailed information about the primers, please also define the PCR protocol used including temperatures, timing, and cycles for Map7-eGFP genotyping

Response: The text has been updated to include the PCR conditions used for genotyping as follows: “Genotyping PCR was routinely performed as follows. Genomic DNA was prepared by incubating a small piece of the cut toe in 180 µL of 50 mM NaOH at 95 °C for 15 min, followed by neutralization with 20 µL of 1 M Tris-HCl (pH 8.0). After centrifugation for 20 min, 1 µL of the resulting DNA solution was used as the PCR template. Each reaction (8 µL total volume) contained 4 µL of Quick Taq HS DyeMix (DTM-101; Toyobo, Osaka, Japan) and a primer mix. PCR cycling conditions were as follows: 94 °C for 2 min; 35 cycles of 94 °C for 30 s, 65 °C for 30 s, and 72 °C for 1 min; followed by a final extension at 72 °C for 2 min and a hold at 4 °C. PCR products were analyzed using agarose gel electrophoresis. This protocol was also applied to other mouse lines and alleles generated in this study.” (page 18, lines 17–25)

- Pg17Line30: Please include in the text the vendor and catalog number for the Laemmli sample buffer

Response: We clarified that the buffer was prepared in-house.

- Pg17Line32&SuppTable1: Thank you for including an organized and detailed table for the primary antibodies used, please also make either a similar table or expand the current table to include secondary antibody information

- Pg17Line32: Please note in the text which primary antibodies and secondary antibodies from Supp Table 1

Response: Supplementary Table 1 has been updated to include both primary and HRP-conjugated secondary antibodies. In the Immunoblotting section of the Materials and Methods, we specified the antibodies used: “The following primary antibodies were used: mouse anti-Actin (C4, 0869100-CF; MP Biomedicals, Irvine, CA, USA), mouse anti-Clathrin heavy chain (610500; BD Biosciences, Franklin Lakes, NJ, USA), rat anti-GFP (GF090R; Nacalai, 04404-84), rabbit anti-MAP7 (SAB1408648; Sigma-Aldrich, St. Louis, MO, USA), rabbit anti-MAP7 (C2C3, GTX120907; GeneTex, Irvine, CA, USA), and mouse anti-α-tubulin (DM1A, T6199; Sigma-Aldrich). Corresponding HRP-conjugated secondary antibodies were used for detection: goat anti-mouse IgG (12-349; Sigma-Aldrich), goat anti-rabbit IgG (12-348; Sigma-Aldrich), and goat anti-rat IgG (AP136P; Sigma-Aldrich). Detailed information for all primary and secondary antibodies is provided in Supplementary Table 1.” (page 19, lines 14-22)

- Pg18Line2: Please include in the text the vendor and catalog number for the Bouin's

Response: The text has been updated to indicate that Bouin’s solution was prepared in-house

- Pg18Line3: Please include in the text the catalog number for the CREST-coated glass slides

- Pg18Line7: Please include in the text the catalog number for the OCT compound

- Pg18Line11: Please include in the text the vendor and catalog number for the Donkey Serum

- Pg18Line11: Please include in the text the vendor and catalog number for the Goat Serum

Response: The text now includes vendor and catalog information for all these reagents, including CREST-coated slides (SCRE-01; Matsunami Glass, Osaka, Japan), OCT compound (4583; Sakura Finetechnical, Tokyo, Japan), donkey serum (017-000-121; Jackson ImmunoResearch Laboratories, PA, USA), and goat serum (005-000-121; Jackson ImmunoResearch Laboratories).

- Pg18Line13: Thank you for including an organized and detailed table for the primary antibodies used, please also make either a similar table or expand the current table to include secondary antibody information

Response: We thank the reviewer for the suggestion. Supplementary Table 1 already includes information for the antibodies used for immunoblotting, and we have now added information for the Alexa Fluor-conjugated secondary antibodies used for immunofluorescence in this study.

- Pg18Line18: Please include in the text the vendor and catalog number for the DAPI

Response: The text has been updated to include the vendor and catalog number for DAPI (D9542; Sigma-Aldrich).

- Pg18Line19: Please also include information about the objectives used including catalog numbers, detectors used (PMT vs HyD)

Response: We thank the reviewer for the suggestion. The following information has been added to the Histological analysis section in Materials and Methods: “Objectives used were HC PL APO 40×/1.30 OIL CS2 (11506428; Leica) and HC PL APO 63×/1.40 OIL CS2 (11506350; Leica), with digital zoom applied as needed for high-magnification imaging. DAPI was detected using PMT detectors, while Alexa Fluor 488, 594, and 647 signals were captured using HyD detectors. Images were acquired in sequential mode with detector settings adjusted to prevent signal bleed-through.” (page 20, lines 13-17)

- Pg18Line23: Please cite in the text the reference paper for Fiji (Schindelin et al. 2012 Nature Methods PMID: 22743772) and note the version of Fiji used

- Pg18Line24: Please note the version of Aivia used

Response: We have revised the text accordingly by citing the reference paper for Fiji (Schindelin et al., 2012, Nature Methods, PMID: 22743772) and noting the version used (v.2.16/1.54p). In addition, we have added the version of Aivia used in this study (version 14.1).

- Pg18Line25: If possible, please use a more robust and reliable system than Microsoft Excel to do statistics (Graphpad Prism, Stata, R, etc), if this is not possible please note the version of Microsoft Excel used

Response: We appreciate the reviewer’s suggestion. For basic statistical analyses such as the Student’s t-test, we used Microsoft Excel (Microsoft Office LTSC Professional Plus 2021), which has been sufficient for these standard calculations. For more advanced analyses, including ANOVA and single-cell RNA-seq analyses, we used R. These details have now been added to the text.

- Pg18Line25: Please cite in the text the reference paper for R (R Core Team 2021 R Foundation for Statistical Computing "R: A Language and Environment for Statistical Computing") and note the version of R used

- Pg18Line25: Please note the specific R package with version used to do ANOVA, and cite in the text the reference for this package

Response: We have cited the reference for R (R Core Team, 2021. R: A Language and Environment for Statistical Computing. R Foundation for Statistical Computing, Vienna, Austria) and noted the version used (version 4.4.0) in the text. In addition, regarding ANOVA, we have added the following description: “For ANOVA analysis, linear models were fitted using the base stats package (lm function), and analysis of variance was conducted with the anova function.” (page 20, lines 23-25)

- Pg18Line25: Please clarify, was a R package called "AVNOVA" used to do ANOVA or is this a typo?

Response: We thank the reviewer for pointing this out. It was a typographical error — the correct term is “ANOVA”. The text has been corrected accordingly.

- Pg18Line32: Please include in the text the catalog number for the EPON 812 Resin

- Pg19Line3: Please include the version number for Stacker Neo

- Pg19Line5: Please include the vendor and version number for Amira 2022

- Pg19Line5: Please include the version number for Microscopy Image Browser

- Pg19Line5: Please include the version number for MATLAB that was used to run Microscopy Image Browser

Response: We added the catalog number for the EPON 812 resin and the vendor and version information for the software used. The following details have been included in the revised text:

EPON 812 resin: TAAB Embedding Resin Kit with DMP-30 (T004; TAAB Laboratory and Microscopy, Berks, UK)

Stacker Neo: version 3.5.3.0; JEOL

Amira 2022: version 2022.1; Thermo Fisher Scientific

Microscopy Image Browser: version 2.91

Note that although Microscopy Image Browser is written in MATLAB, we used the standalone version that does not require a separate MATLAB installation.

- Pg19Line: 9-10: Please include in the text the catalog number for the complete protease inhibitor

- Pg19Line14: Please include in the text the catalog number for the Magnetic Agarose Beads

- Pg19Line16: Please include in the text the catalog number for the GFP-Trap Magnetic Agarose Beads

Response: We have added the catalog numbers for the complete protease inhibitor (4693116001), control magnetic agarose beads (bmab), and GFP-Trap magnetic agarose beads (gtma).

- Pg19Line21: Please note in the text which primary antibodies and secondary antibodies from Supp Table 1

- Pg19Line21-22: Please include in the text the catalog number for the ECL Prime

Response: We thank the reviewer for the helpful suggestions. The description regarding immunoblotting (“Eluted samples were separated by SDS–PAGE, transferred to PVDF membranes…”) was reorganized: overlapping content has been removed, and the necessary information has been integrated into the “Immunoblotting” section, where details of the primary and secondary antibodies (listed in Supplementary Table 1) are already provided. In addition, the information for ECL Prime has been updated to “Amersham ECL Prime (RPN2236; Cytiva, Tokyo, Japan)”.

- Pg20Line2: Please include the version number for Xcalibur

Response: The version of Xcalibur used in this study (version 4.0.27.19) has been added to the text.

- Pg20Line5: Please cite in the text the reference paper for SWISS-PROT (Bairoch and Apweiler 1999 Nucleic Acid Research PMID: 9847139)

Response: The reference paper for SWISS-PROT (Bairoch and Apweiler, 1999, Nucleic Acids Research, PMID: 9847139) has been cited in the text.

- Pg19Line26: Please include in the text the catalog number for the NuPAGE gels

- Pg19Line28: Please include in the text the catalog number for the SimpleBlue SafeStain

Response: Both catalog numbers have been added in the Mass spectrometry section as follows: 4–12% NuPAGE gels (NP0321PK2; Thermo Fisher Scientific) and SimplyBlue SafeStain (LC6060; Thermo Fisher Scientific).

- Pg20Line26: Please include in the text the catalog number for the Chromium Singel Cell 3' Reagent Kits v3

Response: The catalog number for the Chromium Single Cell 3′ Reagent Kits v3 (PN-1000075; 10x Genomics) has been added to the text.

- Pg21Line3: Please cite in the text the reference paper for R (R Core Team 2021 R Foundation for Statistical Computing "R: A Language and Environment for Statistical Computing")

Response: The reference for R (R Core Team, 2021. R: A Language and Environment for Statistical Computing. R Foundation for Statistical Computing, Vienna, Austria) has already been cited in the “Histological analysis” section, where ANOVA analysis is described.

- Pg21Line3 Please cite in the text the reference for RStudio (Posit team (2025). RStudio: Integrated Development Environment for R. Posit Software, PBC, Boston, MA. URL http://www.posit.co/.)

Response: The reference for RStudio (Posit team, 2025. RStudio: Integrated Development Environment for R. Posit Software, PBC, Boston, MA, USA. URL: http://www.posit.co/) has been added to the text.

- Pg21Line23: Please include the version number for Metascape

Response: The version of Metascape used in this study (v3.5.20250701) has been added to the text.

- SuppFig12: please update the legend to include a description after the title and update the figure labeling to correspond to the legend. Also, this figure is currently not referenced anywhere in the text.

Response: We have updated the legend for Supplemental Figure 12 (Supplemental Figure 13) to include a descriptive sentence after the title and have adjusted the figure labeling to match the legend. The revised legend now reads: “Full-scan images of the agarose gels shown in Supplemental Figs. 1B and 2C are displayed in the upper and lower left panels, respectively, while the corresponding full-scan images of the immunoblots shown in Supplemental Figs. 1C and 2D are presented in the upper and lower right panels, respectively.”

As these images serve as source data, they are not referenced directly in the main text.

_Referee cross-commenting_

I generally agree with Reviewer 1 and specifically concur related to adding details about fertility assessment of the Map7 Knockout line, and enhancing the SEM imaging.

Response: As noted in our response to Reviewer #1, we have re-acquired the SEM images in high-resolution mode, focusing on the relevant regions. The new high-resolution images have replaced the original panels in revised Figure 3C, providing clearer visualization of junctional structures at P10 and P21 in Map7+/- and Map7-/- testes. The original Figure 3C images have been moved to Supplemental Figure 4B for reference.

Reviewer #2 (Significance):

There are mouse lines, and datasets that will be useful resources to the field. This work also advances our understanding of a period in Sertoli cell development that is critical to fertility but very understudied.

Response: We thank the reviewer for the positive comments and for recognizing the potential value of our mouse lines and datasets to the field, as well as the significance of our work in advancing the understanding of this critical but understudied period in Sertoli cell development.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript the authors evaluate the role of Microtubule Associated Protein 7 (MAP7) in postnatal Sertoli cell development. The authors build two novel transgenic mouse lines (Map7-eGFP, Map7 knockout) which will be useful tools to the community. The transgenic mouse lines are used in paired advanced sequencing experiments and advanced imaging experiments to determine how Sertoli cell MAP7 is involved in the first wave of spermatogenesis. The authors identify MAP7 as an important regulator of Sertoli cell polarity and junction formation with loss of MAP7 disrupting intracellular microtubule and F-actin arrangement and Sertoli cell morphology. These structural issues impact the first wave of spermatogenesis causing a meiotic delay that limits round spermatid numbers. The authors also identify possible binding partners for MAP7, key among those MYH9.

The authors did a great job building a complex multi-modal project that addressed the question of MAP7 function from many angles. The is an excellent balance of using many advanced methods while still keeping the project narrowed, to use only tools to address the real questions. The lack of quality testing on the germ cells outside of TUNEL is disappointing, but the Conclusion section implies that this sort of work is being done currently so the omission in this manuscript is acceptable. However, there is an issue with the imaging portion of the work on MYH9. The conclusions from the MYH9 data is currently overstated, super-resolution imaging of Map7 knockouts with microtubule and F-actin stains, and imaging that uses MYH9 with either Map7-eGFP or anti-MAP7 are also needed to both support the MAP7-MYH9 interaction normally and lack of interaction with failure of MYH9 to localize to microtubules and F-actin in knockouts. Since a Leica SP8 was used for the imaging, using either Leica LIGHTNING or just higher magnification will likely be the easiest solution.

This manuscript is nicely organized with almost all of the results spelled out very clearly and almost always paired with figures that make compelling and convincing support for the conclusions. There are minor revision suggestions for improving the manuscript listed below. These include synching up Figure and Supplemental Figure reference mismatches. There are also many minor, but important, details that need to be added to the Methods section including many catalog numbers and some references.

• Some of the imaging, especially Fig4F could benefit and be more convincing with super-resolution imaging in the 150nm range (SIM, Airyscan, LIGHTNING, SoRa) possibly even just imaging with a higher magnification objective (60x or 100x)
• SuppFig1D: Please add context in the legend to the meaning of the Yellow Stars and "O->U" labels. The latter would seem to be to indicate the Ovarian and Uterine sides of the image
• Pg6Line7: ¿up to P23 or up to P35?
• SuppFig4B: ¿Does SuppFig4B reference back to Fig3B or Fig3C? If the latter please update this in the legend.
• Pg7Line21-23: ¿Is SuppFig3D,E meant to be referenced and not SuppFig5A,B?
• Pg8Line22-25: ¿Is SuppFig4A meant to be reference and not SuppFig5?
• Pg8Line34-Pg9Line: ¿Is SuppFig4B meant to be reference and not SuppFig5B?
• Pg9Line28-33: ¿Would the authors be willing to rework this figure to include images that more closely match the reported findings? The current version does not strongly support the idea that MYH9 fails to localize to microtubule and F-actin domains in Map7 knockout P17 seminiferous tubules. This could also just be a matter of acquiring these images at a higher magnification or with a lower-end (150nm range) super-resolution system (SIM, Airyscan, LIGHTNING, SoRa etc)
• SuppFig7A: The legend notes these are P23 samples but the image label says 8W. Please update this to whichever is the correct age.
• Pg16Line4-5: Please include in the text the vendor and catalog number for the C57BL/6 mice
• Pg16Line18-19: Please include in the text the catalog number for the DMEM
• Pg16Line19-20: Please include in the text the vendor and catalog number for the FBS
• Pg16Line20: Please include in the text the vendor and catalog number for the Pen-Strep
• Pg17Line6-12: Thank you for including organized and detailed information about the primers, please also define the PCR protocol used including temperatures, timing, and cycles for Map7 knockout genotyping
• Pg17Line20-27: Thank you for including organized and detailed information about the primers, please also define the PCR protocol used including temperatures, timing, and cycles for Map7-eGFP genotyping
• Pg17Line30: Please include in the text the vendor and catalog number for the Laemmli sample buffer
• Pg17Line32&SuppTable1: Thank you for including an organized and detailed table for the primary antibodies used, please also make either a similar table or expand the current table to include secondary antibody information
• Pg17Line32: Please note in the text which primary antibodies and secondary antibodies from Supp Table 1
• Pg18Line2: Please include in the text the vendor and catalog number for the Bouin's
• Pg18Line3: Please include in the text the catalog number for the CREST-coated glass slides
• Pg18Line7: Please include in the text the catalog number for the OCT compound
• Pg18Line11: Please include in the text the vendor and catalog number for the Donkey Serum
• Pg18Line11: Please include in the text the vendor and catalog number for the Goat Serum
• Pg18Line13: Thank you for including an organized and detailed table for the primary antibodies used, please also make either a similar table or expand the current table to include secondary antibody information
• Pg18Line18: Please include in the text the vendor and catalog number for the DAPI
• Pg18Line19: Please also include information about the objectives used including catalog numbers, detectors used (PMT vs HyD)
• Pg18Line23: Please cite in the text the reference paper for Fiji (Schindelin et al. 2012 Nature Methods PMID: 22743772) and note the version of Fiji used
• Pg18Line24: Please note the version of Aivia used
• Pg18Line25: If possible, please use a more robust and reliable system than Microsoft Excel to do statistics (Graphpad Prism, Stata, R, etc), if this is not possible please note the version of Microsoft Excel used
• Pg18Line25: Please cite in the text the reference paper for R (R Core Team 2021 R Foundation for Statistical Computing "R: A Language and Environment for Statistical Computing") and not ethe version of R used
• Pg18Line25: ¿Please clarify, was a R package called "AVNOVA" used to do ANOVA or is this a typo?
• Pg18Line25: Please note the specific R package with version used to do ANOVA, and cite in the text the reference for this package
• Pg18Line32: Please include in the text the catalog number for the EPON 812 Resin
• Pg19Line3: Please include the version number for Stacker Neo
• Pg19Line5: Please include the vendor and version number for Amira 2022
• Pg19Line5: Please include the version number for Microscopy Image Browser
• Pg19Line5: Please include the version number for MATLAB that was used to run Microscopy Image Browser
• Pg19Line: 9-10: Please include in the text the catalog number for the complete protease inhibitor
• Pg19Line14: Please include in the text the catalog number for the Magnetic Agarose Beads
• Pg19Line16: Please include in the text the catalog number for the GFP-Trap Magnetic Agarose Beads
• Pg19Line21: Please note in the text which primary antibodies and secondary antibodies from Supp Table 1
• Pg19Line21-22: Please include in the text the catalog number for the ECL Prime
• Pg20Line2: Please include the version number for Xcalibur
• Pg20Line5: Please cite in the text the reference paper for SWISS-PROT (Bairoch and Apweiler 1999 Nucleic Acid Research PMID: 9847139)
• Pg19Line26: Please include in the text the catalog number for the NuPAGE gels
• Pg19Line28: Please include in the text the catalog number for the SimpleBlue SafeStain
• Pg20Line26: Please include in the text the catalog number for the Chromium Singel Cell 3' Reagent Kits v3
• Pg21Line3: Please cite in the text the reference paper for R (R Core Team 2021 R Foundation for Statistical Computing "R: A Language and Environment for Statistical Computing")
• Pg21Line3 Please cite in the text the reference for RStudio (Posit team (2025). RStudio: Integrated Development Environment for R. Posit Software, PBC, Boston, MA. URL http://www.posit.co/.)
• Pg21Line23: Please include the version number for Metascape
• SuppFig12: please update the legend to include a description after the title and update the figure labeling to correspond to the legend. Also, this figure is currently not referenced anywhere in the text.

Referee cross-commenting

I generally agree with Reviewer 1 and specifically concur related to adding details about fertility assessment of the Map7 Knockout line, and enhancing the SEM imaging.

Significance

There are mouse lines, and datasets that will be useful resources to the field. This work also advances our understanding of a period in Sertoli cell development that is critical to fertility but very understudied.

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

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Referee #1

Evidence, reproducibility and clarity

Summary:

A previous study by Komada et al. demonstrated that MAP7 is expressed in both Sertoli and germ cells, and that Map7 gene-trap mutant mice display disrupted microtubule bundle formation in Sertoli cells, accompanied by defects in spermatid manchettes and germ cell loss. In the current study, Kikuchi et al. investigated the role of MAP7 in the formation of the Sertoli cell apical domain during the first wave of spermatogenesis. They generated a GFP-tagged MAP7 mouse line and demonstrated that the endogenous MAP7 protein localizes to the apical microtubules in Sertoli cells and to the manchette microtubules in step 9-11 spermatids. They also generated a new Map7 knockout (KO) mouse line in a genetic background distinct from the one used in the previous study. Focusing on stages before the emergence of step 9-11 spermatids, the authors aimed to isolate defects caused by the function of MAP7 in Sertoli cells. They report that loss of MAP7 impairs Sertoli cell polarity and apical domain formation, accompanied by the microtubule remodeling defect. Using the GFP-tagged MAP7 line, they performed immunoprecipitation-mass spectrometry and identified several MAP7-interacting proteins in the testis, including MYH9. They further observed that MAP7 deletion alters the distribution of MYH9. Single-cell RNA sequencing revealed that the loss of MAP7 in Sertoli cells resulted in slight transcriptomic shifts but had no significant impact on their functional differentiation. Single-cell RNA sequencing analysis also showed delayed meiotic progression in the MAP7-deficient testis. Overall, while the study provides some interesting discoveries of early Sertoli cell defects in MAP7-deficient testes, some conclusions are premature and not fully supported by the presented data. The mechanistic investigations remain limited in depth.

Major comments:

• Although the infertility phenotype of the Map7 gene-trap mutant mice has been reported previously, it remains essential to assess fertility in this newly generated MAP7 knockout line. While the authors present testis size and histological differences between WT and KO mice (Extended Fig. 2e and 2f), there is no corresponding description or interpretation in the main text regarding fertility outcomes.
• In Figure 2C, the authors identified Sertoli cells, spermatogonia cells, and spermatocytes using SEM, based on their cell morphology and adhesion to the basement membrane. Given that the loss of MAP7 disrupts the polarity and architecture of Sertoli cells, the position of germ cells will be affected, making this identification criterion less reliable.
• In Figure 2e, the number of Sox9-positive Sertoli cells in MAP7 knockout mice appears higher than that in the control at P17. Quantification of total Sox9-positive cells should be done to determine whether MAP7 deletion increases Sertoli cell numbers.
• To determine whether MAP7's role in regulating Sertoli cell polarity relies on germ cells, the authors treated mice with busulfan at P28 to delete germ cells, a stage after Sertoli cell polarity defect has developed in MAP7 knockout mice. This data is insufficient to support the conclusion that MAP7 regulates Sertoli cell polarity independently of the presence of germ cells. Germ cell deletion should be done before the Sertoli cell defect develops to address this question.
• The resolution of the SEM images in Figure 3c is insufficient to evaluate tight and adherens junctions clearly. As such, these images do not convincingly support the claim that adherens junctions are absent in the KO testes.
• GFP-tagged reporter mice and HeLa cells were used for immunoprecipitation-mass spectrometry to identify proteins that interact with MAP7. Given that the authors aimed to elucidate the mechanism by which MAP7 regulates Sertoli cell cytoskeleton organization, the rationale for including HeLa cells is unclear and should be better justified or reconsidered.
• The authors observed that MYH9, one of the MAP7-interacting proteins, does not colocalize with ectopic microtubule and F-actin structures in MAP7 KO testes and concluded that MAP7 facilitates the integration of microtubules and F-actin via interaction with NMII heavy chains. This conclusion is speculative and not adequately supported by the presented data.
• The authors used Spearman correlation coefficients to analyze six Sertoli cell clusters and generated a minimum spanning tree to infer differentiation trajectories. However, details on the method used for constructing the tree are lacking. Moreover, relying solely on Spearman correlation to define differentiation topology is oversimplified.

Minor comments:

• Several extended data figures are redundant with main figures and do not provide additional value (e.g., Fig. 2d vs. Extended Data Fig. 3a; Fig. 2f vs. Extended Data Fig. 3d; Fig. 2C vs. Extended Data Fig. 4b; Fig. 3d vs. Extended Data Fig. 4c). The authors should consolidate or remove duplicates.
• Figure citations in the main text do not consistently match figure content. For example, on page 7 (lines 5-6), the text refers to Extended Data Fig. 4a for SOX9 staining. Yet, it is the extended Data Fig. 3a that contains the relevant data. Similarly, the reference to Extended Data Fig. 4b and 4c on page 7 (lines 7-8) for adult defects is inaccurate.
• In Figure 2e, percentages of Sertoli cells across three layers are shown. The figure legend should specify which layer(s) show statistically significant differences between WT and KO.
• The current color scheme for F-actin and TUBB3 in Figure 3 lacks sufficient contrast. Adjusting to more distinguishable colors would improve readability.
• Since multiple scale bars with different units are present within the same figures, adding units directly above or beside each scale bar would improve readability.
• It is recommended to directly mark Sertoli cells, spermatogonia, and spermatocytes on the SEM images in Figure 2C for clearer visualization.
• The quantification of Sertoli cell positioning shown in Fig. 2C is already described in the main text and is unnecessary in the figure.

Referee cross-commenting

I concur with Reviewer 2 that the Map7-eGFP mouse model is a valuable tool for the research community. I also agree that performing MAP7-MYH9 double immunofluorescence staining to demonstrate their colocalization would further strengthen the authors' conclusions regarding their interaction. My overall assessment of the manuscript remains unchanged: the study represents an incremental advance that extends previous findings on MAP7 function but provides limited new mechanistic insight.

Significance

This study investigates the role of the microtubule-associated protein MAP7 in Sertoli cell polarity and apical domain formation during early stages of spermatogenesis. Using GFP-tagged and MAP7 knockout mouse models, the authors show that MAP7 localizes to apical microtubules and is required for Sertoli cell cytoskeletal organization and germ cell development. While the study identifies early Sertoli cell defects and candidate MAP7-interacting proteins, the mechanistic insights remain limited, and several conclusions require stronger experimental support. Overall, the discovery represents an incremental advance that extends prior findings on MAP7 function, providing additional but modest insights into the role of MAP7 in cytoskeletal regulation in male reproduction.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Summary:

The manuscript titled "Unravelling the Progression of the Zebrafish Primary Body Axis with Reconstructed Spatiotemporal Transcriptomics" presents a comprehensive analysis of the development of the primary body axis in zebrafish by integrating bulk RNA-seq, 3D images, and Stereo-Seq. The authors first clearly demonstrate the application of Palette for integrating RNA-seq and Stereo-Seq using published spatial transcriptomics data of Drosophila embryos. Subsequently, they produced serial bulk RNA-seq data for certain developmental stages of Danio rerio embryos and utilized published Stereo-Seq data. Through robust validation, the authors observe the molecular network involved in AP axis formation. While the authors show that integrating bulk RNA-seq data with Stereo-Seq improves spatial resolution, additional proof is required to demonstrate the extent of this improvement.

Response: We thank the reviewer for the positive feedback on our Palette pipeline, zSTEP construction and analysis of primary body axis development. We appreciate the constructive suggestions provided, which we can implement to improve our manuscript. As pointed out by the reviewer, some analysis procedures were not described in sufficient detail. To address this, we have added more explanatory texts and additional schematic diagrams to make the methods clearer and more understandable. We also thank the reviewer for the meticulous reading and for reminding us to include parameters, references and essential texts, which significantly improve the manuscript quality and make the manuscript more rigorous. Furthermore, as suggested by the reviewer, the extent of the improvement on the spatial resolution was not clearly demonstrated in the manuscript. Therefore, we have provided an additional figure to show the original expression on the stacked Stereo-seq slices and 3D live image compared to the expression from zSTEP, and the results indicate that zSTEP provides better, more continuous expression patterns. We still have two remaining tasks that are expected to be completed within the next month. We hope our responses have address the concerns raised by the reviewer, and we are pleased to provide any additional proof as needed.

Major Comments:

1. Lines 66-68: Discuss the limitations of existing tools and explicitly state the advantages of using Palette.

Response: We thank the reviewer for the valuable suggestion. We have added the following new texts after line 68 to emphasize the features and advantages of Palette.

"Newly developed tools are committed to integrating bulk and/or scRNA-seq data with ST data to enhance spatial resolution, focusing on expression at the spot level. However, gene expression patterns are closely correlated to the biological functions and are more critical for understanding biological processes. Therefore, a tool focusing on inferring spatial gene expression patterns would be desirable."

1. Body Pattern Genes Analysis: For both Drosophila and Danio rerio, it would be valuable to examine body pattern genes in Stereo-Seq and apply Palette to determine if the resolution of the segments improves or merges. The resolution of the A-P axis is convincing, but further evidence for other segments would be beneficial.

Response: We thank the reviewer for the suggestions. For the Drosophila data, we only used two adjacent slices for Palette performance assessment, and thus were only able to evaluate the expression patterns within the slice.

For the zebrafish data, although we have construct zSTEP as a 3D transcriptomic atlas, we have to admit that the left-right (LR) and dorsal-ventral (DV) patterning is not satisfactory enough. Here we show a section from the dorsal part of 16 hpf zSTEP that displays a relatively well-defined left-right pattern (Fig. 2). Along the left-right axis, the notochord cells are centrally located, flanked by somite cells on either side, with the outermost cells being pronephros.

One reason for the limited LR and DV patterning is that the original annotation of the ST data does not clearly distinguish all the cell types. Another reason is likely due to the disordered cell positions when stacking ST slices. Thus, our zSTEP is most suitable for investigating the AP patterns, while the performances on LR and DV patterns may not achieve the same level of accuracy.

See response letter for the figure.

1. Figure 2d: Include the A-P line for which the intensity profile was plotted in the main figure, rather than just in the supplementary material. Additionally, consider simplifying the plot by not combining three lines into one, as it complicates the interpretation of observations.

Response: We thank the reviewer for the helpful suggestions. We have updated Figure 2d and Figure S1b by adding a A-P line on each subfigure (Fig. 3). Additionally, as the reviewer suggested, we have separated the intensity plots so that each subfigure now includes a dedicated intensity plot along A-P axis.

See response letter for the figure.

1. Drosophila Data Analysis: While the alignment and validation of Danio rerio sections are clearly explained, the analysis and validation of Drosophila data are insufficiently detailed. Provide a more thorough explanation of how the intensity profiles between BDGP in situ data and Stereo-Seq data are adjusted.

Response: We thank the reviewer for raising this issue. To make the analysis procedure clearer, we have updated Figure 2a (Fig. 4) and added explanatory texts in the figure legends to describe the processing procedure for the Drosophila ST data.

See response letter for the figure.

Additionally, the following sentences have been added into the Methods section to describe the generation of the intensity profiles.

"The intensity plot profiles along AP axis were generated through the following steps: The expression pattern plot images or in situ hybridization images were imported into ImageJ and converted to grayscale. The colour was then inverted, and a line of a certain width (here set as 10) was drawn across from the anterior part to the posterior part (Fig. S1a). The signal intensities along the width of the line were measured and imported into R for generating intensity plots."

1. Figure 3d: Present a plot with the expected expression profiles of the three genes if the embryo is aligned as anticipated.

Response: We thank the reviewer for this helpful suggestion, which improves the clarity of our manuscript. We have added the following subfigure in as Figure 3d (Fig. 5) to show the expected expression profiles of the three midline genes along left-right axis.

See response letter for the figure.

1. Analysis Without Palette: Between lines 277-438, the outcome of using Palette with bulk RNA-seq and Stereo-Seq is convincing. However, consider the following:

o What would be the observations if the analysis were conducted solely with Stereo-Seq data, without incorporating bulk RNA-seq data and employing Palette?

Response: We thank the reviewer for raising this important question. Here we show the comparison of ST expression on stacked Stereo-seq slices, ST expression projected on 3D live images, and the Palette-inferred expression (Fig. 6). The stacked ST slices do not fully reflect the zebrafish morphology, and the gene expression appears sparse, making it look massive (the first row). While after projecting ST expression onto the live image, the expression patterns can be observed on zebrafish morphology, but the expression is still sparsely distributed in spots (the second row). However, the expression patterns captured by Palette in zSTEP show more continuous expression patterns (the third row), which are more similar to the observations in in situ hybridization images (the fourth row). We are considering put these analyses into the supplementary figure.

See response letter for the figure.

o This study uses only Stereo-Seq as the spatial transcriptomics reference. It would strengthen the argument to use at least one other spatial transcriptomics method, such as Visium or MERFISH, in conjunction with bulk RNA-seq and Palette, to demonstrate whether Palette consistently improves gene expression resolution.

Response: We thank the reviewer for raising this professional question. To demonstrate a broad application of Palette, it would be necessary to test Palette performance using different types of ST references. We plan to perform extra analyses to evaluate Palette performance using Visium and MERFISH data as ST references, respectively. Additionally, our Palette pipeline only takes the overlapped genes for inference. As only hundreds of genes can be detected by MERFISH, Palette can only infer the expression patterns of these genes. As mentioned in the work of Liu et al. (2023), MERFISH can independently resolve distinct cell types and spatial structures, and thus we believe Palette will also show great performance when using MERFISH as ST reference. We've already started the analyses and expect to accomplish it within the next month. And we will update the analyses as separated tutorials to the GitHub repository.

Reference:

Liu, J. et al. Concordance of MERFISH spatial transcriptomics with bulk and single-cell RNA sequencing. Life Sci Alliance 6 (2023).

1. PDAC Data Analysis: Provide a more detailed explanation of the PDAC data analysis and use appropriate colors in the tissue images to clearly distinguish cell types.

Response: We thank the reviewer for the suggestions. We have updated the colours used in the tissue images to be consistent to the colours in tissue clustering analysis. Additionally, we have added an additional subfigure in supplementary figure (Fig. 7) with more explanatory texts in the figure legends to provide a more thorough explanation for the analysis.

See response letter for the figure.

1. Comparison with Other Methods: State the limitations of not using STitch3D and Spateo for alignment and explain why these methods were not employed.

Response: We thank the reviewer for raising this constructive comment. We fully agree with you that the introduction of published alignment algorithms would be helpful in our analysis. Currently, the slice alignment is adjusted manually, and thus the main limitation of not using these tools is that manual operation may induce bias compared to the alignment generated by computational algorithm. Unfortunately, STitch3D and Spateo are not included in this study because of two reasons. First, these two newly developed tools have been recently posted, and our analyses were largely completed before that. Therefore, we only mentioned these tools in the Discussion section. Second, we do not want to embed too many external tools into our analysis, which may increase the difficulties for researchers' operation. Specifically, STitch3D and Spateo are configured to run in Python environment, while Palette is based on R packages. Moreover, without these tools, our current manual alignment also achieves desired performance. However, we value this enlightening suggestion by the reviewer and therefore plan to further compare the performance of manual alignment versus the mentioned two alignment tools. At present, we have a preliminary comparison scheme and collected relevant datasets. Hopefully, we will complete this analysis within the next 1 to 2 weeks.

Minor Comments:

1. References: Add references to the statements in lines 51-53.

Response: We thank the reviewer for reminding us of the missing references. We have added the works of Junker et al. (2014), Liu et al. (2022), Chen et al. (2022), Wang et al. (2022), Shi et al. (2023) and Satija et al. (2015) as references in line 53 as follows.

"Thus, great efforts are ongoing to construct gene expression maps of these models with higher resolution, depth, and comprehensiveness1-6."

References:

1. Junker, J.P. et al. Genome-wide RNA Tomography in the zebrafish embryo. Cell 159, 662-675 (2014).
2. Liu, C. et al. Spatiotemporal mapping of gene expression landscapes and developmental trajectories during zebrafish embryogenesis. Dev Cell 57, 1284-1298 e1285 (2022).
3. Chen, A. et al. Spatiotemporal transcriptomic atlas of mouse organogenesis using DNA nanoball-patterned arrays. Cell 185, 1777-1792 e1721 (2022).
4. Wang, M. et al. High-resolution 3D spatiotemporal transcriptomic maps of developing Drosophila embryos and larvae. Dev Cell 57, 1271-1283 e1274 (2022).
5. Shi, H. et al. Spatial atlas of the mouse central nervous system at molecular resolution. Nature 622, 552-561 (2023).
6. Satija, R. et al. Spatial reconstruction of single-cell gene expression data. Nature biotechnology 33, 495-502 (2015)

1. Scientific Name Consistency: Ensure consistency in using either "Danio rerio" or "zebrafish" throughout the manuscript.

Response: We thank the reviewer for this suggestion. We have changed "Danio rerio" to "zebrafish" to make "zebrafish" consistent throughout the manuscript.

1. Related References: Include the following relevant references:

o https://academic.oup.com/bib/article/25/4/bbae316/7705532

o https://www.life-science-alliance.org/content/6/1/e202201701

Response: We thank the reviewer for bringing these two relevant works to us. Baul et al. (2024) presented STGAT leveraging Graph Attention Networks for integrating spatial transcriptomics and bulk RNA-seq, and Liu et al. (2023) demonstrated the concordance of MERFISH ST with bulk and single-cell RNA-seq. Both are excellent works and relevant to our work. We have added these two references in line 61 and line 68, respectively.

References:

Baul, S. et al. Integrating spatial transcriptomics and bulk RNA-seq: predicting gene expression with enhanced resolution through graph attention networks. Brief Bioinform 25 (2024).

Liu, J. et al. Concordance of MERFISH spatial transcriptomics with bulk and single-cell RNA sequencing. Life Sci Alliance 6 (2023).

1. Figure 1a: In the Venn diagram, include the number of genes in the bulk and Stereo-Seq datasets, as well as the number of overlapping genes.

Response: We thank the reviewer reminding us to include these important numbers. And in our current manuscript, we have added the following sentences in the Methods section to provide the gene numbers (Fig. 8). While the Venn diagram in Figure 1a serves as a schematic representation, so we did not include the gene numbers, as these may vary depending on the actual data.

"Palette was performed on the aligned slices using the overlapped genes. For the 10 hpf embryo, there were 24,658 genes in the bulk data, 18,698 genes in the Stereo-seq data, and 16,601 overlapped genes. For the 12 hpf embryo, there were 23,018 genes in the bulk data, 18,948 genes in the Stereo-seq data, and 16,401 overlapped genes. For the 16 hpf embryo, there were 24,357 genes in the bulk data, 23,110 genes in the Stereo-seq data, and 19,539 overlapped genes."

See response letter for the figure.

1. Figure 1 Improvement: Enlarge Figure 1 and reduce repetitive elements, such as parts of the deconvolution and Figure 1b.

Response: We thank the reviewer for the helpful suggestion. We agree with the reviewer that the deconvolution sections appear repetitive. We have updated Figure 1 (Fig. 9) by replacing these repetitive elements with a clearer and simpler diagram.

See response letter for the figure.

1. Figure 3f: Explain the black discontinuous line in the plot.

Response: We thank the reviewer for the reminder. We are sorry about the lack of the explanation. We have added the below explanation for the black discontinuous line in the legend of Figure 3 (Fig. 10) as follows.

See response letter for the figure.

1. Line 610: State the percentage of unpaired imaging spots.

Response: We thank the review for the reminder. We are sorry about not including the paired and unpaired spot number. We have added the number of paired spots with the percentage in the total spots in the Method section as follows.

"The numbers of mapped spots for the 10 hpf, 12 hpf and 16 hpf embryos are 15,379 (69.4% of the total spots), 14,697 (70.5% of the total spots) and 21,605 (77.2% of the total spots), respectively."

1. Lines 616-618: Specify the unit for the spot diameter.

Response: We thank the reviewer for the reminder. Again, we are sorry about not including the spot diameter information in our previous version of manuscript. We have added the spot diameter in Method section as follows.

"In the Stereo-seq data, each spot contained 15 × 15 DNA nanoball (DNB) spots (The diameter of each spot is near 10 μm)."

Reviewer #1 (Significance):

This algorithm will be useful not only for the field of developmental biology but also for wider applications in spatial omics. Although I have expertise in spatial omics technology development, my understanding of computational biology is limited, which restricts my ability to fully evaluate the Palette algorithm presented in this paper.

Response: We thank the reviewer for recognizing our work, and we greatly appreciate the constructive suggestions from the reviewer. Although the reviewer acknowledged limited expertise in computational biology, the comments from the reviewer are highly professional and valuable. Following the suggestions from the reviewer, we have not only included more explanatory texts and figures to make the analysis procedures clearer and more understandable, but also supplemented the important parameters that were missing in our previous manuscript. We also provided extra figure to demonstrate the improvements of zSTEP on gene expression patterns. We believe that our work is now more scientific and more understandable, and we will continue working to solve the remaining issues as planned. We express our thanks for the reviewer again.

Reviewer #2 (Evidence, reproducibility and clarity):

The authors of the study introduce the Palette method, a novel approach designed to infer spatial gene expression patterns from bulk RNA-sequencing (RNA-seq) data. This method is complemented by the development of the DreSTEP 3D spatial gene expression atlas of zebrafish embryos, establishing a comprehensive resource for visualizing gene expression and investigating spatial cell-cell interactions in developmental biology.

Response: We sincerely appreciate the reviewer's positive feedback on our Palette pipeline and the zSTEP 3D spatial expression atlas of zebrafish embryos. We also thank the reviewer for the professional comments and constructive suggestions. The reviewer raised the concerns from the aspect of algorithm design and computational biology, which we did not address well in our previous manuscript. We agree with the reviewer that we did not clarify the selection criteria of the parameters in detail, and we are now working on the additional analyses to address this issue.

We also agree with the reviewer that we did not provide enough discussion of the strategies used in the pipeline, the features of Palette and the application scenarios of Palette and zSTEP. For wide use of our tools, it is significantly important to state these aspects. In this revised version, we have added more paragraphs in the Discussion section to address this issue. Additionally, we acknowledge that we did not adequately demonstrate the computational efficacy and computational requirements, which are important for researchers. We are also working on the additional analyses to address this issue.

Finally, we thank the reviewer again for the professional and constructive suggestions. These suggestions are addressable, and by following them, we believe our manuscript will see a significant improvement, especially in the Palette pipeline part, making the pipeline more rigorous and easier to access. We are confident that we can complete the planned additional tasks within the next 1-2 months.

1. The efficacy of the Palette method may be compromised by its dependency on the quality of the reference spatial transcriptomics data. As highlighted in the study, variations in data quality can lead to significant challenges in reconstructing accurate spatial expression patterns from bulk data. This underscores the necessity of evaluating quality parameters, such as the number of gene detections and spatial resolution, to ensure reliable outcomes. Additional studies should rigorously assess how these quality factors influence the accuracy and efficiency of the algorithm in various data contexts, particularly under diverse conditions of gene detection.

Response: We thank the reviewer for this valuable suggestion. We agree with the reviewer that the quality of the reference ST data may greatly influence the performance and efficacy of the Palette, and we have added paragraphs in the Discussion section to further discuss the impact of ST data quality on Palette performance. As mentioned by the reviewer, gene detections and spatial resolution are two important parameters that can influence the Palette performance. Low gene detection may impact the clustering process, making the cell types of spots not distinguished well. To evaluate the performance of Palette when ST data shows low gene detection, we plan to applied Palette using MERFISH data as the ST reference, which only captures hundreds of genes. Moreover, we will also investigate the impact of spatial resolution on Palette performance by merging ST spots to simulate lower resolution scenarios, as well as the impact of gene detection by randomly reducing detected genes. Through the comparison among the inferred expression patterns with ST data of different spatial resolutions or different numbers of detected genes, we can better access the performance of Palette and provide guidance to researchers on the appropriate ST data requirements for optimal performance. These analyses will take another one month to accomplish after this round of revision due to the limited response time.

1. The methodology raises pertinent questions regarding how the clustering results from different algorithms may affect the reconstructions by the Palette method. The authors would better provide a detailed discussion/comparison of clustering processes that optimize the reconstruction of spatial patterns, ensuring precision in the downstream analyses.

Response: We thank the reviewer for the constructive comments. We agree with the reviewer that the differences in clustering results would impact the inference of the Palette. In our Palette pipeline, rather than develop a new methodology for clustering, we employ the BayesSpace for spot clustering, which considers both spot transcriptional similarity and neighbouring structure for clustering. In this case, researchers may adjust the parameters in the BayesSpace package to achieve optimal clustering results. Actually, in most cases, the spot identities were achieved through UMAP analysis, which only considers the transcriptional differences but does not consider the spatial information. This kind of clustering strategy will potentially lead to an intricate arrangement of spots belonging to different clusters, and may result in sparse gene expression in Palette outcome, which is different from the patterns in bona fide tissues. Therefore, a suitable clustering strategy will definitely help capture the local patterns.

Moreover, our Palette pipeline also can use the clustering results from the tissue histomorphology. Using tissue histomorphology for clustering would be a good choice, as it is closer to the real case. The following Figure (Fig. 11) displays the Palette performance on PDAC datasets using both spatial clustering and histomorphology clustering strategies. The result using histomorphology clustering captures the weak pattern (indicated by the red circle) that were missed when using the spatial clustering (Fig. 11d).

See response letter for the figure.

1. The choice to utilize only highly expressed genes in the initial stages of the Palette algorithm also warrants further exploration. Addressing the criteria for determining which genes qualify as "highly expressed" and outlining robust cutoff will enhance the algorithm's rigor and applicability. Similarly, in the iterative estimation of gene expression across spatial spots, establishing optimal iteration conditions is crucial. Implementing a loss function may offer a systematic method for concluding iterations, thus refining computational efficiency.

Response: We thank the reviewer for the professional suggestions. As pointed out by the reviewer, the selection of highly expressed genes and the iteration times are two important parameters in our pipeline. The definition of highly expressed genes and the number of highly expressed genes are important for achieving a satisfactory clustering performance. We tested the impact of different numbers of highly expressed genes on cluster performance in our preliminary analyses, while we did not summarize these tests and specify the parameters. Therefore, we plan to include a supplementary figure showing the clustering performances under different definitions of highly expressed genes and different numbers of highly expressed genes. Additionally, for the iteration conditions, we have tested different iteration numbers to find out a suitable iteration number to achieve a stable expression in each spot. The following figure (Fig. 1) shows the results after performing Palette with different iteration times. We randomly selected 20 cells and compared their expression across tests with varying iteration times. The results indicate that for a ST dataset with 819 spots, the expression in each spot becomes nearly stable after 5000 iteration times. We previously did not consider the computational efficiency, while here the reviewer raises a valuable and professional suggestion to implement a loss function to determine the optimal number of iterations. We greatly appreciate this suggestion, and plan to apply a loss function to summarize the optimal iteration times for ST datasets of different sizes. This will provide guidance for potential researchers in selecting iteration times and enhance computational efficiency.

See response letter for the figure.

1. Performance metrics relating to processing speed and computational demands remain inadequately addressed in the current framework. Understanding how the Palette method scales across varying gene counts and bulk RNA-seq datasets will be essential for potential applications in larger biological contexts. Notably, the quantitative demands of analyzing 20,000 genes when processing 10, 100, or 1,000 bulk RNA profiles must be articulated to guide researchers in planning accordingly.

Response: We thank the reviewer for this valuable and professional suggestion. In our previous analyses, we did not consider the computation efficiency, processing speed and computational demands, which are important information for potential researchers. To address this issue, we will list our computer configuration first. And under this configuration, we plan to run Palette on datasets with different numbers of overlapped genes or ST references with varying spot numbers, and then summarize the running times into a metrics table. This will help researchers estimate the running time for their datasets and guide them in planning the analyses. We will begin the analyses soon and expect to complete the analysis within the next 1 to 2 months.

Minor opinions:

1. Despite the promising advances offered by the zebrafish 3D reconstruction, there is a lack of details regarding numbers of the spatial transcriptomics (ST) data utilized, and the number of bulk RNA-seq data employed in the analyses. These parameters need to be clarified.

Response: We thank the reviewer for reminding us of these parameters. We are sorry for not including these parameters in our previous manuscript. We have now included the numbers of bulk, ST and overlap genes in the Methods section as follows (Fig. 12).

"Palette was performed on the aligned slices using the overlapped genes. For the 10 hpf embryo, there were 24,658 genes in the bulk data, 18,698 genes in the Stereo-seq data, and 16,601 overlapped genes. For the 12 hpf embryo, there were 23,018 genes in the bulk data, 18,948 genes in the Stereo-seq data, and 16,401 overlapped genes. For the 16 hpf embryo, there were 24,357 genes in the bulk data, 23,110 genes in the Stereo-seq data, and 19,539 overlapped genes."

See response letter for the figure.

1. Issues regarding spatial cell-cell communication, especially concerning interactions over longer distances, necessitate careful consideration. Introducing spatial distance constraints could help formulate more realistic models of cellular interactions, a vital aspect of embryonic development.

Response: We thank the reviewer for this essential comment. We agree with the reviewer that the spatial distance is an essential factor to investigate in vivo cell-cell communication during embryonic development. Therefore, in our analyses, we employed CellChat for spatial cell-cell communication analysis, which can be used to infer and visualize spatial cell-cell communication network for ST datasets, considering the spatial distance as constrains of the computed communication probability. However, during our analyses, we observed that there were interactions between cell types over longer distances, as mentioned by the reviewer. We then investigated how these interactions of longer distances occurred. Here, we show the FGF interaction between tail bud and neural crest cells from our spatial cell-cell analysis as an example, and the distance between these two cell types appears quite significant (Fig. 13). We labelled tail bud cells and neural crest cells on the selected midline section and observed that, although most neural crest cells are distributed anteriorly, a small number of neural crest cells are located at tail, close to the tail bud cells. Therefore, the observed interaction between tail bud and neural crest cells is likely due to their adjacent distribution in the tail region, while the anteriorly distributed of neural crest spot in spatial cell-cell communication analysis reflects the anterior positioning of most neural crest cells. As a result, the distances shown on the spatial cell-cell communication analysis are not the real distance between two cell types.

In most cases in our spatial cell-cell communication analyses, the observed interactions over longer distances are likely influenced by this visualization strategy. Additionally, pre-processing the dataset may enhance the performance of the analyses. Here we performed systematic analyses of the entire embryo, which can make the interactions between cell types appear massive. To investigate specific biological questions, researchers can subset cell types of interest or categorize them into different subtypes based on their positions.

See response letter for the figure.

1. Evaluation metrics such as the Adjusted Rand Index (ARI) and Root Mean Square Error (RMSE) represent critical tools for systematically measuring the similarity of inferred spatial patterns, yet their specific application within this context should be elaborated.

Response: We thank the reviewer for recommending these two tools. We have applied them to evaluate the similarity between the expression patterns (Fig. 14). The inclusion of these statistical values makes our comparisons of expression patterns more scientific and convincing. And we have added the following texts in the Methods section to describe the calculation of these two values.

"The Adjusted Rand Index (ARI) and Root Mean Square Error (RMSE) were used to evaluate the similarity of the expression patterns. The expression patterns of in situ hybridization images were considered as the expected values, and the expression patterns of ST data and inferred expression patterns were compared to the expected values. Common positions along the AP axis within all three expression profiles were used, and the RMSE were calculated based on the scaled intensity of these positions. Values greater than the threshold were set to 1; otherwise, they were set to 0, and the ARI was then calculated based on the intensity category. Higher ARI and lower RMSE indicate greater similarity."

See response letter for the figure.

1. The study's limitations surrounding ST data quality cannot be overstated. Discussing scenarios where only limited or poor-quality ST data are available will be crucial for guiding future studies. Furthermore, a clear explanation of how enhanced specificity and accuracy translate into tangible biological insights is essential for demystifying the underlying mechanisms driving developmental processes.

Response: We thank the reviewer for raising this essential suggestion. We have realized that in our previous manuscript, our discussion on the advantages and limitations of Palette and zSTEP was neither broad nor detailed enough.

Therefore, in our revised manuscript, we have added the following paragraphs to further discuss the advantages and limitations of Palette and zSTEP, as well as the potential application of zSTEP in developmental biology.

In this section, we have emphasized again the impact of ST data quality on the performance of Palette and zSTEP, and then compared Palette with the strategy that uses well-established marker genes to infer spatial information. We demonstrated that although Palette cannot achieve single cell resolution, it captures the major expression patterns, which are closely correlated to biological functions and critical for embryonic development. Furthermore, we further discussed that zSTEP is not only a valuable tool for investigating gene expression patterns, but also has the potential in evaluating the reaction-diffusion model to investigate the complicated and well-choreographed pattern formation during embryonic development.

As here we have provided a more comprehensive discussion about Palette and zSTEP, we think that the potential researchers will better understand the application scenarios of our inference pipeline and our datasets. We hope our study can assist and inspire further research in the field of spatial transcriptomics and developmental biology.

"Thirdly, the performance of Palette and zSTEP heavily relied on the quality of ST data. If the quality of ST data is not of sufficient quality, the low-expression genes may not be detected or only appear in very few scattered spots, and the performance of spot clustering could also be affected. Moreover, in this study, for example, the Stereo-seq data of 12 hpf zebrafish embryo had fewer slices on the right side (Fig. S3b), resulting in more blank spots in the right part of zSTEP for the 12 hpf embryo. However, with the ongoing advancements in spatial resolution and data quality, the performance of Palette is expected to be enhanced and demonstrate even greater potential for analysing spatiotemporal gene expression.

On the other hand, compared to the brilliant strategy that infers spatial information of scRNA-seq data from well-established genes, our Palette pipeline cannot achieve single cell resolution. However, our Palette pipeline is based on the ST reference, and thus preserves the real positional relationships between spots. Furthermore, the focus of our pipeline is to infer the gene expression patterns, which are closely correlated to biological functions and critical for embryonic development, rather than the sparse expression within individual spots. In this regard, our Palette pipeline can be advantageous, as it allows for reconstruction of the major expression profiles, which are often more relevant for understanding developmental processes. Additionally, our Palette can be applied to serial sections, enabling the construction of 3D ST atlas.

Finally, while the current analyses demonstrated that zSTEP can serve as a valuable tool for identifying genes having specific patterns at certain developmental stages, the exploration of zSTEP is still limited. During animal development, pattern formation is always one of the most important developmental issues. As demonstrated by the reaction-diffusion (RD) model, morphogen molecules are produced at specific regions of the embryo, forming morphogen gradients to guide cell specification, while interactions between different morphogens instruct more complicated and well-choreographed pattern formation. Our Palette constructed zSTEP, as a comprehensive transcriptomic expression pattern during development, could be leveraged to evaluate and prove the RD model during development, including AP patterning. Moreover, the investigation of gene expression patterns should not be limited to morphogens and TFs, and further investigation of their roles in AP patterning is desirable. Additionally, here a random forest model may be sufficient for investigating the most essential morphogens and TFs for AP axis refinement, while more sophisticated machine learning models may be required for addressing more specific biological questions."

Reviewer #2 (Significance):

The Palette pipeline demonstrates a marked improvement in specificity and accuracy when predicting spatial gene expression patterns. Evaluative studies on Drosophila and zebrafish datasets affirm its enhanced performance compared to existing methodologies. By effectively reconstructing spatial information from bulk transcriptomic data, the Palette method innovatively merges the philosophy of leveraging single-cell transcriptomic data for deconvolution analyses. This integration is pivotal, advancing traditional bulk RNA-seq approaches while laying the groundwork for future research.

One of the notable achievements in this work is the construction of the DreSTEP atlas, which integrates serial bulk RNA-seq data with advanced 3D imaging techniques. This resource grants researchers unprecedented access to the visualization of gene expression patterns across the zebrafish embryo, facilitating the investigation of spatial relationships and cell-cell interactions critical for developmental processes. Such capabilities are invaluable for understanding the intricate dynamics of embryogenesis and the distinct roles of individual cell types.

Response: We thank the reviewer for the positive evaluation of our work, either the Palette pipeline or zSTEP. The reviewer has strong expertise in algorithm development and computational biology, and the concerns and suggestions from the reviewer are significantly precious and valuable for us. Regarding the bioinformatics tool development, we did not have extensive experiences, and thus we did not thoroughly address the selection criteria or clarify the parameters used in the pipeline, which may influence the application by other researchers. Therefore, we sincerely appreciate the professional suggestions from the reviewer, which we can follow to address these issues, improve our manuscript and make our work more impactful for researchers. Additionally, we did not consider computation efficiency, processing speed and computational demands, which would be important factors for other researchers to use Palette. We would like to add extra analyses to address these aspects.

Currently, based on the suggestions from the reviewer, we have added extra texts discussing the clustering strategy in Palette pipeline, the advantages and limitations of Palette, and the potential application of zSTEP in developmental biology. We believe that readers will now have a clearer understanding of the performance of Palette and the application scenarios of both Palette and zSTEP. We have not fully addressed the comments raised by the reviewer yet, while we are working on the planned additional analyses and expect to complete all these tasks within the next 1-2 months. We sincerely thank the reviewer for the professional and valuable suggestions, which definitely improve our work and will make it accessible for a wide range of researchers.

Finally, through this review process, we have learned a lot about the important considerations and requirements when designing bioinformatics tools, and we benefit a lot from the thoughtful guidance. We express our thanks to the reviewer again for the guidance, and we will try our best to address the remaining issues to further improve our manuscript.

Reviewer #3 (Evidence, reproducibility and clarity):

Evidence, reproducibility and clarity

In this study, Dong and colleagues developed a computational pipeline to use spatial transcriptomics (ST) datasets as a reference to infer the spatial patterns of gene expression from bulk RNA sequencing data. This approach aims to overcome the low read depth and limited gene detection capabilities in current ST datasets, while exploiting its ability to provide highly resolved spatial information. By combining bulk RNA-seq datasets from 3 developmental stages during early zebrafish development with previously available ST and imaging datasets, the authors build DreSTEP (Danio rerio spatiotemporal expression profiles). Using this approach, they go on to identify the morphogens and transcription factors involved in anteroposterior patterning.

The paper is well written, and the pipeline presented in this study is likely to be useful beyond the case studies included in this study. There are a few questions that, in my view, would be important to clarify to increase the impact of this work:

Response: We sincerely appreciate the positive feedback from the reviewer on the Palette pipeline and zebrafish spatiotemporal expression profiles zSTEP. We thank the reviewer for the constructive suggestions, which have inspired us to think deeply about application and advantages of Palette and zSTEP for future studies.

We fully agree with the reviewer that we do not sufficiently clarify the advantages and limitations of our inference pipeline in the original manuscript. The questions raised by the reviewer are very insightful. For example, while the inference expression patterns may closely resemble the in situ hybridization observation, which we consider as good performance, the reviewer pointed out that we should consider whether weak, yet real expression may have been removed. These questions have motivated us to think more deeply about the underlying principles and assumptions of our inference pipeline. Following the reviewer's questions, we have expanded our discussion on the application of zSTEP in developmental biology and the features of Palette compared to the existing strategies.

We believe that after incorporating the revisions, our current manuscript now demonstrates the application scenario of Palette clearer and suggested the application of zSTEP for investigating biological questions in developmental biology. We are grateful for the reviewer's guidance, which helps us increase the impact of our work.

1. The authors mention that they used a variable factor to adjust expression differences between the ST and bulk RNA-seq datasets. It would be important for the authors to comment on how much overlap in gene expression is necessary between the datasets for an accurate calculation of this variable factor? Can this be directly tested, for instance, by testing how their conclusions vary if expression is adjusted by a variable factor calculated from only a smaller set of genes?

Response: We thank the reviewer for the professional questions. We are sorry about not including the gene numbers in our previous manuscript. And now we have provided the numbers of genes in bulk and ST data and the numbers of the overlapped genes (Fig. 15).

"Palette was performed on the aligned slices using the overlapped genes. For the 10 hpf embryo, there were 24,658 genes in the bulk data, 18,698 genes in the Stereo-seq data, and 16,601 overlapped genes. For the 12 hpf embryo, there were 23,018 genes in the bulk data, 18,948 genes in the Stereo-seq data, and 16,401 overlapped genes. For the 16 hpf embryo, there were 24,357 genes in the bulk data, 23,110 genes in the Stereo-seq data, and 19,539 overlapped genes."

See response letter for the figure.

For Palette implementation, we took all the overlapped genes. To calculate the variable factor, we aggregated the expression of each gene in the ST data, and then used the expression of the bulk data to divide the aggregated expression for variable factor calculation. As a result, each overlapped gene was assigned a variable factor to adjust its expression, based on its difference between bulk and ST data. The rationale behind this approach is that by considering the ST data as a whole, we can effectively reduce the variations among individual spots. This allows the variable factors to provide reasonable adjustment to gene expression.

Above all, the variable factors can be directly calculated. Currently Palette only can infer the expression patterns of overlapped genes. It means when the number of overlapped genes is small, such as MERFISH only detecting hundreds of genes, Palette can only infer the expression patterns of these genes. However, if the MERFISH data have good quality, which enable resolving distinct cell types, we believe Palette will also show good performance when using MERFISH as ST reference. Additionally, we plan to perform Palette using MERFISH as ST reference to further demonstrate its broad application when using different ST references.

1. Palette gives rise to highly spatially precise patterns, which closely match those found in ISH. However, the smoothening of the expression can also remove weak, yet real, local expression patterns, as shown for idgf6 in Fig. 2a. Can the authors test this more extensively for other genes?

Response: We thank the reviewer for this essential question. We agree with the reviewer that weak, yet real expression might be removed in our Palette inference pipeline. The weak, sparse expression may be due to the ST technique itself or the variations in samples. However, that sparse gene expression may not have biological meaning, and the focus of our pipeline in to capture the expression patterns, which are closely correlated with functions and crucial for embryonic development. Therefore, our algorithm considers spot characteristics and emphasize cluster-specific expression, resulting in spatial-specific expression patterns. In most cases, the main gene expression patterns can be captured, which can help understand gene functions and roles in embryonic development. We have updated Supplementary Figure S1a (Fig. 16) to include more gene patterns to demonstrate this point.

See response letter for the figure.

1. Using adjacent slices for ST and "bulk RNA-seq" may provide better results than those obtained when comparing two independent datasets. Could the authors also extend the analysis of Palette's functionalities by using separate, previously available but independent datasets, for ST and bulk RNA-seq in Drosophila as well?

Response: We thank the reviewer for the valuable question. We agree with the reviewer that using adjacent slices may provide better results. The idea here is that the inferred spatial expression patterns from pseudo bulk RNA-seq can be used to compare with the real expression of ST to evaluate Palette performance. We have updated our Figure 2a (Fig. 17) to illustrate the analysis clearer.

See response letter for the figure.

To demonstrate the Palette's functionalities, we have used Palette to infer zebrafish bulk RNA-seq slice (Junker et al., 2014) using Stereo-seq slice (Liu et al., 2022) as ST reference, and these two datasets are separate and independent. We agree with the reviewer that it would be good to use separate datasets to test in Drosophila to further demonstrate the Palette's functionalities. However, unfortunately, we did not find the Drosophila serial bulk RNA-seq data along left-right axis of the corresponding stages, and thus we might be unable to perform the extra analyses using independent Drosophila datasets.

References:

Junker, J.P. et al. Genome-wide RNA Tomography in the zebrafish embryo. Cell 159, 662-675 (2014).

Liu, C. et al. Spatiotemporal mapping of gene expression landscapes and developmental trajectories during zebrafish embryogenesis. Dev Cell 57, 1284-1298 e1285 (2022).

1. The DreSTEP analysis in zebrafish embryos is interesting and validates well-established observations in the field. Can the authors also discuss whether and how their dataset allows them to refine our understanding of the spatial or temporal pattern of the morphogens and TFs involved in AP patterning? This would further validate their approach.

Response: We appreciate the reviewer for recognition of our zSTEP and raising this valuable question, which has inspired us to think more deeply about the potential application of zSTEP in developmental biology. As the reviewer noted, our zSTEP analyses have validated well-established observations in the field. Rather than focusing on the sparse expression detected in ST data, zSTEP emphasizes the gene expression patterns that are closely correlated with biological functions and critical for embryonic development. Therefore, zSTEP can serve as a valuable tool for identifying the genes having specific patterns at certain developmental stages.

Pattern formation is one of the most important developmental issues for all animals. The reaction-diffusion (RD) model is a widely recognized theoretical framework used to explain self-regulated pattern formation in developing animal embryos (Kondo & Miura, 2010). Morphogen molecules are produced at specific regions of the embryo, forming morphogen gradients to guide cell specification. Most importantly, interactions between different morphogens instruct more complicated and well-choreographed pattern formation. Our Palette-constructed zSTEP provides a comprehensive transcriptomic expression pattern, including all morphogens and TFs, across the whole embryo during development. These valuable resources, in our opinion, could be leveraged to evaluate and prove the RD model during development, including AP patterning. In our current zSTEP analyses, we have already identified genes that exhibit specific expression patterns along AP axis, some of which have not been fully characterized. These genes could be potential targets for further investigation into their roles in AP patterning, although they are not the primary focus of this study. Additionally, our analyses only focused on morphogens and TFs, but zSTEP can be used to investigate the expression patterns of other genes as well. Moreover, we employed a random forest model to investigate the most essential morphogens and TFs for AP axis refinement, which is one of the basic applications of zSTEP. To investigate specific biological questions of interest, it would be worth exploring the use of more sophisticated machine learning models.

We have added the following paragraph in the Discussion section to discuss the potential application of zSTEP in future studies.

"Finally, while the current analyses demonstrated that zSTEP can serve as a valuable tool for identifying genes having specific patterns at certain developmental stages, the exploration of zSTEP is still limited. During animal development, pattern formation is always one of the most important developmental issues. As demonstrated by the reaction-diffusion (RD) model, morphogen molecules are produced at specific regions of the embryo, forming morphogen gradients to guide cell specification, while interactions between different morphogens instruct more complicated and well-choreographed pattern formation. Our Palette constructed zSTEP, as a comprehensive transcriptomic expression pattern during development, could be leveraged to evaluate and prove the RD model during development, including AP patterning. Moreover, the investigation of gene expression patterns should not be limited to morphogens and TFs, and further investigation of their roles in AP patterning is desirable. Additionally, here a random forest model may be sufficient for investigating the most essential morphogens and TFs for AP axis refinement, while more sophisticated machine learning models may be required for addressing more specific biological questions."

Reference

Kondo, S. & Miura, T. Reaction-Diffusion model as a framework for understanding biological pattern formation. Science 329, 1616-1620 (2010).

1. Can the authors comment on the limits of this inference pipeline? And how it performs as compared to single-cell RNA sequencing datasets where spatial information is inferred from well-established marker genes?

Response: We appreciate the reviewer for this insightful question, which has inspired us to further explore the advantages and limitations of the Palette pipeline in comparison with other inference strategies. As mentioned in the Discussion section, a key limitation of the inference pipeline is its heavy reliance on the quality of ST data. It is obvious that if the quality of ST data is not of sufficient quality, the low-expression genes may not be detected or only appear in very few scattered spots. We think it is a common issue for any inference tools using ST data as the reference. However, with the ongoing advancements in spatial resolution and data quality, the performance of Palette is expected to be improved.

As a comparison, the single-cell RNA sequencing datasets where spatial information is inferred from well-established marker genes do not face this limitation. The ground-breaking work by Satija et al. (2015) used such a strategy that combined scRNA-seq and in situ hybridizations of well-established marker genes to infer spatial location, enabling single cell resolution, as it maintains the high read depth and gene detection. One advantages of this scRNA-seq-based strategy is that it provides the transcriptomics of individual cells, rather than a combination of cell within a ST spot, although the positional relationships between cells are not real.

However, compared to the inference from ST data, the positional relationships between cells are not directly captured. On the other hand, as the embryonic development progresses, more cell types will be specified, and the body patterning becomes more complex. In this scenario, using well-established marker gene to infer spatial information would be much more challenging. Additionally, there are not many scRNA-seq datasets of serial sections, and thus this strategy may not be used to construct 3D ST atlas.

In contrast, our Palette inference pipeline is based on the ST data, which preserves the real positional relationships between spots. Although our inference pipeline cannot achieve single cell resolution, it focuses on the gene expression patterns rather than the sparse expression within individual spots. By applying Palette to paired serial sections, we were able to generated a 3D spatial expression atlas of zebrafish embryos, which has showed promising performance for investigating gene expression patterns and their involvement in AP patterning.

Reference

Satija, R. et al. Spatial reconstruction of single-cell gene expression data. Nature biotechnology 33, 495-502 (2015)

We have updated the following paragraphs to further demonstrating the limitation of the inference pipeline in details in the Discussion section.

"Thirdly, the performance of Palette and zSTEP heavily relied on the quality of ST data. If the quality of ST data is not of sufficient quality, the low-expression genes may not be detected or only appear in very few scattered spots, and the performance of spot clustering could also be affected. Moreover, in this study, for example, the Stereo-seq data of 12 hpf zebrafish embryo had fewer slices on the right side (Fig. S3b), resulting in more blank spots in the right part of zSTEP for the 12 hpf embryo. However, with the ongoing advancements in spatial resolution and data quality, the performance of Palette is expected to be enhanced and demonstrate even greater potential for analysing spatiotemporal gene expression.

On the other hand, compared to the brilliant strategy that infers spatial information of scRNA-seq data from well-established genes, our Palette pipeline cannot achieve single cell resolution. However, our Palette pipeline is based on the ST reference, and thus preserves the real positional relationships between spots. Furthermore, the focus of our pipeline is to infer the gene expression patterns, which are closely correlated to biological functions and critical for embryonic development, rather than the sparse expression within individual spots. In this regard, our Palette pipeline can be advantageous, as it allows for reconstruction of the major expression profiles, which are often more relevant for understanding developmental processes. Additionally, our Palette can be applied to serial sections, enabling the construction of 3D ST atlas."

Reviewer #3 (Significance):

This study tackles an important challenge in biology - the difficult to resolve gene expression patterns with high spatial precision and in a high-throughput manner. By integrating sequencing datasets from previously published studies, as well as newly-generated datasets, the authors provide evidence that their novel inference pipeline enables them to obtain high-quality spatial information simply from bulk RNA-seq datasets, using ST as a reference. The development of this pipeline - Palette - is a major part of this manuscript and its applicability is validated using datasets from Drosophila and zebrafish embryos. This in an important advance for the field, but it would be nice for the authors to further comment on i) the validity of some of their approaches and how they may influence the quality of their inference, as well as, ii) potential pitfalls/limitations of this approach as compared to others available in the field. This would synthetize both previous and current findings into a conceptual and technological framework that would have a strong impact well beyond cell and developmental biology.

Audience: This study would be relevant for a broad audience of biologists, interested in morphogen signaling, gene regulatory networks and cell fate specification.

Expertise in zebrafish development, gastrulation, morphogen signaling and morphogenesis.

Response: We thank the reviewer for providing the positive feedback, arising these valuable questions, which have motivated us to deeply consider the design concept and further application of Palette and zSTEP. Based on the insightful questions from the reviewer, we have added two extra paragraphs in the Discussion section to further discuss the potential application of zSTEP in developmental biology and application scenarios of the Palette pipeline. Specially, we have demonstrated that the performance of the inference pipeline relies on the spatial resolution and data quality of the ST data. We have then compared the advantages and limitations of Palette with the existing brilliant spatial inference strategy, which infers spatial information of scRNA-seq from well-established marker genes. Although our inference pipeline cannot achieve single cell resolution, it can capture the major expression patterns, which are closely correlated to functions and critical for embryonic development. We believe this will help readers gain a clearer understanding of the advantage and limitations of our pipeline compared to other tools, as well as the tasks for which Palette and our constructed zSTEP can be utilized. We express our thanks to the reviewer again for the valuable comments.

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Referee #3

Evidence, reproducibility and clarity

In this study, Dong and colleagues developed a computational pipeline to use spatial transcriptomics (ST) datasets as a reference to infer the spatial patterns of gene expression from bulk RNA sequencing data. This approach aims to overcome the low read depth and limited gene detection capabilities in current ST datasets, while exploiting its ability to provide highly resolved spatial information. By combining bulk RNAseq datasets from 3 developmental stages during early zebrafish development with previously available ST and imaging datasets, the authors build DreSTEP (Danio rerio spatiotemporal expression profiles). Using this approach, they go on to identify the morphogens and transcription factors involved in anteroposterior patterning.

The paper is well written, and the pipeline presented in this study is likely to be useful beyond the case studies included in this study. There are a few questions that, in my view, would be important to clarify to increase the impact of this work:

1. The authors mention that they used a variable factor to adjust expression differences between the ST and bulk RNAseq datasets. It would be important for the authors to comment on how much overlap in gene expression is necessary between the datasets for an accurate calculation of this variable factor? Can this be directly tested, for instance, by testing how their conclusions vary if expression is adjusted by a variable factor calculated from only a smaller set of genes?
2. Palette gives rise to highly spatially precise patterns, which closely match those found in ISH. However, the smoothening of the expression can also remove weak, yet real, local expression patterns, as shown for idgf6 in Fig. 2a. Can the authors test this more extensively for other genes?
3. Using adjacent slices for ST and "bulk RNAseq" may provide better results than those obtained when comparing two independent datasets. Could the authors also extend the analysis of Palette's functionalities by using separate, previously available but independent datasets, for ST and bulk RNAseq in Drosophila as well?
4. The DreSTEP analysis in zebrafish embryos is interesting and validates well-established observations in the field. Can the authors also discuss whether and how their dataset allows them to refine our understanding of the spatial or temporal pattern of the morphogens and TFs involved in AP patterning? This would further validate their approach.
5. Can the authors comment on the limits of this inference pipeline? And how it performs as compared to single-cell RNA sequencing datasets where spatial information is inferred from well-established marker genes?

Significance

This study tackles an important challenge in biology - the difficult to resolve gene expression patterns with high spatial precision and in a high-throughput manner. By integrating sequencing datasets from previously published studies, as well as newly-generated datasets, the authors provide evidence that their novel inference pipeline enables them to obtain high-quality spatial information simply from bulk RNAseq datasets, using ST as a reference. The development of this pipeline - Palette - is a major part of this manuscript and its applicability is validated using datasets from Drosophila and zebrafish embryos. This in an important advance for the field, but it would be nice for the authors to further comment on i) the validity of some of their approaches and how they may influence the quality of their inference, as well as, ii) potential pitfalls/limitations of this approach as compared to others available in the field. This would synthetize both previous and current findings into a conceptual and technological framework that would have a strong impact well beyond cell and developmental biology.

Audience: This study would be relevant for a broad audience of biologists, interested in morphogen signaling, gene regulatory networks and cell fate specification.

Expertise in zebrafish development, gastrulation, morphogen signaling and morphogenesis.

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Referee #2

Evidence, reproducibility and clarity

The authors of the study introduce the Palette method, a novel approach designed to infer spatial gene expression patterns from bulk RNA-sequencing (RNA-seq) data. This method is complemented by the development of the DreSTEP 3D spatial gene expression atlas of zebrafish embryos, establishing a comprehensive resource for visualizing gene expression and investigating spatial cell-cell interactions in developmental biology.

Major concerns:

1. The efficacy of the Palette method may be compromised by its dependency on the quality of the reference spatial transcriptomics data. As highlighted in the study, variations in data quality can lead to significant challenges in reconstructing accurate spatial expression patterns from bulk data. This underscores the necessity of evaluating quality parameters, such as the number of gene detections and spatial resolution, to ensure reliable outcomes. Additional studies should rigorously assess how these quality factors influence the accuracy and efficiency of the algorithm in various data contexts, particularly under diverse conditions of gene detection.
2. The methodology raises pertinent questions regarding how the clustering results from different algorithms may affect the reconstructions by the Palette method. The authors would better provide a detailed discussion/comparison of clustering processes that optimize the reconstruction of spatial patterns, ensuring precision in the downstream analyses.
3. The choice to utilize only highly expressed genes in the initial stages of the Palette algorithm also warrants further exploration. Addressing the criteria for determining which genes qualify as "highly expressed" and outlining robust cutoff will enhance the algorithm's rigor and applicability. Similarly, in the iterative estimation of gene expression across spatial spots, establishing optimal iteration conditions is crucial. Implementing a loss function may offer a systematic method for concluding iterations, thus refining computational efficiency.
4. Performance metrics relating to processing speed and computational demands remain inadequately addressed in the current framework. Understanding how the Palette method scales across varying gene counts and bulk RNA-seq datasets will be essential for potential applications in larger biological contexts. Notably, the quantitative demands of analyzing 20,000 genes when processing 10, 100, or 1,000 bulk RNA profiles must be articulated to guide researchers in planning accordingly.

Minor opinions:

1. Despite the promising advances offered by the zebrafish 3D reconstruction, there is a lack of details regarding numbers of the spatial transcriptomics (ST) data utilized, and the number of bulk RNA-seq data employed in the analyses. These parameters need to be clarified.
2. Issues regarding spatial cell-cell communication, especially concerning interactions over longer distances, necessitate careful consideration. Introducing spatial distance constraints could help formulate more realistic models of cellular interactions, a vital aspect of embryonic development.
3. Evaluation metrics such as the Adjusted Rand Index (ARI) and Root Mean Square Error (RMSE) represent critical tools for systematically measuring the similarity of inferred spatial patterns, yet their specific application within this context should be elaborated.
4. The study's limitations surrounding ST data quality cannot be overstated. Discussing scenarios where only limited or poor-quality ST data are available will be crucial for guiding future studies. Furthermore, a clear explanation of how enhanced specificity and accuracy translate into tangible biological insights is essential for demystifying the underlying mechanisms driving developmental processes.

Significance

The Palette pipeline demonstrates a marked improvement in specificity and accuracy when predicting spatial gene expression patterns. Evaluative studies on Drosophila and zebrafish datasets affirm its enhanced performance compared to existing methodologies. By effectively reconstructing spatial information from bulk transcriptomic data, the Palette method innovatively merges the philosophy of leveraging single-cell transcriptomic data for deconvolution analyses. This integration is pivotal, advancing traditional bulk RNA-seq approaches while laying the groundwork for future research.

One of the notable achievements in this work is the construction of the DreSTEP atlas, which integrates serial bulk RNA-seq data with advanced 3D imaging techniques. This resource grants researchers unprecedented access to the visualization of gene expression patterns across the zebrafish embryo, facilitating the investigation of spatial relationships and cell-cell interactions critical for developmental processes. Such capabilities are invaluable for understanding the intricate dynamics of embryogenesis and the distinct roles of individual cell types.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript titled "Unravelling the Progression of the Zebrafish Primary Body Axis with Reconstructed Spatiotemporal Transcriptomics" presents a comprehensive analysis of the development of the primary body axis in zebrafish by integrating bulk RNA-seq, 3D images, and Stereo-Seq. The authors first clearly demonstrate the application of Palette for integrating RNA-seq and Stereo-Seq using published spatial transcriptomics data of Drosophila embryos. Subsequently, they produced serial bulk RNA-seq data for certain developmental stages of Danio rerio embryos and utilized published Stereo-Seq data. Through robust validation, the authors observe the molecular network involved in AP axis formation. While the authors show that integrating bulk RNA-seq data with Stereo-Seq improves spatial resolution, additional proof is required to demonstrate the extent of this improvement.

Major Comments:

1. Lines 66-68: Discuss the limitations of existing tools and explicitly state the advantages of using Palette.
2. Body Pattern Genes Analysis: For both Drosophila and Danio rerio, it would be valuable to examine body pattern genes in Stereo-Seq and apply Palette to determine if the resolution of the segments improves or merges. The resolution of the A-P axis is convincing, but further evidence for other segments would be beneficial.
3. Figure 2d: Include the A-P line for which the intensity profile was plotted in the main figure, rather than just in the supplementary material. Additionally, consider simplifying the plot by not combining three lines into one, as it complicates the interpretation of observations.
4. Drosophila Data Analysis: While the alignment and validation of Danio rerio sections are clearly explained, the analysis and validation of Drosophila data are insufficiently detailed. Provide a more thorough explanation of how the intensity profiles between BDGP in situ data and Stereo-Seq data are adjusted.
5. Figure 3d: Present a plot with the expected expression profiles of the three genes if the embryo is aligned as anticipated.
6. Analysis Without Palette: Between lines 277-438, the outcome of using Palette with bulk RNA-seq and Stereo-Seq is convincing. However, consider the following:<br /> o What would be the observations if the analysis were conducted solely with Stereo-Seq data, without incorporating bulk RNA-seq data and employing Palette?<br /> o This study uses only Stereo-Seq as the spatial transcriptomics reference. It would strengthen the argument to use at least one other spatial transcriptomics method, such as Visium or MERFISH, in conjunction with bulk RNA-seq and Palette, to demonstrate whether Palette consistently improves gene expression resolution.
7. PDAC Data Analysis: Provide a more detailed explanation of the PDAC data analysis and use appropriate colors in the tissue images to clearly distinguish cell types.
8. Comparison with Other Methods: State the limitations of not using STitch3D and Spateo for alignment and explain why these methods were not employed.

Minor Comments:

1. References: Add references to the statements in lines 51-53.
2. Scientific Name Consistency: Ensure consistency in using either "Danio rerio" or "zebrafish" throughout the manuscript.
3. Related References: Include the following relevant references:
4. https://academic.oup.com/bib/article/25/4/bbae316/7705532
5. https://www.life-science-alliance.org/content/6/1/e202201701
6. Figure 1a: In the Venn diagram, include the number of genes in the bulk and Stereo-Seq datasets, as well as the number of overlapping genes.
7. Figure 1 Improvement: Enlarge Figure 1 and reduce repetitive elements, such as parts of the deconvolution and Figure 1b.
8. Figure 3f: Explain the black discontinuous line in the plot.
9. Line 610: State the percentage of unpaired imaging spots.
10. Lines 616-618: Specify the unit for the spot diameter.

Significance

This algorithm will be useful not only for the field of developmental biology but also for wider applications in spatial omics. Although I have expertise in spatial omics technology development, my understanding of computational biology is limited, which restricts my ability to fully evaluate the Palette algorithm presented in this paper.

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Reply to the reviewers

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Reply to the Reviewers

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 #3

Evidence, reproducibility and clarity

This is a good manuscript, well performed and well presented. I have several suggestions/questions to enhance the clarity of the concept, as technically the work is rather well performed.

1. I suggest that the authors explain better the mesenchymal-to-epithelial (MET) transition in reprogramming. Perhaps, explaining that epithelial gene acquisition (e.g., CDH1) and epidermal cell fate are not exactly the same. This approach could also be used to divide the genes they study further in their analyses.
2. KLF4 is both a repressor and an activator in different cell contexts including reprogramming. Does HIC2 act only as repressor? Is it possible that HIC2 is repressing KLF4-activated genes bad for reprogramming (including epidermal genes) and activating KLF4-suppressed genes ncessary for reprogramming? This should not be too difficult to explore with their current dataset and they also could look at available datasets for histone modifications in reprogramming.
3. Does HIC2 bind to genes related to somatic cell identify that need to be suppressed in reprogramming before the MET phase takes place?
4. Does HIC2 influence proliferation during reprogramming?

Referee cross-commenting

Comments by the other reviewers are sound and will help improve the manuscript.

Significance

In this manuscript, Kaji and colleagues perform a CRISPR/Cas9 screen to identify genes involved in mouse somatic cell reprogramming, identifying HIC2 as a target that they further validate. They conclude that HIC2 acts by repressing the epidermal/epithelial program induced by KLF4 during reprogramming. Studying the complex role of transcription factor interactions in the context of cell fate conversions (of any kind and not just somatic cell reprogramming) is highly relevant. This work helps clarify such complexity in a specific context but the work has wider conceptual implications.

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Referee #2

Evidence, reproducibility and clarity

The study by Beniazza et al. aims to address the inefficiencies associated with OSKM-mediated reprogramming. Through a genome-wide CRISPR/Cas9 knockout screen, the authors identified 14 genes essential for iPSC reprogramming but dispensable for ESC self-renewal. Among these, HIC2 significantly enhanced reprogramming efficiency, yielding approximately a tenfold increase compared to standard conditions. scRNA-seq analyses revealed that HIC2-overexpressing cells follow a more direct trajectory toward pluripotency, bypassing the KLF4-dependent activation of keratinocyte and epidermal gene programs. ChIP-seq profiling further demonstrated that HIC2 and KLF4 co-occupy approximately 60% of their genomic targets, indicating substantial regulatory overlap. Notably, this co-binding and its functional effects are dose-dependent on KLF4, as shown by experiments comparing high KLF4 expression systems (standard OSKM and STEMCCA+9 constructs) with low KLF4 conditions (STEMCCA cassette lacking additional KLF4). The authors conclude that HIC2's modulatory effect occurs specifically under high KLF4 levels.

Major Comments

Figure 1D: What is the efficiency of gRNA library transduction into MEFs? What percentage of MEF cells were successfully knocked out? Figures 2B/C: To rule out the possibility that the observed variability in reprogramming efficiency among the tested factor combinations stems from differences in MKOS expression levels, the authors should provide evidence showing that the expression levels of all MKOS factors are comparable across samples. Figures 2D/E: To rule out a fibroblast-specific effect, can the authors show whether the epidermal gene signature is also upregulated during NSC reprogramming and whether Hic2 overexpression suppresses this signature? Figure 2H: Are the 13 signature genes that distinguish MKOS-Hic2-iPSCs from MKOS-iPSCs consistently identified across independent Hic2-iPSC lines, or does each reprogramming event produce a distinct gene set? If the signature is consistent, this is an important observation and should be further addressed and discussed. Figure 3K: Can the authors show the expression levels of MKOS and Hic2 transgenes in all samples? The same concern applies to Figure 4I. The reviewer wishes to be confident that the reduction in epidermal gene expression observed in MEFs is not due to variable transgene expression caused by multiple vector introductions (e.g., KLF4 alone versus KLF4 + Hic2), which could potentially lead to lower KLF4 expression through co-transfection competition. Does KLF4 overexpression in Hic2-knockdown MEFs lead to greater upregulation of the epidermal gene signature compared to the wild-type control? Figure 4C: It appears that only about half of the Hic2 binding sites overlap with KLF4 sites. What are the characteristics of the other Hic2-specific sites, and how might they contribute to reprogramming, if at all? Can the authors perform a reprogramming experiment using a combination that lacks KLF4 (e.g., replacing KLF4 with Esrrb or BMP4, as shown in PMID: 19136965 and PMID: 21135873) and test the effect of Hic2 under these conditions? Do KLF4 and HIC2 physically interact? The authors should perform a co-immunoprecipitation assay to address this question. What is the effect of Hic2 during human reprogramming? Does it play a similar regulatory role?

Minor Comments

• Typographical errors should be checked and avoided; for example, on page 10, the word 'colonies' was misspelled.
• Some blank squares appear in the Methods section; please correct these formatting errors.

Referee cross-commenting

All suggestions are feasible within a relatively short time frame and will improve the manuscript.

Significance

Overall, this study is of significant interest to the stem cell community and presents a well-designed and carefully executed experimental framework. However, several concerns remain that should be addressed prior to publication.

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Referee #1

Evidence, reproducibility and clarity

Summary: This work identified 14 genes essential for iPSC reprogramming but not essential for ESC maintenance and MEF proliferation by analyzing three CRISPR/Cas9-mediated genome-wide KO screens. Among them, they found that overexpression of the Hic2 gene can greatly promote OSKM-driven reprogramming. By using scRNA-seq in time points of the reprogramming process, they found that Hic2 can bypass the epidermal gene expressing state during reprogramming. Then, using ChIP-seq, they found that HIC2 and KLF4 have common binding sites on epidermal genes. Finally, by expressing KLF4 alone or KLF4 and HIC2 together, they demonstrated that HIC2 can inhibit KLF4-driven epidermal gene expression.

Major comments: The claims and conclusions are well-supported by the data and do not require additional experiments or analysis. The data and methods are presented in a reproducible way.

Minor comments: There seem to be some typos. For example, "we selected 30 genes with low FDRs in ESC maintenance" may be "high depletion FDR," since you want nonessential genes for ESC maintenance. The "log10(-FDR)" may be "-log10(FDR)." Some figures lack P values. Perhaps it would be useful to analyze whether Hic2 reduces reprogramming heterogeneity. Validation experiments, such as trilineage differentiation, could be considered to demonstrate that Hic2 does not affect the pluripotency and differentiation capacity of iPSCs.

Significance

General Assessment: This work is based on three CRISPR/Cas9-mediated genome-wide KO screens, which makes it comprehensive and reliable. They discovered that HIC2 and OSKM can drive reprogramming without an epidermal gene expression intermediate. They also found extensive common binding sites of HIC2 and KLF4 at target genes. This work not only enables more efficient reprogramming but also expands our understanding of the reprogramming process. Among HIC2 and KLF4 common target genes, some are repressed while others are activated, and it will be very interesting to study the mechanism of this selective function.

Advance: Compared to natural `embryonic development, OSKM-driven reprogramming is very inefficient, and our understanding of the mechanisms of efficient reprogramming remains poor. The specific role of the epidermal gene expression state in the reprogramming process remains unclear. This work strongly supports the idea that repression of the epidermal gene expression state can promote iPSC generation. Moreover, previous studies on Hic2 are limited, and this work enriches our understanding of its mechanisms and functions.

Audience: This study may be of interest to those interested in basic research on reprogramming mechanisms or Hic2, as well as those developing efficient reprogramming technologies.

My field: Reprogramming, stem cells, aging, transcription factors.

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

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

In this manuscript, Xiong and colleagues investigate the mechanisms operating downstream to TRIM32 and controlling myogenic progression from proliferation to differentiation. Overall, the bulk of the data presented is robust. Although further investigation of specific aspects would make the conclusions more definitive (see below), it is an interesting contribution to the field of scientists studying the molecular basis of muscle diseases.

We thank the Reviewer for appreciating our work and for their valuable suggestions to improve our manuscript. We have carefully addressed some of the concerns raised, as detailed here, while others, which require more experimental efforts, will be addressed as detailed in the Revision Plan.

In my opinion, a few aspects would improve the manuscript. Firstly, the conclusion that Trim32 regulates c-Myc mRNA stability could be expanded and corroborated by further mechanistic studies:

1. Studies investigating whether Tim32 binds directly to c-Myc RNA. Moreover, although possibly beyond the scope of this study, an unbiased screening of RNA species binding to Trim32 would be informative. Authors’ response. This point will be addressed as detailed in the Revision Plan

If possible, studies in which the overexpression of different mutants presenting specific altered functional domains (NHL domain known to bind RNAs and Ring domain reportedly involved in protein ubiquitination) would be used to test if they are capable or incapable of rescuing the reported alteration of Trim32 KO cell lines in c-Myc expression and muscle maturation.

Authors’ response. This point will be addressed as detailed in the Revision Plan

An optional aspect that might be interesting to explore is whether the alterations in c-Myc expression observed in C2C12 might be replicated with primary myoblasts or satellite cells devoid of Trim32.

Authors’ response. This point will be addressed as detailed in the Revision Plan

I also have a few minor points to highlight:

• • It is unclear if the differences highlighted in graphs 5G, EV5D, and EV5E are statistically significant.*

Authors’ response. We thank the Reviewer for raising this point. We now indicated the statistical analyses performed on the data presented in the mentioned figures (according also to a point of Reviewer #3). According to the conclusion that Trim32 is necessary for proper regulation of c-Myc transcript stability, using 2-way-ANOVA, the data now reported as Figure 5G show the statistically significant effect of the genotype at 6h (right-hand graph) but not at D0 (left-hand graph). In the graphs of Fig. EV5 D and E at D0 no significant changes are observed whereas at 6h the data show significant difference at the 40 min time point. We included this info in the graphs and in the corresponding legends.

- On page 10, it is stated that c-Myc down-regulation cannot rescue KO myotube morphology fully nor increase the differentiation index significantly, but the corresponding data is not shown. Could the authors include those quantifications in the manuscript?

Authors’ response. As suggested, we included the graph showing the differentiation index upon c-Myc silencing in the Trim32 KO clones and in the WT clones, as a novel panel in Figure 6 (Fig. 6D). As already reported in the text, a partial recovery of differentiation index is observed but the increase is not statistically significant. In contrast, no changes are observed applying the same silencing in the WT cells. Legend and text were modified accordingly.

Reviewer #1 (Significance (Required)):

The manuscript offers several strengths. It provides novel mechanistic insight by identifying a previously unrecognized role for Trim32 in regulating c-Myc mRNA stability during the onset of myogenic differentiation. The study is supported by a robust methodology that integrates CRISPR/Cas9 gene editing, transcriptomic profiling, flow cytometry, biochemical assays, and rescue experiments using siRNA knockdown. Furthermore, the work has a disease relevance, as it uncovers a mechanistic link between Trim32 deficiency and impaired myogenesis, with implications for the pathogenesis of LGMDR8. * * At the same time, the study has some limitations. The findings rely exclusively on the C2C12 myoblast cell line, which may not fully represent primary satellite cell or in vivo biology. The functional rescue achieved through c-Myc knockdown is only partial, restoring Myogenin expression but not the full differentiation index or morphology, indicating that additional mechanisms are likely involved. Although evidence supports a role for Trim32 in mRNA destabilization, the precise molecular partners-such as RNA-binding activity, microRNA involvement, or ligase function-remain undefined. Some discrepancies with previous studies, including Trim32-mediated protein degradation of c-Myc, are acknowledged but not experimentally resolved. Moreover, functional validation in animal models or patient-derived cells is currently lacking. Despite these limitations, the study represents an advancement for the field. It shifts the conceptual framework from Trim32's canonical role in protein ubiquitination to a novel function in RNA regulation during myogenesis. It also raises potential clinical implications by suggesting that targeting the Trim32-c-Myc axis, or modulating c-Myc stability, may represent a therapeutic strategy for LGMDR8. This work will be of particular interest to muscle biology researchers studying myogenesis and the molecular basis of muscle disease, RNA biology specialists investigating post-transcriptional regulation and mRNA stability, and neuromuscular disease researchers and clinicians seeking to identify new molecular targets for therapeutic intervention in LGMDR8. * * The Reviewer expressing this opinion is an expert in muscle stem cells, muscle regeneration, and muscle development.

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

Summary: * * In this study, the authors sought to investigate the molecular role of Trim32, a tripartite motif-containing E3 ubiquitin ligase often associated with its dysregulation in Limb-Girdle Muscular Dystrophy Recessive 8 (LGMDR8), and its role in the dynamics of skeletal muscle differentiation. Using a CRISPR-Cas9 model of Trim32 knockout in C2C12 murine myoblasts, the authors demonstrate that loss of Trim32 alters the myogenic process, particularly by impairing the transition from proliferation to differentiation. The authors provide evidence in the way of transcriptomic profiling that displays an alteration of myogenic signaling in the Trim32 KO cells, leading to a disruption of myotube formation in-vitro. Interestingly, while previous studies have focused on Trim32's role in protein ubiquitination and degradation of c-Myc, the authors provide evidence that Trim32-regulation of c-Myc occurs at the level of mRNA stability. The authors show that the sustained c-Myc expression in Trim32 knockout cells disrupts the timely expression of key myogenic factors and interferes with critical withdrawal of myoblasts from the cell cycle required for myotube formation. Overall, the study offers a new insight into how Trim32 regulates early myogenic progression and highlights a potential therapeutic target for addressing the defects in muscular regeneration observed in LGMDR8.

We thank the Reviewer for valuing our work and for their appreciated suggestions to improve our manuscript. We have carefully addressed some of the concerns raised as detailed here, while others, which require more laborious experimental efforts, will be addressed as reported in the Revision Plan.

Major Comments:

The work is a bit incremental based on this:

https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0030445 * * And this:

https://www.nature.com/articles/s41418-018-0129-0 * * To their credit, the authors do cite the above papers.

Authors’ response. We thank the Reviewer for this careful evaluation of our work against the current literature and for recognising the contribution of our findings to the understanding of myogenesis complex picture in which the involvement of Trim32 and c-Myc, and of the Trim32-c-Myc axis, can occur at several stages and likely in narrow time windows along the process, thus possibly explaining some reports inconsistencies.

The authors do provide compelling evidence that Trim32 deficiency disrupts C2C12 myogenic differentiation and sustained c-Myc expression contributes to this defective process. However, while knockdown of c-Myc does restore Myogenin levels, it was not sufficient to normalize myotube morphology or differentiation index, suggesting an incomplete picture of the Trim32-dependent pathways involved. The authors should qualify their claim by emphasizing that c-Myc regulation is a major, but not exclusive, mechanism underlying the observed defects. This will prevent an overgeneralization and better align the conclusions with the author's data.

Authors’ response. We agree with the Reviewer and we modified our phrasing that implied Trim32-c-Myc axis as the exclusive mechanism by explicitly indicated that other pathways contribute to guarantee proper myogenesis, in the Abstract and in Discussion.

The Abstract now reads: “… suggesting that the Trim32–c-Myc axis may represent an essential hub, although likely not the exclusive molecular mechanism, in muscle regeneration within LGMDR8 pathogenesis.”

The Discussion now reads: “Functionally, we demonstrated that c-Myc contributes to the impaired myogenesis observed in Trim32 KO clones, although this is clearly not the only factor involved in the Trim32-mediated myogenic network; realistically other molecular mechanisms can participate in this process as also suggested by our transcriptomic results.”

The authors provide a thorough and well-executed interrogation of cell cycle dynamics in Trim32 KO clones, combining phosphor-histone H3 flow cytometry of DNA content, and CFSE proliferation assays. These complementary approaches convincingly show that, while proliferation states remain similar in WT and KO cells, Trim32-deficient myoblasts fail in their normal withdraw from the cell cycle during exposure to differentiation-inducing conditions. This work adds clarity to a previously inconsistent literature and greatly strengthens the study.

Authors’ response. We thank the Reviewer for appreciating our thorough analyses on cell cycle dynamics in proliferation conditions and at the onset of the differentiation process.

The transcriptomic analysis (detailed In the "Transcriptomic analysis of Trim32 WT and KO clones along early differentiation" section of Results) is central to the manuscript and provides strong evidence that Trim32 deficiency disrupts normal differentiation processes. However, the description of the pathway enrichment results is highly detailed and somewhat compressed, which may make it challenging for readers to following the key biological 'take-homes'. The narrative quickly moves across their multiple analyses like MDS, clustering, heatmaps, and bubble plots without pausing to guide the reader through what each analysis contributes to the overall biological interpretation. As a result, the key findings (reduced muscle development pathways in KO cells and enrichment of cell cycle-related pathways) can feel somewhat muted. The authors may consider reorganizing this section, so the primary biological insights are highlighted and supported by each of their analyses. This would allow the biological implications to be more accessible to a broader readership.

Authors’ response. We thank the Reviewer for raising this point and apologise for being too brief in describing the data, leaving indeed some points excessively implicit. As suggested, we now reorganised this session and added the lists of enriched canonical pathways relative to WT vs KO comparisons at D0 and D3 (Fig. EV3B) as well as those relative to the comparison between D0 and D3 for both WT and Trim32 KO samples (Fig. EV3C), with their relative scores. We changed the Results section “Transcriptomic analysis of Trim32 WT and Trim32 KO clones along early differentiation” as reported here below and modified the legends accordingly.

The paragraph now reads: “Based on our initial observations, the absence of Trim32 already exerts a significant impact by day 3 (D3) of C2C12 myogenic differentiation. To investigate how Trim32 influences early global transcriptional changes during the proliferative phase (D0) and early differentiation (D3), we performed an unbiased transcriptomic profiling of WT and Trim32 KO clones (Fig. 2A). Multidimensional Scaling (MDS) analysis revealed clear segregation of gene expression profiles based on both time of differentiation (Dim1, 44% variance) and Trim32 genotype (Dim2, 16% variance) (Fig. 2A). Likewise, hierarchical clustering grouped WT and Trim32 KO clones into distinct clusters at both timepoints, indicating consistent genotype-specific transcriptional differences (Fig. EV3A). Differentially Expressed Genes (DEGs) were detected in the Trim32 KO transcriptome relative to WT, at both D0 and D3. In proliferating conditions, 72 genes were upregulated and 189 were downregulated whereas at D3 of differentiation, 72 genes were upregulated and 212 were downregulated. Ingenuity Pathway Analysis of the DEGs revealed the top 10 Canonical Pathways displayed in Fig. EV3B as enriched at either D0 or D3 (Fig. EV3B). Several of these pathways can underscore relevant Trim32-mediated functions though most of them represent generic functions not immediately attributable to the observed myogenesis defects.

Notably, the transcriptional divergence between WT and Trim32 KO cells is more pronounced at D3, as evidenced by a greater separation along the MSD Dim2 axis, suggesting that Trim32-dependent transcriptional regulation intensifies during early differentiation (Fig. 2A). Given our interest in the differentiation process, we therefore focused our analyses comparing the changes occurring from D0 to D3 in WT (WT D3 vs. D0) and in Trim32 KO (KO D3 vs. D0) RNAseq data.

Pathway enrichment analysis of D3 vs. D0 DEGs allowed the selection of the top-scored pathways for both WT and Trim32 KO data. We obtained 18 top-scored pathways enriched in each genotype (-log(p-value) ³ 9 cut-off): 14 are shared while 4 are top-ranked only in WT and 4 only in Trim32 KO (Fig. EV3C). For the following analyses, we employed thus a total of 22 distinct pathways and to better mine those relevant in the passage from the proliferation stage to the early differentiation one and that are affected by the lack of Trim32, we built a bubble plot comparing side-by-side the scores and enrichment of the 22 selected top-scored pathways above in WT and Trim32 KO (Fig. 2B). A heatmap of DEGs included within these selected pathways confirms the clustering of the samples considering both the genotypes and the timepoints highlighting gene expression differences (Fig. 2C). These pathways are mainly related to muscle development, cell cycle regulation, genome stability maintenance and few other metabolic cascades.

As expected given the results related to Figure 1, moving from D0 to D3 WT clones showed robust upregulation of key transcripts associated with the Inactive Sarcomere Protein Complex, a category encompassing most genes in the “Striated Muscle Contraction” pathway, while in Trim32 KO clones this pathway was not among those enriched in the transition from D0 to D3 (Fig. EV3C). Detailed analyses of transcripts enclosed within this pathway revealed that on the transition from proliferation to differentiation, WT clones show upregulation of several Myosin Heavy Chain isoforms (e.g., MYH3, MYH6, MYH8), α-Actin 1 (ACTA1), α-Actinin 2 (ACTN2), Desmin (DES), Tropomodulin 1 (TMOD1), and Titin (TTN), a pattern consistent with previous reports, while these same transcripts were either non-detected or only modestly upregulated in Trim32 KO clones at D3 (Fig. 2D). This genotype-specific disparity was further confirmed by gene set enrichment barcode plots, which demonstrated significant enrichment of these muscle-related transcripts in WT cells (FDR_UP = 0.0062), but not in Trim32 KO cells (FDR_UP = 0.24) (Fig. EV3D). These findings support an early transcriptional basis for the impaired myogenesis previously observed in Trim32 KO cells.

In addition to differences in muscle-specific gene expression, we observed that also several pathways related to cell proliferation and cell cycle regulation were more enriched in Trim32 KO cells compared to WT. This suggests that altered cell proliferation may contribute to the distinct differentiation behavior observed in Trim32 KO versus WT (Fig. 2B). Given that cell cycle exit is a critical prerequisite for the onset of myogenic differentiation and considering that previous studies on Trim32 role in cell cycle regulation have reported inconsistent findings, we further examined cell cycle dynamics under our experimental conditions to clarify Trim32 contribution to this process”

The work would be greatly strengthened by the conclusion of LGMDR8 primary cells, and rescue experiments of TRIM32 to explore myogenesis.

Authors’ response. This point will be addressed as detailed in the Revision Plan

Also, EU (5-ethynyl uridine) pulse-chase experiments to label nascent and stable RNA coupled with MYC pulldowns and qPCR (or RNA-sequencing of both pools) would further enhance the claim that MYC stability is being affected.

Authors’ response. This point will be addressed as detailed in the Revision Plan

"On one side, c-Myc may influence early stages of myogenesis, such as myoblast proliferation and initial myotube formation, but it may not contribute significantly to later events such as myotube hypertrophy or fusion between existing myotubes and myocytes. This hypothesis is supported by recent work showing that c-Myc is dispensable for muscle fiber hypertrophy but essential for normal MuSC function (Ham et al, 2025)." Also address and discuss the following, as what is currently written is not entirely accurate: https://www.embopress.org/doi/full/10.1038/s44319-024-00299-z and https://journals.physiology.org/doi/prev/20250724-aop/abs/10.1152/ajpcell.00528.2025

Authors’ response. We thank the Reviewer for bringing to our attention these two publications, that indeed, add important piece of data to recapitulate the in vivo complexity of c-Myc role in myogenesis. We included this point in our Discussion.

The Discussion now reads: “On one side, c-Myc may influence early stages of myogenesis, such as myoblast proliferation and initial myotube formation, but it may not contribute significantly to later events such as myotube hypertrophy or fusion between existing myotubes and myocytes. This hypothesis is supported by recent work showing that c-Myc is dispensable for muscle fiber hypertrophy but essential for normal MuSC function (Ham et al, 2025). Other reports, instead, demonstrated the implication of c-Myc periodic pulses, mimicking resistance-exercise, in muscle growth, a role that cannot though be observed in our experimental model (Edman et al., 2024; Jones et al., 2025).”

Minor Comments:

Z-score scale used in the pathway bubble plot (Figure 2C) could benefit from alternative color choices. Current gradient is a bit muddy and clarity for the reader could be improved by more distinct color options, particularly in the transition from positive to negative Z-score.

Authors’ response. As suggested, we modified the z-score-representing colors using a more distinct gradient especially in the positive to negative transition in Figure 2B.

Clarification on the rationale for selecting the "top 18" pathways would be helpful, as it is not clear if this cutoff was chosen arbitrarily or reflects a specific statistical or biological threshold.

Authors’ response. As now better explained (see comment regarding Major point: Transcriptomics), we used a cut-off of -log(p-value) above or equal to 9 for pathways enriched in DEGs of the D0 vs D3 comparison for both WT and Trim32 KO. The threshold is now included in the Results section and the pathways (shared between WT and Trim32 KO and unique) are listed as Fig. EV3C.

The authors alternates between using "Trim 32 KO clones" and "KO clones" throughout the manuscript. Consistent terminology across figures and text would improve readability.

Authors’ response. We thank the Reviewer for this remark, and we apologise for having overlooked it. We amended this throughout the manuscript by always using for clarity “Trim32 KO clones/cells”.

Cell culture methodology does not specify passage number or culture duration (only "At confluence") before differentiation. This is important, as C2C12 differentiation potential can drift with extended passaging.

Authors’ response. We agree with the Reviewer that C2C12 passaging can reduce the differentiation potential of this myoblast cell lines; this is indeed the main reason why we decided to employ WT clones, which underwent the same editing process as those that resulted mutated in the Trim32 gene, as reference controls throughout our study. We apologise for not indicating the passages in the first version of the manuscript that now is amended as per here below in the Methods section:

“The C2C12 parental cells used in this study were maintained within passages 3–8. All clonal cell lines (see below) were utilized within 10 passages following gene editing. In all experiments, WT and Trim32 KO clones of comparable passage numbers were used to ensure consistency and minimize passage-related variability.”

Reviewer #2 (Significance (Required)):

General Assessment:

This study provides a thorough investigation of Trim32's role the processes related to skeletal muscle differentiation using a CRISPR-Cas9 knockout C2C12 model. The strengths of this study lie in the multi-layered experimental approach as the authors incorporated transcriptomics, cell cycle profiling, and stability assays which collectively build a strong case for their hypothesis that Trim32 is a key factor in the normal regulation of myogenesis. The work is also strengthened by the use of multiple biological and technical replicates, particularly the independent KO clones which helps address potential clonal variation issues that could occur. The largest limitation to this study is that, while the c-Myc mechanism is well explored, the other Trim32-dependent pathways associated with the disruption (implicated by the incomplete rescue by c-Myc knockdown) are not as well addressed. Overall however, the study convincingly identifies a critical function for Trim32 during skeletal muscle differentiation. * * Advance: * * To my knowledge, this is the first study to demonstrate the mRNA stability level of c-Myc regulation by Trim32, rather than through the ubiquitin-mediated protein degradation. This work will advance the current understanding and provide a more complete understanding of Trim32's role in c-Myc regulation. Beyond c-Myc, this work highlights the idea that TRIM family proteins can influence RNA stability which could implicate a broader role in RNA biology and has potential for future therapeutic targeting. * * Audience: * * This research will be of interest to an audience that focuses on broad skeletal muscle biology but primarily to readers with more focused research such as myogenesis and neuromuscular disease (LGMDR8 in particular) where the defined Trim32 governance over early differentiation checkpoints will be of interest. It will also provide mechanistic insights to those outside of skeletal muscle that study TRIM family proteins, ubiquitin biology, and RNA regulation. For translational/clinical researchers, it identifies the Trim32/c-Myc axis as a potential therapeutic target for LGMDR8 and related muscular dystrophies.

Expertise: * * My expertise lies in skeletal muscle biology, gene editing, transgenic mouse models, and bioinformatics. I feel confident evaluating the data and conclusions as presented.

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

• In this paper, the authors examine the role of TRIM32, implicated in limb girdle muscular dystrophy recessive 8 (LGMDR8), in the differentiation of C2C12 mouse myoblasts. Using CRISPR, they generate mutant and wild-type clones and compare their differentiation capacity in vitro. They report that Trim32-deficient clones exhibit delayed and defective myogenic differentiation. RNA-seq analysis reveals widespread changes in gene expression, although few are validated by independent methods. Notably, Trim32 mutant cells maintain residual proliferation under differentiation conditions, apparently due to a failure to downregulate c-Myc. Translation inhibition experiments suggest that TRIM32 promotes c-Myc mRNA destabilization, but this conclusion is insufficiently substantiated. The authors also perform rescue experiments, showing that c-Myc knockdown in Trim32-deficient cells alleviates some differentiation defects. However, this rescue is not quantified, was conducted in only two of the three knockout lines, and is supported by inappropriate statistical analysis of gene expression. Overall, the manuscript in its current form has substantial weaknesses that preclude publication. Beyond statistical issues, the major concerns are: (1) exclusive reliance on the immortalized C2C12 line, with no validation in primary/satellite cells or in vivo, (2) insufficient mechanistic evidence that TRIM32 acts directly on c-Myc mRNA, and (3) overinterpretation of disease relevance in the absence of supporting patient or in vivo data. Please find more details below:*

We thank the Reviewer for the in-depth assessment of our work and precious suggestions to improve the manuscript. We have carefully addressed some of the concerns raised, as detailed here, while others, which require more experimental efforts, will be addressed as detailed in the Revision Plan.

- TRIM32 complementation / rescue experiments to exclude clonal or off-target CRISPR effects and show specificity are lacking.

Authors’ response. This point will be addressed as detailed in the Revision Plan

- The authors link their in vitro findings to LGMDR8 pathogenesis and propose that the Trim32-c-Myc axis may serve as a central regulator of muscle regeneration in the disease. However, LGMDR8 is a complex disorder, and connecting muscle wasting in patients to differentiation assays in C2C12 cells is difficult to justify. No direct evidence is provided that the proposed mRNA mechanism operates in patient-derived samples or in mouse satellite cells. Moreover, the partial rescue achieved by c-Myc knockdown (which does not fully restore myotube morphology or differentiation index) further suggests that the disease connection is not straightforward. Validation of the TRIM32-c-Myc axis in a physiologically relevant system, such as LGMD patient myoblasts or Trim32 mutant mouse cells, would greatly strengthen the claim.

Authors’ response. This point will be addressed as detailed in the Revision Plan

-Some gene expression changes from the RNA-seq study in Figure 2 should be validated by qPCR

Authors’ response. We thank the reviewer for this suggestion. This point will be addressed as detailed in the Revision Plan. We have selected several transcripts that will be evaluated in independent samples in order to validate the RNAseq results.

- The paper shows siRNA knockdown of c-Myc in KO restores Myogenin RNA/protein but does not fully rescue myotube morphology or differentiation index. This suggests that Trim32 controls additional effectors beyond c-Myc; yet the authors do not pursue other candidate mediators identified in the RNA-seq. The manuscript would be strengthened by systematically testing whether other deregulated transcripts contribute to the phenotype.

Authors’ response. This point will be addressed as detailed in the Revision Plan

- There are concerns with experimental/statistical issues and insufficient replicate reporting. The authors use unpaired two-tailed Student's t-test across many comparisons; multiple testing corrections or ANOVA where appropriate should be used. In Figure EV5B and Figure 6B, the authors perform statistical analyses with control values set to 1. This method masks the inherent variability between experiments and artificially augments p values. Control sample values need to be normalized to one another to have reliable statistical analysis. Myotube morphology and differentiation index quantifications need clear description of fields counted, blind analysis, and number of biological replicates.

Authors’ response. We thank the Reviewer for raising this point.

Regarding the replicates, we clarified in the Methods and Legends that the Trim32 KO experiments have been performed on 3 biological replicates (independent clones) and the same for the reference control (3 independent WT clones), except for the Fig. 6 experiments that were performed on 2 Trim32 KO and 2 WT clones. All the Western Blots, immunofluorescence, qPCR data are representative of the results of at least 3 independent experiments unless otherwise stated. We reported the number and type of replicates as well as the microscope fields analyzed.

We repeated the statistical analyses of the data in Figure 5G, EV5D, EV5E, employing more appropriately the 2-way-ANOVA test, as suggested, and we now reported this info in the graphs and legends.

We thank the Reviewer for raising this point, we agree and substituted the graphs in Fig. EV5B and 6B showing the control values normalised as suggested. The statistical analyses now reflect this change.

-Some English mistakes require additional read-throughs. For example: "Indeed, Trim32 has no effect on the stability of c-Myc mRNA in proliferating conditions, but upon induction of differentiation the stability of c-Myc mRNA resulted enhanced in Trim32 KO clones (Fig. 5G, Fig. EV5D and 5E)."

Authors’ response. We re-edited this revised version of the manuscript as suggested.

-Results in Figure 5A should be quantified

Authors’ response. We amended this point by quantifying the results shown in Fig. 5A, we added the graph of the quantification of 3 experimental replicates to the Figure. Quantification confirms that no statistically significant difference is observed. The Figure and the relative legend are modified accordingly.

-Based on the nuclear marker p84, the separation of cytoplasmic and nuclear fractions is not ideal in Figure 5D

Authors’ response. We agree with the Reviewer that the presence of p84 also in the cytoplasmic fraction is not ideal. Regrettably, we observed this faint p84 band in all the experiments performed. We think however, that this is not impacting on the result that clearly shows that c-Myc and Trim32 are never detected in the same compartment.

-In Figure 6, it is not appropriate to perform statistical analyses on only two data points per condition.

Authors’ response. We agree with the Reviewer and we now show the graph of the results of the 3 technical replicates for 2 biological replicates and do not indicate any statistics (Fig. 6B). The graph was also modified according to a previous point raised.

-The nuclear MYOG phenotype is very interesting; could this be related to requirements of TRIM32 in fusion?

Authors’ response. We agree with the Reviewer that Trim32 might also be necessary for myoblast fusion. This point is however beyond the scope of the present study and will be addressed in future work.

- The hypothesis that TRIM32 destabilizes c-Myc mRNA is intriguing but requires stronger mechanistic support. This would be more convincing with RNA immunoprecipitation to test direct association with c-Myc mRNA, and/or co-immunoprecipitation to identify interactions between TRIM32 and proteins involved in mRNA stability. The study would also be strengthened by reporter assays, such as c-Myc 3′UTR luciferase constructs in WT and KO cells, to directly demonstrate 3′UTR-dependent regulation of mRNA stability.

Authors’ response. This point will be addressed as detailed in the Revision Plan

Reviewer #3 (Significance (Required)):

The manuscript presents a minor conceptual advance in understanding TRIM32 function in myogenic differentiation. Its main limitation is that all experiments were performed in C2C12 cells. While C2C12 are a classical system to study muscle differentiation, they are an immortalized, long-cultured, and genetically unstable line that represents a committed myoblast stage rather than bona fide satellite cells. They therefore do not fully model the biology of early regenerative responses. Several TRIM32 phenotypes reported in the literature differ between primary satellite cells and cell lines, and the authors themselves note such discrepancies. Extrapolating these findings to LGMDR8 pathogenesis without validation in primary human myoblasts, satellite cell assays, or in vivo regeneration models is therefore not justified. Previous work has already established clear roles for TRIM32 in mouse satellite cells in vivo and in patient myoblasts in vitro, whereas this study introduces a novel link to c-Myc regulation during differentiation. In addition, without mechanistic evidence, the central claim that TRIM32 regulates c-Myc mRNA stability remains descriptive and incomplete. Nevertheless, the results will be of interest to researchers studying LGMD and to those exploring TRIM32 biology in broader contexts. I review this manuscript as a muscle biologist with expertise in satellite cell biology and transcriptional regulation.

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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

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1. The text contains several...

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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...

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1. The text contains several...

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Referee #3

Evidence, reproducibility and clarity

In this paper, the authors examine the role of TRIM32, implicated in limb girdle muscular dystrophy recessive 8 (LGMDR8), in the differentiation of C2C12 mouse myoblasts. Using CRISPR, they generate mutant and wild-type clones and compare their differentiation capacity in vitro. They report that Trim32-deficient clones exhibit delayed and defective myogenic differentiation. RNA-seq analysis reveals widespread changes in gene expression, although few are validated by independent methods. Notably, Trim32 mutant cells maintain residual proliferation under differentiation conditions, apparently due to a failure to downregulate c-Myc. Translation inhibition experiments suggest that TRIM32 promotes c-Myc mRNA destabilization, but this conclusion is insufficiently substantiated. The authors also perform rescue experiments, showing that c-Myc knockdown in Trim32-deficient cells alleviates some differentiation defects. However, this rescue is not quantified, was conducted in only two of the three knockout lines, and is supported by inappropriate statistical analysis of gene expression. Overall, the manuscript in its current form has substantial weaknesses that preclude publication. Beyond statistical issues, the major concerns are: (1) exclusive reliance on the immortalized C2C12 line, with no validation in primary/satellite cells or in vivo, (2) insufficient mechanistic evidence that TRIM32 acts directly on c-Myc mRNA, and (3) overinterpretation of disease relevance in the absence of supporting patient or in vivo data. Please find more details below:

• TRIM32 complementation / rescue experiments to exclude clonal or off-target CRISPR effects and show specificity are lacking.
• The authors link their in vitro findings to LGMDR8 pathogenesis and propose that the Trim32-c-Myc axis may serve as a central regulator of muscle regeneration in the disease. However, LGMDR8 is a complex disorder, and connecting muscle wasting in patients to differentiation assays in C2C12 cells is difficult to justify. No direct evidence is provided that the proposed mRNA mechanism operates in patient-derived samples or in mouse satellite cells. Moreover, the partial rescue achieved by c-Myc knockdown (which does not fully restore myotube morphology or differentiation index) further suggests that the disease connection is not straightforward. Validation of the TRIM32-c-Myc axis in a physiologically relevant system, such as LGMD patient myoblasts or Trim32 mutant mouse cells, would greatly strengthen the claim. -Some gene expression changes from the RNA-seq study in Figure 2 should be validated by qPCR
• The paper shows siRNA knockdown of c-Myc in KO restores Myogenin RNA/protein but does not fully rescue myotube morphology or differentiation index. This suggests that Trim32 controls additional effectors beyond c-Myc; yet the authors do not pursue other candidate mediators identified in the RNA-seq. The manuscript would be strengthened by systematically testing whether other deregulated transcripts contribute to the phenotype.
• There are concerns with experimental/statistical issues and insufficient replicate reporting. The authors use unpaired two-tailed Student's t-test across many comparisons; multiple testing corrections or ANOVA where appropriate should be used. In Figure EV5B and Figure 6B, the authors perform statistical analyses with control values set to 1. This method masks the inherent variability between experiments and artificially augments p values. Control sample values need to be normalized to one another to have reliable statistical analysis. Myotube morphology and differentiation index quantifications need clear description of fields counted, blind analysis, and number of biological replicates. -Some English mistakes require additional read-throughs. For example: "Indeed, Trim32 has no effect on the stability of c-Myc mRNA in proliferating conditions, but upon induction of differentiation the stability of c-Myc mRNA resulted enhanced in Trim32 KO clones (Fig. 5G, Fig. EV5D and 5E)." -Results in Figure 5A should be quantified -Based on the nuclear marker p84, the separation of cytoplasmic and nuclear fractions is not ideal in Figure 5D -In Figure 6, it is not appropriate to perform statistical analyses on only two data points per condition. -The nuclear MYOG phenotype is very interesting; could this be related to requirements of TRIM32 in fusion?
• The hypothesis that TRIM32 destabilizes c-Myc mRNA is intriguing but requires stronger mechanistic support. This would be more convincing with RNA immunoprecipitation to test direct association with c-Myc mRNA, and/or co-immunoprecipitation to identify interactions between TRIM32 and proteins involved in mRNA stability. The study would also be strengthened by reporter assays, such as c-Myc 3′UTR luciferase constructs in WT and KO cells, to directly demonstrate 3′UTR-dependent regulation of mRNA stability.

Significance

The manuscript presents a minor conceptual advance in understanding TRIM32 function in myogenic differentiation. Its main limitation is that all experiments were performed in C2C12 cells. While C2C12 are a classical system to study muscle differentiation, they are an immortalized, long-cultured, and genetically unstable line that represents a committed myoblast stage rather than bona fide satellite cells. They therefore do not fully model the biology of early regenerative responses. Several TRIM32 phenotypes reported in the literature differ between primary satellite cells and cell lines, and the authors themselves note such discrepancies. Extrapolating these findings to LGMDR8 pathogenesis without validation in primary human myoblasts, satellite cell assays, or in vivo regeneration models is therefore not justified. Previous work has already established clear roles for TRIM32 in mouse satellite cells in vivo and in patient myoblasts in vitro, whereas this study introduces a novel link to c-Myc regulation during differentiation. In addition, without mechanistic evidence, the central claim that TRIM32 regulates c-Myc mRNA stability remains descriptive and incomplete. Nevertheless, the results will be of interest to researchers studying LGMD and to those exploring TRIM32 biology in broader contexts. I review this manuscript as a muscle biologist with expertise in satellite cell biology and transcriptional regulation.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, the authors sought to investigate the molecular role of Trim32, a tripartite motif-containing E3 ubiquitin ligase often associated with its dysregulation in Limb-Girdle Muscular Dystrophy Recessive 8 (LGMDR8), and its role in the dynamics of skeletal muscle differentiation. Using a CRISPR-Cas9 model of Trim32 knockout in C2C12 murine myoblasts, the authors demonstrate that loss of Trim32 alters the myogenic process, particularly by impairing the transition from proliferation to differentiation. The authors provide evidence in the way of transcriptomic profiling that displays an alteration of myogenic signaling in the Trim32 KO cells, leading to a disruption of myotube formation in-vitro. Interestingly, while previous studies have focused on Trim32's role in protein ubiquitination and degradation of c-Myc, the authors provide evidence that Trim32-regulation of c-Myc occurs at the level of mRNA stability. The authors show that the sustained c-Myc expression in Trim32 knockout cells disrupts the timely expression of key myogenic factors and interferes with critical withdrawal of myoblasts from the cell cycle required for myotube formation. Overall, the study offers a new insight into how Trim32 regulates early myogenic progression and highlights a potential therapeutic target for addressing the defects in muscular regeneration observed in LGMDR8.

Major Comments:

The work is a bit incremental based on this: https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0030445 And this: https://www.nature.com/articles/s41418-018-0129-0 To their credit, the authors do cite the above papers.

The authors do provide compelling evidence that Trim32 deficiency disrupts C2C12 myogenic differentiation and sustained c-Myc expression contributes to this defective process. However, while knockdown of c-Myc does restore Myogenin levels, it was not sufficient to normalize myotube morphology or differentiation index, suggesting an incomplete picture of the Trim32-dependent pathways involved. The authors should qualify their claim by emphasizing that c-Myc regulation is a major, but not exclusive, mechanism underlying the observed defects. This will prevent an overgeneralization and better align the conclusions with the author's data. The authors provide a thorough and well-executed interrogation of cell cycle dynamics in Trim32 KO clones, combining phosphor-histone H3 flow cytometry of DNA content, and CFSE proliferation assays. These complementary approaches convincingly show that, while proliferation states remain similar in WT and KO cells, Trim32-deficient myoblasts fail in their normal withdraw from the cell cycle during exposure to differentiation-inducing conditions. This work adds clarity to a previously inconsistent literature and greatly strengthens the study.

The transcriptomic analysis (detailed In the "Transcriptomic analysis of Trim32 WT and KO clones along early differentiation" section of Results) is central to the manuscript and provides strong evidence that Trim32 deficiency disrupts normal differentiation processes. However, the description of the pathway enrichment results is highly detailed and somewhat compressed, which may make it challenging for readers to following the key biological 'take-homes'. The narrative quickly moves across their multiple analyses like MDS, clustering, heatmaps, and bubble plots without pausing to guide the reader through what each analysis contributes to the overall biological interpretation. As a result, the key findings (reduced muscle development pathways in KO cells and enrichment of cell cycle-related pathways) can feel somewhat muted. The authors may consider reorganizing this section, so the primary biological insights are highlighted and supported by each of their analyses. This would allow the biological implications to be more accessible to a broader readership.

The work would be greatly strengthened by the conclusion of LGMDR8 primary cells, and rescue experiments of TRIM32 to explore myogenesis. Also, EU (5-ethynyl uridine) pulse-chase experiments to label nascent and stable RNA coupled with MYC pulldowns and qPCR (or RNA-sequencing of both pools) would further enhance the claim that MYC stability is being affected.

"On one side, c-Myc may influence early stages of myogenesis, such as myoblast proliferation and initial myotube formation, but it may not contribute significantly to later events such as myotube hypertrophy or fusion between existing myotubes and myocytes. This hypothesis is supported by recent work showing that c-Myc is dispensable for muscle fiber hypertrophy but essential for normal MuSC function (Ham et al, 2025)." Also address and discuss the following, as what is currently written is not entirely accurate: https://www.embopress.org/doi/full/10.1038/s44319-024-00299-z and https://journals.physiology.org/doi/prev/20250724-aop/abs/10.1152/ajpcell.00528.2025

Minor Comments:

Z-score scale used in the pathway bubble plot (Figure 2C) could benefit from alternative color choices. Current gradient is a bit muddy and clarity for the reader could be improved by more distinct color options, particularly in the transition from positive to negative Z-score.

Clarification on the rationale for selecting the "top 18" pathways would be helpful, as it is not clear if this cutoff was chosen arbitrarily or reflects a specific statistical or biological threshold.

The authors alternates between using "Trim 32 KO clones" and "KO clones" throughout the manuscript. Consistent terminology across figures and text would improve readability.

Cell culture methodology does not specify passage number or culture duration (only "At confluence") before differentiation. This is important, as C2C12 differentiation potential can drift with extended passaging.

Significance

General Assessment:

This study provides a thorough investigation of Trim32's role the processes related to skeletal muscle differentiation using a CRISPR-Cas9 knockout C2C12 model. The strengths of this study lie in the multi-layered experimental approach as the authors incorporated transcriptomics, cell cycle profiling, and stability assays which collectively build a strong case for their hypothesis that Trim32 is a key factor in the normal regulation of myogenesis. The work is also strengthened by the use of multiple biological and technical replicates, particularly the independent KO clones which helps address potential clonal variation issues that could occur. The largest limitation to this study is that, while the c-Myc mechanism is well explored, the other Trim32-dependent pathways associated with the disruption (implicated by the incomplete rescue by c-Myc knockdown) are not as well addressed. Overall however, the study convincingly identifies a critical function for Trim32 during skeletal muscle differentiation.

Advance:

To my knowledge, this is the first study to demonstrate the mRNA stability level of c-Myc regulation by Trim32, rather than through the ubiquitin-mediated protein degradation. This work will advance the current understanding and provide a more complete understanding of Trim32's role in c-Myc regulation. Beyond c-Myc, this work highlights the idea that TRIM family proteins can influence RNA stability which could implicate a broader role in RNA biology and has potential for future therapeutic targeting.

Audience:

This research will be of interest to an audience that focuses on broad skeletal muscle biology but primarily to readers with more focused research such as myogenesis and neuromuscular disease (LGMDR8 in particular) where the defined Trim32 governance over early differentiation checkpoints will be of interest. It will also provide mechanistic insights to those outside of skeletal muscle that study TRIM family proteins, ubiquitin biology, and RNA regulation. For translational/clinical researchers, it identifies the Trim32/c-Myc axis as a potential therapeutic target for LGMDR8 and related muscular dystrophies.

Expertise:

My expertise lies in skeletal muscle biology, gene editing, transgenic mouse models, and bioinformatics. I feel confident evaluating the data and conclusions as presented.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Xiong and colleagues investigate the mechanisms operating downstream to TRIM32 and controlling myogenic progression from proliferation to differentiation. Overall, the bulk of the data presented is robust. Although further investigation of specific aspects would make the conclusions more definitive (see below), it is an interesting contribution to the field of scientists studying the molecular basis of muscle diseases. In my opinion, a few aspects would improve the manuscript.

Firstly, the conclusion that Trim32 regulates c-Myc mRNA stability could be expanded and corroborated by further mechanistic studies:

1. Studies investigating whether Tim32 binds directly to c-Myc RNA. Moreover, although possibly beyond the scope of this study, an unbiased screening of RNA species binding to Trim32 would be informative.
2. If possible, studies in which the overexpression of different mutants presenting specific altered functional domains (NHL domain known to bind RNAs and Ring domain reportedly involved in protein ubiquitination) would be used to test if they are capable or incapable of rescuing the reported alteration of Trim32 KO cell lines in c-Myc expression and muscle maturation. An optional aspect that might be interesting to explore is whether the alterations in c-Myc expression observed in C2C12 might be replicated with primary myoblasts or satellite cells devoid of Trim32.

I also have a few minor points to highlight:

• It is unclear if the differences highlighted in graphs 5G, EV5D, and EV5E are statistically significant.
• On page 10, it is stated that c-Myc down-regulation cannot rescue KO myotube morphology fully nor increase the differentiation index significantly, but the corresponding data is not shown. Could the authors include those quantifications in the manuscript?

Significance

The manuscript offers several strengths. It provides novel mechanistic insight by identifying a previously unrecognized role for Trim32 in regulating c-Myc mRNA stability during the onset of myogenic differentiation. The study is supported by a robust methodology that integrates CRISPR/Cas9 gene editing, transcriptomic profiling, flow cytometry, biochemical assays, and rescue experiments using siRNA knockdown. Furthermore, the work has a disease relevance, as it uncovers a mechanistic link between Trim32 deficiency and impaired myogenesis, with implications for the pathogenesis of LGMDR8. At the same time, the study has some limitations. The findings rely exclusively on the C2C12 myoblast cell line, which may not fully represent primary satellite cell or in vivo biology. The functional rescue achieved through c-Myc knockdown is only partial, restoring Myogenin expression but not the full differentiation index or morphology, indicating that additional mechanisms are likely involved. Although evidence supports a role for Trim32 in mRNA destabilization, the precise molecular partners-such as RNA-binding activity, microRNA involvement, or ligase function-remain undefined. Some discrepancies with previous studies, including Trim32-mediated protein degradation of c-Myc, are acknowledged but not experimentally resolved. Moreover, functional validation in animal models or patient-derived cells is currently lacking.

Despite these limitations, the study represents an advancement for the field. It shifts the conceptual framework from Trim32's canonical role in protein ubiquitination to a novel function in RNA regulation during myogenesis. It also raises potential clinical implications by suggesting that targeting the Trim32-c-Myc axis, or modulating c-Myc stability, may represent a therapeutic strategy for LGMDR8. This work will be of particular interest to muscle biology researchers studying myogenesis and the molecular basis of muscle disease, RNA biology specialists investigating post-transcriptional regulation and mRNA stability, and neuromuscular disease researchers and clinicians seeking to identify new molecular targets for therapeutic intervention in LGMDR8.

The Reviewer expressing this opinion is an expert in muscle stem cells, muscle regeneration, and muscle development.

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Reply to the reviewers

We are grateful to the reviewers for their thoughtful and constructive evaluations of our manuscript. Their comments helped us clarify key aspects of the study and strengthen both the presentation and interpretation of our findings. The central goal of this work is to dissect how the opposing activities of GATA4 and CTCF coordinate chromatin topology and transcriptional timing during human cardiomyogenesis. The reviewers’ feedback has allowed us to refine this message and better contextualize our results within the broader framework of chromatin regulation and cardiac development.

In response to the reviews, in our preliminary revision we have already implemented substantial improvements to the manuscript, including additional analyses, clearer data visualization, and revisions to the text to avoid overinterpretation. These refinements enhance the robustness of our conclusions without altering the overall scope of the study. A small number of additional analyses and experiments are ongoing and will be added to the full revision, as detailed below.

We believe that the revised manuscript, together with the planned updates, fully addresses the reviewers’ concerns and substantially strengthens the contribution of this work to the field.

Reviewer 1 – Point 1:

In the datasets you are examining, what are the relative percentages in each of the four groups relating compartmentalization change to expression change (A→B, expression up; A→B, down; B→A, up; B→A, down)?

We quantified compartment–expression relationships using Hi-C and bulk RNA-seq from H9 ESCs and CMs. The percentages for each category are shown below and incorporated into updated Figure S2H.

Group

Downregulated in CM

Upregulated in CM

A-to-A

11.92%

8.44%

A-to-B

18.20%

2.79%

B-to-A

7.96%

18.07%

B-to-B

14.36%

6.44%

A chi-squared test comparing observed vs. expected distributions (based on gene density across bins) confirmed a strong association between compartment dynamics and transcriptional behavior. B-to-A genes are significantly enriched among genes upregulated in CMs, while A-to-B genes are enriched among those downregulated (updated Figure S2H).

We next assessed with GSEA how these gene classes respond to GATA4 and CTCF knockdown. In 2D CMs, GATA4 knockdown reduces expression of CM-upregulated B-to-A genes and increases expression of CM-downregulated A-to-B genes, whereas CTCF knockdown produces the opposite pattern (updated Figure 2F).

Applying the same analysis to cardioid bulk RNA-seq (updated Figure 4E) revealed the strongest effects in SHF-RV organoids, consistent with monolayer data. In SHF-A organoids, only GATA4 knockdown had a measurable impact on CM-upregulated B-to-A and CM-downregulated A-to-B genes. Because the subsets of CM-downregulated B-to-A and CM-upregulated A-to-B genes were very small and showed no consistent trends, Figure 4 focuses on the two informative categories only. The full classification is provided in Reviewer Figure 1 below.

(The figure cannot be rendered in this text-only format)

Reviewer Figure 1. GSEA for CM-upregulated B-to-A and CM-downregulated A-to-B genes. p-values by Adaptive Monte-Carlo Permutation test.

Reviewer 1 – Point 2

This phrase in the abstract is imprecise: ‘whereas premature CTCF depletion accelerates yet confounds cardiomyocyte maturation.’

---

The abstract has been revised to: “whereas premature CTCF depletion accelerates yet alters cardiomyocyte maturation.” (lines 29-30).

Reviewer 1 – Point 3

Regarding this statement: "Disruption of [3D chromatin architecture] has been linked to genetic dilated cardiomyopathy (DCM) caused by lamin A/C mutations8,9, and mutations in chromatin regulators are strongly enriched in de novo congenital heart defects (CHD)10, underscoring their pathogenic relevance11." The first studies to implicate chromatin structural changes in heart disease, including the role of CTCF in that process, were PMID: 28802249, a model of acquired, rather than genetic, disease.

We added the following sentence to the paragraph introducing CTCF: “Moreover, depletion of CTCF in the adult cardiomyocytes leads to heart failure28,29.” (line 72)

Reviewer 1 – Point 4

Can you quantify this statement: ‘the compartment switch coincided with progressive reduction of promoter–gene body interactions’?

We quantified promoter–gene body contacts by calculating the area under the curve (AUC) of the virtual 4C signal derived from H9 Hi-C data across differentiation. As a result of this analysis we added the following sentence: “Quantitatively, interactions between the TTN promoter and its gene body decreased by ~55% from the pluripotent stage to day 80 cardiomyocytes.” (lines 89-91).

Reviewer 1 – Point 5

Regarding this statement: "six regions became less accessible in CMs, correlating with ChIP-seq signal for the ubiquitous architectural protein CTCF." I don't see 6 ATAC peaks in either TTN trace in Figure 1A.

We corrected the text as it follows: “TTN experienced clear changes in chromatin accessibility during CM differentiation: ATAC-seq identified two CM-specific peaks that correlated with ChIP-seq signal for the cardiac pioneer TF GATA4 at the two promoters, one driving full length titin and the other the shorter cronos isoform. In contrast, two regions became less accessible in CMs, correlating with two of the six ChIP-seq peaks for the ubiquitous architectural protein CTCF” (lines 93-97). We attribute the differences between ChIP-seq and ATAC-seq profiles to methodological sensitivity and/or biological variability between datasets generated in different laboratories and cell batches.

Reviewer 1 – Point 6

Western blots need molecular weight markers.

We edited the relevant panels accordingly (updated Figures 1E and 2B).

Reviewer 1 – Point 7

Regarding this statement: "The decrease in CTCF protein levels may explain its selective detachment from TTN during cardiomyogenesis." At face value, these findings suggest the opposite: i.e. that a massive downregulation of CTCF at protein level should affect its binding across the genome, which is not tested and is hard to evaluate between ChIP-seq studies from different groups and from different developmental timeframes.

We revised the text to avoid implying selective detachment and performed a genome-wide analysis of CTCF occupancy using ENCODE ChIP-seq datasets generated by the same laboratory with matched protocols in hESCs and hESC-derived CMs. This analysis shows that 43.2% of CTCF sites present in ESCs are lost in CMs, whereas only 5.7% are gained, confirming a broad reduction in CTCF binding during differentiation. These results are now included in__ updated Figure 1B__.

Reviewer 1 – Point 8a

A couple thoughts on the FISH experiments in Figure 2. A claim of 'impaired B-A transition' would be more convincing if you show, by FISH, that the relative distance of TTN from lamin B increases with differentiation.

Although prior work from us and others has established that TTN transitions from the nuclear periphery in hESCs to a more internal position during cardiomyogenesis (Poleshko et al. 2017; Bertero et al. 2019a), we are reproducing this trajectory in WTC11 hiPSCs as part of the FISH experiments for the full revision.

__Reviewer 1 – Point 8b __

In the [FISH] images: are you showing a total projection of all z planes? One assumes the quantitation is relative to a 3D reconstruction in which the lamin B signal is restricted to the periphery. Have you shown this? __

Quantification was performed on full 3D reconstructions from Z-stacks, as detailed in the Methods (lines 721-727). While the original submission displayed maximum-intensity projections, updated Figure 2D and Figure S2E now show representative single optical sections, which more clearly highlight the spatial relationship between the TTN locus and the nuclear lamina.

Reviewer 1 – Point 8c

Lastly, these data are very interesting and important, provoking reexamination of your interpretation of the results in Figure 1. Figure 1 was interpreted to show that less CTCF binding led to decreased lamina (and thus B compartment) association during development. Figure 2 shows that depleting CTCF does not change association of TTN with lamina.

Our interpretation is that by day 25 of hiPSC-CM differentiation the TTN locus may have reached its maximal radial repositioning even in control cells, limiting the ability to detect earlier effects of CTCF depletion. To test whether CTCF knockdown accelerates lamina detachment at earlier stages, we are repeating the FISH analysis for the inducible CTCF knockdown line at multiple time points during differentiation.

Reviewer 1 – Point 9

A thought about this statement: "Altogether, these results suggest that GATA4 and CTCF function as positive and negative regulators of B-to-A compartment switching, likely acting through global and local chromatin remodeling, respectively." GATA4 induces TTN expression and its knockdown prevents TTN expression-the evidence that GATA4 affects compartmentalization is unclear. By activating the gene, GATA4 may shift TTN to B classification.

Our current data do not allow us to disentangle whether GATA4-driven transcriptional activation precedes or follows the B-to-A compartment shift. We have therefore removed the mechanistic speculation from this sentence to avoid overinterpretation. Nevertheless, the analyses in updated Figure 2F, discussed in the response to Reviewer 1 - Point 1, show that GATA4 knockdown preferentially reduces expression of CM-upregulated B-to-A genes, while CTCF knockdown has the opposite effect, supporting the conclusion that both factors influence the transcriptional programs associated with B-to-A transitions.

Reviewer 1 – Point 10

__I'm not sure what I am looking at in Figure 3C. Are those traces integration of interactions over a defined window? "Each [mutant is] clearly different from WT" is not obvious from the presentation. The histograms are plotting AUC of what? Interactions of those peaks with the mutated region? I genuinely appreciate how laborious this experiment must have been and encourage you to explain better what you are showing. __

We revised the main text to avoid overstating the differences (“clearly” “in a similar manner”, line 192) and expanded the l__egends of updated Figures 3C–D__ to clarify what is being shown: “(C) 4C-seq in hiPSCs using the promoter-proximal region of TTN as viewpoint. The top panel shows raw interaction profiles. The lower panels plot pairwise differences between conditions to reveal subtle changes. A schematic indicating the 4C viewpoint is included for clarity. Right inset: zoom of the CBS4–5 region. Mean of n = 3 cultures. (D) AUC of the differential 4C-seq signal for defined intervals (panel C). p-values by one-sample t-test against μ = 0.”. We also added a visual cue in updated Figure 3C indicating the 4C viewpoint to facilitate interpretation.

Reviewer 1 – Point 11

Again acknowledging how challenging these experiments are: when you mutant a locus, you change CTCF binding but you also change the DNA. Thus, attributing the changes in interactions to presence/absence of CTCF binding is difficult, because the DNA substrate itself has changed. Perhaps you are presenting all of this as a negative result, given the modest effect on transcription, which is as important as a positive result, given the assumptions usually made about such things. But the results are not clearly described and your interpretation seems to go between implying the structural change causative and being agnostic.

We recognize that deleting a genomic region can affect both CTCF binding and the DNA substrate itself. For this reason, we implemented two parallel genome-editing strategies:

(1) a straightforward Cas9-mediated deletion of ~100 bp centered on each CBS, and

(2) a more precise HDR approach replacing only the 20 bp core CTCF motif.

Because the HDR strategy succeeded, all downstream analyses were carried out on these minimal edits, which substantially limit disruption of other transcription factor motifs and reduce the likelihood of sequence-dependent polymer effects unrelated to CTCF.

Nevertheless, to avoid implying unwarranted causality in the absence of more conclusive evidence, we added a paragraph to the Discussion outlining these limitations, including the sentence: “Our study also reflects general challenges in separating chromatin-architectural and transcriptional mechanisms. Although the CBS edits were restricted to the core CTCF motifs, additional sequence-dependent effects cannot be fully excluded, and we therefore interpret the resulting changes as consistent with—but not exclusively due to—loss of CTCF binding.” (lines 365-368)

Reviewer 1 - Point 12.

Figure 4C: since you have RNA-seq data, a much more objective way to present these data would be to show all data (again, A-B, up; A-B, down; B-A, up; B-A, down) and the effects of CTCF or GATA4. Regardless, you can still focus on the cardiac specific genes. But my guess is if you examine all genes, the pattern you show in panel C will not be present in the majority of cases. Furthermore, if this hypothesis is wrong, such an analysis will allow you to identify other genes affected by the mechanisms you describe and your analysis will test whether these mechanisms are in fact conserved at different loci.

As outlined in our response to Point 1, we extended the analysis to all genes undergoing compartment changes and incorporated this into the cardioid RNA-seq dataset. This revealed a clear and consistent relationship between GATA4 or CTCF knockdown and the expression of B-to-A and A-to-B gene classes (updated Figure 4E).

Reviewer 2 - Point 1.1

1. CTCF regulation at TTN locus:

(1) Figure 1A: The claim of the authors about convergent CTCF sites and transcriptional activation of TTN is quite simplistic. This claim is only valid when we know where cohesin is loaded. If cohesin is loaded at then intragenic GATA4 binding site, then the only important CTCF sites is at the promoter of TTN. I suggest that the authors read few more publications which may help the authors to better understand how cohesin and CTCF team up to regulate transcription, such as Hsieh et al., Nature Genetics, 2022; Liu et al., Nature Genetics, 2021; Rinzema et al., Nature Structural and Molecular Biology, 2022.

__Suggestion: The authors should add cohesin (RAD21/SMC1A) and NIPBL ChIP-seq for better interpretation. __

In line with the reviewer’s insightful suggestion, we integrated cohesin ChIP-seq data into updated Figure 1A. Specifically, we added a RAD21 ChIP-seq track from hESCs, which provides direct evidence of cohesin occupancy across the TTN locus. RAD21 binding closely parallels CTCF binding at five sites within the gene body, supporting a model in which promoter-proximal CTCF anchors cohesin to stabilize repressive loops at this locus. This analysis substantially strengthens the mechanistic framework and is consistent with the studies recommended by the reviewer, which we have now cited (lines 68 and 104).

Reviewer 2 - Point 1.2. (2) Figure 3B: If delta2CBS only has heterozygenous deletion of CBS6, why we would expect the binding will be weaken to 50%. However, the CTCF binding is reduced to around 1/10 in the ChIP-qPCR. How do the authors explain this?

Sequencing of the Δ2CBS line shows that one CBS6 allele carries the intended EcoRI replacement, while the second allele contains a 2-bp deletion within the core CTCF motif (Figure S3C). Remarkably, this small deletion is sufficient to abolish CTCF binding, resulting in complete loss of occupancy at CBS6 despite heterozygosity. We clarified this in the text as follows: “CTCF ChIP-qPCR in hiPSCs confirmed complete loss of CTCF binding at the targeted sites, including CBS6 in the Δ2CBS line, indicating that the 2-bp deletion sufficed to disrupt CTCF binding while occupancy at other CBSs remained unaffected.” (lines 187–189).

Reviewer 2 - Point 1.3a (3) Figure 3C: There are two problems with the 4C experiments: (a) The changes are really mild. In fact, none of the p-values in Figure 3D are significant.

The effect of deleting CBS1 is indeed modest, consistent with reports that individual CTCF binding sites often show functional redundancy (i.e., Rodríguez-Carballo et al. 2017; Barutcu et al. 2018; Kang et al. 2021). Nevertheless, our 4C-seq experiments have reproducibly shown the same directional trend across biological replicates. To increase statistical power and more rigorously assess the robustness of this effect, we are generating additional 4C replicates as part of the full revision.

Reviewer 2 - Point 1.3b [In the 4C experiments] (b) The authors should also consider a model that CTCF directly serves as a repressor. In this way, 3D genome may not be involved. B-A switch is simply caused by the activation of the locus.

We now explicitly acknowledge this possibility in the Discussion. The revised text states: “Moreover, our data cannot unambiguously separate CTCF’s architectural role from potential direct repressive activity. Both mechanisms could contribute to the observed effects, and our findings likely reflect the combined influence of CTCF on chromatin topology and gene regulation.” (lines 368–371).

Reviewer 2 - Point 2.1a 2. __(CTCF) detachment: The authors mentioned few times "detachment". In the context of this manuscript, the authors indicate detachment from nuclear lamina. However, the authors haven't provide convincing evidence about this. __

In the two instances where we used the term “detachment,” we intended it to refer exclusively to reduced CTCF binding to DNA, not to lamina repositioning. To avoid ambiguity, we have replaced “detachment” with “reduced binding” in both locations (lines 123 and 329). We do not use this term to describe TTN–lamina positioning.

Reviewer 2 - Point 2.1b (1) Figure 1D: I doubt whether such changes of CTCF protein abundance will lead to LAD detachment. Suggest the authors read van Schaik et al., Genome Biology, 2022. With the full depletion of CTCF, the effects on LADs are still very restricted.

We agree that the observed correlation between reduced CTCF levels and the relocation of TTN away from a LAD does not establish causality. As outlined in our response to Reviewer 1 – Point 8c, we are performing additional FISH experiments at earlier differentiation stages in the CTCF inducible knockdown line to directly assess whether partial CTCF depletion is sufficient to alter the timing of TTN–lamina separation.

Reviewer 2 - Point 2.2 (2) Figure 2D: Lamin B1 should be mostly at nuclear periphery. I have few questions: (1) is the antibody specific? (2) do these cells carry mutation in LMNB1 gene? (3) is the staining actually LMNA?

As also clarified in response to Reviewer 1 – Point 8b, the original images displayed maximum-intensity projections of Z-stacks, which obscured the peripheral distribution of LMNB1. We have updated Figure 2D and Figure S2E to show representative individual optical sections, which more clearly display the expected peripheral LMNB1 signal. We also confirm that the antibody used is specific for LMNB1 and previously validated (Bertero et al. 2019b), and that the WTC11-derived lines used in this study carry no mutation in LMNB1.

Reviewer 2 - Point 3

3. Opposite functions of GATA4 and CTCF: These data in Figure 5E-H argues the opposite role of GATA4 and CTCF in transcriptional regulation. Would it be that CTCF KD just affected cell proliferation, which is actually known for many cell types, rather than affect CM differentiation process? If this is the reason, inversed correlation between CTCF KD and GATA4 KD in Figure 4D could also be explained by opposite effects on cell cycle.

We directly evaluated this possibility. In FHF–LV cardioids, cell cycle profiling in Figure 6C and Figure S6C (now S7C) showed that CTCF knockdown does not alter the distribution of CMs across G1/S/G2–M phases, in contrast to the marked increase in proliferation observed with GATA4 knockdown.

Because this comment referred specifically to the SHF data, we also analyzed mitotic gene expression in the SHF–RV bulk RNA-seq dataset using GSEA. CTCF knockdown did not significantly enrich any cell cycle–related gene sets, whereas GATA4 knockdown produced a strong enrichment for mitotic cell cycle terms, in line with FHF-LV data (Reviewer Figure 2).

These results are summarized in updated Figure S5C, reporting also the results of the broader GSEA analysis, and together indicate that the transcriptional divergence between CTCF and GATA4 knockdown is not simply explained by opposing effects on proliferation.

(The figure cannot be rendered in this text-only format)

Reviewer Figure 2. GSEA for mitotic cell cycle in SHF-RV after inducible knockdown of CTCF (left) or GATA4 (right). p-values by Adaptive Monte-Carlo Permutation test.

Reviewer 2 - Point 4 4. In discussion, the authors suggested that CTCF is a local chromatin remodeller. In my view, association with local chromatin compaction doesn't qualify CTCF as a chromatin remodeler. To my knowledge, CTCF does not have an enzymatic domain, then how does it remodel chromatin?

Our intended meaning was that CTCF shapes 3D chromatin architecture through its role in organizing intergenic looping, not that it remodels chromatin enzymatically. To avoid confusion, we have removed the original sentence from the Discussion.

Reviewer 2 - Point 5. 5. Some conclusions are drawn based on insignificant p-values, e.g. Figure 2F, Figure 3D, etc. The authors should be careful about their conclusion, and tone down their statement for the observations have borderline significance.

The conclusions based on bulk RNA-seq have been revised in response to Reviewer 1 – Point 1 (updated Figure 2F). By subsetting B-to-A and A-to-B genes according to their expression dynamics, this analysis now yields clearer and statistically significant differences between conditions.

Regarding the 4C-seq data, as acknowledged in Reviewer 2 – Point 3a, the observed effects are modest. We are generating additional biological replicates to increase statistical power. In the meantime, we have adjusted the text to avoid overstating these findings. The revised manuscript now states: “While the difference did not reach significance, these trends suggest …” (lines 199–200).

Reviewer 2 - Minor comment 1. Minor comments: 1. Figure 1A: (1) I suggest to label two promoters in the gene model. It's unclear in the figure in the current version; (2) I was a bit confused with the way how the authors labeled CTCF directionality. I thought there are a lot of promoters. Why didn't they use triangles?

We updated Figure 1A to label both TTN promoters and indicate their orientation. For CTCF sites, we now clearly display the motif direction and core binding region as determined by FIMO analysis of the CTCF ChIP-seq peaks, improving consistency and interpretability.

Reviewer 2 - Minor comment 2. 2. Figure 2C: I think the drastical reduction of titin-mEGFP levels is only due to the way how the authors analyze their FACS data. Can the author quantify on median fluorescence intensity?

The gating strategy for titin-mEGFP⁺ cells was defined using a reporter-negative control, and cells lacking TNNT2 expression showed no detectable titin-mEGFP signal, confirming the specificity of the gate. To complement this analysis, we also quantified the median fluorescence intensity (MFI) of titin-mEGFP⁺ cells. The MFI analysis corroborates the original findings, showing a significant decrease in GATA4 knockdown and an increase in CTCF knockdown (updated Figure S2D).

__Reviewer 2 - Minor comment 3. 3. Figure S2G: P value should be -log10, I assume. Please label it accurately. __

We appreciate the reviewer pointing out this labeling error. In the revised manuscript, this panel has been removed to accommodate the updated compartment–expression analysis now presented in updated Figure 2H (see response to Reviewer 1 – Point 1), and the issue is no longer applicable.

References

Barutcu AR, Maass PG, Lewandowski JP, Weiner CL, Rinn JL. 2018. A TAD boundary is preserved upon deletion of the CTCF-rich Firre locus. Nat Commun 9: 1444.

Bertero A, Fields PA, Ramani V, Bonora G, Yardımcı GG, Reinecke H, Pabon L, Noble WS, Shendure J, Murry CE. 2019a. Dynamics of genome reorganization during human cardiogenesis reveal an RBM20-dependent splicing factory. Nature communications 10: 1538.

Bertero A, Fields PA, Smith AS, Leonard A, Beussman K, Sniadecki NJ, Kim D-H, Tse H-F, Pabon L, Shendure J, et al. 2019b. Chromatin compartment dynamics in a haploinsufficient model of cardiac laminopathy. Journal of Cell Biology 218: 2919–44.

Kang J, Kim YW, Park S, Kang Y, Kim A. 2021. Multiple CTCF sites cooperate with each other to maintain a TAD for enhancer–promoter interaction in the β-globin locus. The FASEB Journal 35: e21768.

Poleshko A, Shah PP, Gupta M, Babu A, Morley MP, Manderfield LJ, Ifkovits JL, Calderon D, Aghajanian H, Sierra-Pagán JE, et al. 2017. Genome-Nuclear Lamina Interactions Regulate Cardiac Stem Cell Lineage Restriction. Cell 171: 573–587.

Rodríguez-Carballo E, Lopez-Delisle L, Zhan Y, Fabre PJ, Beccari L, El-Idrissi I, Huynh THN, Ozadam H, Dekker J, Duboule D. 2017. The HoxD cluster is a dynamic and resilient TAD boundary controlling the segregation of antagonistic regulatory landscapes. Genes Dev 31: 2264–2281.

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Referee #2

Evidence, reproducibility and clarity

Becca et al. characterized the functions of GATA4 and CTCF in the context of cardiomyogenesis. The authors aim to establish a link between 3D genome changes (A/B compartment and long-range chromatin interactions) and activation of cardiac specific genes such as TTN. They showed opposite effects of GATA4 and CTCF in regulating these genes as well as phenotypical traits. I have the following suggestions and questions:

Major comments:

1. CTCF regulation at TTN locus:

(1) Figure 1A: The claim of the authors about convergent CTCF sites and transcriptional activation of TTN is quite simplistic. This claim is only valid when we know where cohesin is loaded. If cohesin is loaded at then intragenic GATA4 binding site, then the only important CTCF sites is at the promoter of TTN. I suggest that the authors read few more publications which may help the authors to better understand how cohesin and CTCF team up to regulate transcription, such as Hsieh et al., Nature Genetics, 2022; Liu et al., Nature Genetics, 2021; Rinzema et al., Nature Structural and Molecular Biology, 2022.

Suggestion: The authors should add cohesin (RAD21/SMC1A) and NIPBL ChIP-seq for better interpretation. (2) Figure 3B: If delta2CBS only has heterozygenous deletion of CBS6, why we would expect the binding will be weaken to 50%. However, the CTCF binding is reduced to around 1/10 in the ChIP-qPCR. How do the authors explain this?

(3) Figure 3C: There are two problems with the 4C experiments: (a) The changes are really mild. In fact, none of the p-values in Figure 3D are significant; (b) The authors should also consider a model that CTCF directly serves as a repressor. In this way, 3D genome may not be involved. B-A switch is simply caused by the activation of the locus. 2. (CTCF) detachment: The authors mentioned few times "detachment". In the context of this manuscript, the authors indicate detachment from nuclear lamina. However, the authors haven't provide convincing evidence about this.

(1) Figure 1D: I doubt whether such changes of CTCF protein abundance will lead to LAD detachment. Suggest the authors read van Schaik et al., Genome Biology, 2022. With the full depletion of CTCF, the effects on LADs are still very restricted.

(2) Figure 2D: Lamin B1 should be mostly at nuclear periphery. I have few questions: (1) is the antibody specific? (2) do these cells carry mutation in LMNB1 gene? (3) is the staining actually LMNA? 3. Opposite functions of GATA4 and CTCF: These data in Figure 5E-H argues the opposite role of GATA4 and CTCF in transcriptional regulation. Would it be that CTCF KD just affected cell proliferation, which is actually known for many cell types, rather than affect CM differentiation process? If this is the reason, inversed correlation between CTCF KD and GATA4 KD in Figure 4D could also be explained by opposite effects on cell cycle. 4. In discussion, the authors suggested that CTCF is a local chromatin remodeller. In my view, association with local chromatin compaction doesn't qualify CTCF as a chromatin remodeler. To my knowledge, CTCF does not have an enzymatic domain, then how does it remodel chromatin? 5. Some conclusions are drawn based on insignificant p-values, e.g. Figure 2F, Figure 3D, etc. The authors should be careful about their conclusion, and tone down their statement for the observations have borderline significance.

Minor comments:

1. Figure 1A: (1) I suggest to label two promoters in the gene model. It's unclear in the figure in the current version; (2) I was a bit confused with the way how the authors labeled CTCF directionality. I thought there are a lot of promoters. Why didn't they use triangles?
2. Figure 2C: I think the drastical reduction of titin-mEGFP levels is only due to the way how the authors analyze their FACS data. Can the author quantify on median fluorescence intensity?
3. Figure S2G: P value should be -log10, I assume. Please label it accurately.

Significance

Strengths and limitations:

I feel that single-cell analysis and functional analysis of GATA4 and CTCF using cardiac organoid model are elegant. However, the weak part of the manuscript is the link between 3D genome and activation of TTN. I also think the authors should include more possible explanations for the interpretation of some genome organization data (CTCF site deletion, 4C, etc).

Advance: The study does provide useful information to understand transcriptional regulation during cardiac lineage specification. The link between 3D genome and cardiac lineage specification is conceptually nice but needs more data to support.

Audience: developmental biologists who is interested in heart development and molecular biologists with specific interests in gene regulation.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by Becca and others examines the relationship between GATA4 and CTCF in chromatin organization and cardiac maturation. There are several very interesting observations that lead to potentially new insights into the relationship between genome folding, gene expression and the relationship between transcription factors and chromatin structural proteins. To better justify their interpretations and provide a more objective analysis of the data, the authors may consider the following:

In the datasets you are examining, what are the relative percentages in each of the four groups relating compartmentalization change to expression change (A to B, expression up; A-B, down; B-A, up; B-A, down)?

This phrase in the abstract is imprecise: "whereas premature CTCF depletion accelerates yet confounds cardiomyocyte maturation."

Regarding this statement: "Disruption of [3D chromatin architecture] has been linked to genetic dilated cardiomyopathy (DCM) caused by lamin A/C mutations8,9, and mutations in chromatin regulators are strongly enriched in de novo congenital heart defects (CHD)10, underscoring their pathogenic relevance11." The first studies to implicate chromatin structural changes in heart disease, including the role of CTCF in that process, were PMID: 28802249, a model of acquired, rather than genetic, disease.

Can you quantify this statement: "the compartment switch coincided with progressive reduction of promoter-gene body interactions"?

Regarding this statement: "six regions became less accessible in CMs, correlating with ChIP-seq signal for the ubiquitous architectural protein CTCF." I don't see 6 ATAC peaks in either TTN trace in Figure 1A.

Western blots need molecular weight markers.

Regarding this statement: "The decrease in CTCF protein levels may explain its selective detachment from TTN during cardiomyogenesis." At face value, these findings suggest the opposite: i.e. that a massive downregulation of CTCF at protein level should affect its binding across the genome, which is not tested and is hard to evaluate between ChIP-seq studies from different groups and from different developmental timeframes.

A couple thoughts on the FISH experiments in Figure 2. A claim of 'impaired B-A transition' would be more convincing if you show, by FISH, that the relative distance of TTN from lamin B increases with differentiation. In the images: are you showing a total projection of all z planes? One assumes the quantitation is relative to a 3D reconstruction in which the lamin B signal is restricted to the periphery. Have you shown this? Lastly, these data are very interesting and important, provoking reexamination of your interpretation of the results in Figure 1. Figure 1 was interpreted to show that less CTCF binding led to decreased lamina (and thus B compartment) association during development. Figure 2 shows that depleting CTCF does not change association of TTN with lamina.

A thought about this statement: "Altogether, these results suggest that GATA4 and CTCF function as positive and negative regulators of B-to-A compartment switching, likely acting through global and local chromatin remodeling, respectively." GATA4 induces TTN expression and its knockdown prevents TTN expression-the evidence that GATA4 affects compartmentalization is unclear. By activating the gene, GATA4 may shift TTN to B classification.

I'm not sure what I am looking at in Figure 3C. Are those traces integration of interactions over a defined window? "Each [mutant is] clearly different from WT" is not obvious from the presentation. The histograms are plotting AUC of what? Interactions of those peaks with the mutated region? I genuinely appreciate how laborious this experiment must have been and encourage you to explain better what you are showing.

Again acknowledging how challenging these experiments are: when you mutant a locus, you change CTCF binding but you also change the DNA. Thus, attributing the changes in interactions to presence/absence of CTCF binding is difficult, because the DNA substrate itself has changed. Perhaps you are presenting all of this as a negative result, given the modest effect on transcription, which is as important as a positive result, given the assumptions usually made about such things. But the results are not clearly described and your interpretation seems to go between implying the structural change causative and being agnostic.

Figure 4C: since you have RNA-seq data, a much more objective way to present these data would be to show all data (again, A-B, up; A-B, down; B-A, up; B-A, down) and the effects of CTCF or GATA4. Regardless, you can still focus on the cardiac specific genes. But my guess is if you examine all genes, the pattern you show in panel C will not be present in the majority of cases. Furthermore, if this hypothesis is wrong, such an analysis will allow you to identify other genes affected by the mechanisms you describe and your analysis will test whether these mechanisms are in fact conserved at different loci.

Significance

This manuscript by Becca and others examines the relationship between GATA4 and CTCF in chromatin organization and cardiac maturation. There are several very interesting observations that lead to potentially new insights into the relationship between genome folding, gene expression and the relationship between transcription factors and chromatin structural proteins.

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Reply to the reviewers

Reviewer #1

1. First, the authors have not convincingly shown that skin cells, or more specifically skin ECs, are a major source of circulating G-CSF in the psoriasis model as stated in the title and abstract. The data in Figure 4 show selective upregulation of Csf3 gene in skin ECs and their ability to secrete G-CSF upon IMQ treatment in vitro. However, the provided data do not address to what degree the skin EC-derived G-CSF contributes to the elevated level of circulating G-CSF. Additional experiments to selectively deplete G-CSF in skin ECs, or at least in skin cells of the affected site, are warranted to support the authors' claim. Does intradermal injection of G-CSF neutralizing antibody into the psoriatic skin reduce circulating levels of G-CSF?

Author's response:

Thank you for reviewer's comment. We agree with the Reviewer#1 that it is important to directly block G-CSF to the skin via intradermal injection and measure the G-CSF level in the serum afterwards. Therefore, we will perform intradermal injection of IgG-isotype or anti-G-CSF antibody into the IMQ-induced psoriatic mice.

Another concern is insufficient demonstration of G-CSF-mediated emergency granulopoiesis in the psoriasis model. All data in Figure 5 were obtained from experiments with only n=3, and adding more replicates, in particular to those in Figure 5B, which show quite some variation in MPP numbers, is recommended. The relatively small reduction of BM granulocyte numbers (Figure 5C) compared to greater depletion of circulating granulocytes (Figure S5A) raises the possibility that it is the mobilization effect rather than granulopoiesis-stimulating effect that skin-derived G-CSF exerts to promote supply of circulating neutrophils that eventually infiltrate into the affected skin. This could also explain the negligible effect of IL-1blockade (Figure S4), which selectively shut off myelopoiesis-stimulating effect of IL-1 (Pietras et al. Nat Cell Biol 2016, PMID: 27111842). Are the HSPCs in the psoriasis model more cycling? Do they show myeloid-skewed differentiation when cultured ex vivo or upon transplantation?

Author's response: Thank you for these critical comments. We agree to do the following experiments to address them:

1) HSPCs quantification in Figure 5 especially the MPPs will be added with more replicates.

2) We will assess cycling status of HSPCs by flow cytometric analysis of Ki67and Propidium Iodide to characterize G0, G1 and G2/M cell cycle phase.

3) To test myeloid-skewed differentiation, Lin- c-Kit+ Sca-1+ cells containing HSPCs will be isolated from bone marrow of Vas/IMQ-treated mice and transplanted into lethally irradiated syngeneic mice.

The authors' claim that skin-derived G-CSF "induces" neutrophil infiltration warrants further clarification. Alternative explanation is that the upregulated neutrophil-attracting chemokines (Figure S1D) could induce infiltration, whereas G-CSF increase the number of neutrophils to circulate in the vessels near the psoriatic skin. This notion seems supported elsewhere (Moos et al. J Invest Dermatol. 2019, PMID: 30684554). Can the infiltration be inhibited by systemically injecting neutralizing antibody of their receptor, CXCR2?

Author's response: The manuscript focuses on the skin-derived G-CSF function as a long-distance signal for emergency granulopoiesis in the bone marrow upon psoriasis, not the chemoattractant property of it. The sentence of interest is "We found that upon psoriasis induction, skin-resident endothelial cells are activated to produce G-CSF which activates emergency granulopoiesis in bone marrow and induces cutaneous infiltration and accumulation of neutrophil that are functionally inflammatory." in line 28-30. In agreement with point #2 from Reviewer#2, the fact that neutrophil recruitment factors (CXCL1, CXCL2, and CXCL5) were upregulated in psoriatic skin (Figure S1D), suggesting a CXCL-mediated neutrophil recruitment. The sentence of concern need to be changed to "We found that upon psoriasis induction, skin-resident endothelial cells are activated to produce G-CSF which activates emergency granulopoiesis in bone marrow, leading to cutaneous accumulation of neutrophil that are functionally inflammatory.". This revised sentence has omitted the proposal that G-CSF directly dictates neutrophils mobilization to the skin, which is not the key message of the study. Therefore, we found that the CXCR2 (CXCLs receptor) blockade experiment may be of the benefit of future studies.

It remains unclear how skin-derived G-CSF accumulates pathogenic neutrophils. The authors state "pathogenic granulopoiesis," but are the circulating neutrophils in the psoriatic mice already "pathogenic" or do they acquire pathogenic phenotype after cutaneous infiltration? Additional RNA-seq to compare circulating and infiltrated neutrophils would answer this question.

Author's response: We appreciate this valuable comment. We will perform RNA-seq with the peripheral blood-circulating neutrophils (CD45+ CD11b+ Ly6G+ Ly6Cmid) versus skin-infiltrating neutrophils from both Vas/IMQ mice.

In addition, how the accumulated pathogenic neutrophils exacerbate the psoriatic changes remains obscure. Although the authors have attempted to correlate Il17a gene expression in infiltrated neutrophils with psoriatic skin changes, the data do not address to what degree it contributes to cutaneous IL-17A protein levels. The data that cutaneous neutrophil depletion leads to subtle decrease in skin IL-17A expression (Figure 2H) rather supports alternative possibilities. For instance, as indicated elsewhere, IL-17A cutaneous tone could be enhanced by neutrophil-mediated augmentation of Th17 or gamma/delta T cell function (Lambert et al. J Invest Dermatol. 2019, PMID: 30528823). Does neutrophil depletion or G-CSF neutralization alter cell numbers or function of cutaneous Th17 and gamma/delta T cells?

Author's response: Thank you for this insightful comment. To better understand the relative contribution of neutrophils to the cutaneous IL-17A tone in the psoriatic skin, we will perform flowcytometric analysis of Th17 and gamma/delta T cells which are widely known as the major source of IL-17 in psoriatic skin of IMQ-induced mice following injection of isotype-matched or anti-Ly6G antibody.

Finally, as the above conclusions rely solely on the IMQ-induced acute psoriasis model, it would be informative if they could be derived from another psoriasis model. IMQ is known to induce unintended systemic inflammation due to grooming-associated ingestion (Gangwar et al. J Invest Dermatol. 2022, PMID: 34953514), and "pathological crosstalk between skin and BM in psoriatic inflammation" could be strengthened by an intradermal injection model.

Author's response: We appreciate the reviewer for bringing this important point. Regarding the systemic inflammation upon psoriasis, the above-cited study reported increased IFN-B expression in the intestines of IMQ-ingested animal (Grine L et al. Sci Rep. 2016, PMID: 26818707 in Gangwar et al. J Invest Dermatol. 2022, PMID: 34953514). We examined several pro-inflammatory cytokines including IFN-b, IFN-g, and IL-6 and in contrast, found no systemic increase in all these cytokines, except for IFN-g downregulation (Explanation Figure 1), which suggests no evidence of grooming-associated ingestion.

We also examined the Csf3 expression across several distinctively located tissues which showed a selective upregulation in the skin (Figure 4C), suggesting a skin-restricted perturbation. In addition, one study showed that IMQ-ingestion didn't alter number of gut injury-associated CXCR3+ macrophages nor did it aggravate skin inflammation (Pinget et al. Cell Reports. 2022, PMID: 35977500). Together, these findings support that IMQ-induced psoriasis by topical cutaneous application used in our study elicit a local inflammation but not systemic inflammation.

The authors, however, realize that testing alternative psoriasis model such as intradermal injection of IL-23 (Chan et al. J Exp Med. 2006, PMID: 17074928) will strengthen the skin-local insults within the psoriasis model employed, and should be tested in the future.

Minor comments

Figure 1E shows multiple elongated Ly6G+ structures in d0-2 control and d0 IMQ skins that do not appear to be neutrophils.

Author's response: We appreciate the Reviewer#1 pointing this issue. As mentioned by the Reviewer#1, the elongated structures detected in the intravital microscopy are not neutrophils, but autofluorescence from the skin bulge regions (Wun et al. J Invest Dermatol. 2005, PMID: 15816847). We have eliminated these unspecific signals from the transformation and quantification (Figure 1F, S1G, and S1H). We will also add an explanatory sentence in Materials and Methods section "Of note, the fluorescent signal with elongated structures resembling hair bulge were autofluorescence and thus removed from further analysis." to be more precise about our methods.

In Figure 2C, the bottom GSEA seems to be showing type II IFN response, not type I IFN, according to the text.

Author's response: Thank you for the comment, we will correct this misspelling.

Author's response: We appreciate that Reviewer#1 bring up this point. We examined the kinetics of the bone marrow cellularity and GMPs across 4 days of psoriasis induction in mice. The bone marrow cell number was lowered along that span with lowermost count at 2 days. Consistent to the BM-cellularity, the GMP number was also lowered about one-third in the first 2 days of psoriasis. This kinetic is consistent with the previous report showing a rapid reduction of GMPs in the bone marrow within 2 days following systemic G-CSF administration driven emergency granulopoiesis (Hirai et al. Nat. Immunol. 2006, PMID: 16751774). From 2 days to 4 days, the GMP number rapidly increased to slightly above basal number (Explanation Figure 2). This timely coordinated expansion suggests a significant supply of GMPs from the differentiating upstream myeloid progenitors (Figure 3B).

When the psoriatic mice with elevated G-CSF is injected with anti-G-CSF or IgG-isotype antibody, the bone marrow cellularity and GMP numbers at 4 days were (Explanation Figure 3). Firstly, as psoriasis reduced bone marrow cellularity (Explanation Figure 2), the unchanged number after anti-G-CSF injection indicates that administration of 10µg/day for 4 days does not significantly affect mobilization of psoriatic bone marrow cells. Secondly, the similar GMP numbers at 4 days psoriasis is plausibly due to snapshot analysis when it has already in the numerical recovery period (Explanation Figure 2). Importantly, the notion that anti-G-CSF injection to psoriatic mice reduced granulocytes in the bone marrow, peripheral blood, and skin suggesting G-CSF as a key mediator in psoriatic driven emergency granulopoiesis on top of unlikely case of ineffective anti-G-CSF treatment.

Taken together, these data suggest a G-CSF mediated emergency granulopoiesis occurrence in the IMQ-induced psoriasis. We will put these data into a revised Figure.

In Figures 6B, in which cluster of human skin cells IL-17A expression would be enriched?

Author's response: Thank you for this important point. The IL-17A expression is found in the T-cell cluster (Explanation Figure 4). We also expected to see IL-17A contribution from other cell subset(s), in particular neutrophil. However, due to the fragile nature of neutrophils and thereby, technical difficulty to get their sequencing reads, this dataset (GSE173706) doesn't contain neutrophils, but rather monocytes, macrophages, and dendritic cells among the myeloid subset (Explanation Figure 5). With this, it leaves open the question on what potential contribution of IL-17A produced by neutrophils is in human psoriasis (Reich et al. Exp. Dermatol. 2015, PMID: 25828362).

Figure 1E shows multiple elongated Ly6G+ structures in d0-2 control and d0 IMQ skins that do not appear to be neutrophils.

Author's response: We appreciate the Reviewer#1 pointing this issue. As mentioned by the Reviewer#1, the elongated structures detected in the intravital microscopy are not neutrophils, but autofluorescence from the skin bulge regions (Wun et al. J Invest Dermatol. 2005, PMID: 15816847). We have eliminated these unspecific signals from the transformation and quantification (Figure 1F, S1G, and S1H). We will also add an explanatory sentence in Materials and Methods section "Of note, the fluorescent signal with elongated structures resembling hair bulge were autofluorescence and thus removed from further analysis." to be more precise about our methods.

In Figure 2C, the bottom GSEA seems to be showing type II IFN response, not type I IFN, according to the text.

Author's response: Thank you for the comment, we will correct this misspelling.

Reviewer#2

1. Interpretation of neutrophil transcriptomic changes (Figure 2)

The RNA-seq analysis reveals substantial downregulation of several canonical pro inflammatory pathways in neutrophils from psoriatic skin, including IL-6, IL-1, and type II interferon signaling. The authors should discuss the functional relevance of this unexpected transcriptional repression. For example, does this indicate a shift toward specialized effector functions rather than classical cytokine responsiveness? More importantly, the most striking transcriptional change is the upregulation of NADPH oxidase-related genes (e.g., Nox1, Nox3, Nox4, Enox2). This suggests an oxidative stress-driven pathogenic mechanism, potentially more relevant than IL-17A production. Yet this aspect is not explored in the manuscript. Assessing ROS levels or oxidative neutrophil effector functions in this model would considerably strengthen the mechanistic link. Conversely, although IL-17A is upregulated in neutrophils, neutrophil depletion reduces total Il17a expression in skin only partially. This indicates that neutrophils are unlikely to be the dominant IL-17A source in the lesion. The authors' focus on neutrophil-derived IL 17A therefore seems overstated. A more rigorous assessment-e.g., conditional deletion of Il17a specifically in neutrophils-would be required to establish its true contribution. Taken together, the data suggest that oxidative programs, rather than IL-17A production, may represent the principal pathogenic axis downstream of neutrophils, and this deserves deeper discussion.

Author's response: Thank you for raising this valuable views. We have agreed to address these critical points by the following approaches:

1) To address the changes in NADPH oxidase-related gene signature, we will measure ROS production in the neutrophils from skin and peripheral blood with DHR123.

2) Responding to the IL17A contribution by neutrophils, we will flow cytometrically assess the Th17 and gamma/delta T cell population in the skin of psoriatic mice treated with anti-Ly6G or isotype-matched antibody as was suggested by Reviewer#1.

3) We will discuss downregulation of the canonical pro inflammatory and IL-17 pathways in the psoriatic neutrophils in the discussion.

Human data reanalysis (Figure 6):

The re-analysis of bulk and single-cell RNA-seq datasets is valuable but incomplete. Several mechanistically relevant questions could be addressed with the available data:

2.1. GM-CSF (CSF2) is also strongly upregulated in psoriatic lesions (bulk RNA-seq). It would be informative to determine whether endothelial cells also express CSF2 in the scRNA-seq dataset, as this would suggest coordinated regulation of myeloid-supporting cytokines.

2.2. Myeloid cell subsets should be examined more closely. A comparison of human myeloid transcriptomes with the mouse neutrophil RNA-seq would clarify whether similar IL-17A-related or NADPH oxidase-related signatures occur in human disease. In particular, which cell types express IL17A in human lesions?

2.3. Chemokine production should be attributed to specific cell types. Bulk RNA-seq confirms strong induction of CXCL1, CXCL2, CXCL5, but the scRNA-seq dataset allows determining whether these chemokines originate from endothelial cells or other stromal/immune populations. This information is important for defining whether endothelial cells coordinate both neutrophil recruitment and granulopoiesis.

Addressing these points would make the human-mouse comparison substantially stronger.

Author's response: Thank you for pointing these important issues. By reanalyzing the dataset, we found several points regarding the comments, as follows:

2.1) CSF2 is expressed by T-cell cluster in the human skin dataset (Explanation Figure 4), in agreement with previous murine study (Hartwig et al. Cell Reports. 2018, PMID: 30590032). We will add this data in the revised manuscript.

2.2) In line with point#10 from Reviewer#1, the dataset clearly shows T-cell cluster as the main IL17A source (Explanation Figure 4 above). The dataset, however, doesn't contain phenotypic neutrophils (CEACAM (CD66b) and PGLYRP1) but monocytes, macrophages, and dendritic cells (Explanation Figure 5 above). This loss was probably due to a technical limitation given the difficulty in capturing sequencing reads from fragile neutrophils. Therefore, it is no longer possible to reanalyze IL-17 expression in the absence of neutrophils in the datapool.

2.3) Reanalysis of CXCLs in the human scRNAseq dataset (GSE173706) clarified their secretion dynamics and cellular sources under normal and psoriatic condition. In normal skin, all examined cell subsets show only low CXCLs expression. In contrast, psoriatic skin exhibits significant CXCLs upregulation with distinct cell subsets clearly showing dramatic upregulation, potentially being the major CXCLs source. CXCL1 is markedly upregulated in fibroblasts, myeloid cells, and melanocyte and nerve cells. CXCL2 is strikingly upregulated to myeloid cells, while CXCL5 is hugely increased in fibroblasts, myeloid cells, and mast cells (Explanation Figure 7). Taken together, these results suggest that CXCLs upregulation in the psoriatic skin is coordinatively executed by both stromal and immune compartments. Of note, the endothelial cells show minimal changes in CXCLs expression, even downregulate CXCL2 in psoriasis, indicating that they are unlikely to be the major contributor to CXCL-mediated neutrophil recruitment.

**Referees cross-commenting**

I agree with Reviewer 1 that the contribution of EC-derived G-CSF to circulating G-CSF levels and to emergency myelopoiesis requires additional genetic or neutralization experiments to be fully established.

Author's response: We appreciate that Reviewer#2 raised this key point. In addition to examining the serum G-CSF upon intradermal anti-G-CSF administration in point#1 from Reviewer#1 above, we will also examine the emergency myelopoiesis signs in vivo.

Minor points

1. Line 319: the text likely refers to Figure S4, not S3.

Author's response: Thank you, we will correct the nomenclature.

Line 338: "psoriatic" is misspelled.

Author's response: Thank you, we will change this to "psoriatic".

Reviewer #3

• Place the work in the context of the existing literature (provide references, where appropriate).

Psoriasis is extensively studied, a good recent reference- https://doi.org/10.1016/j.mam.2024.101306

Author's response: Thank you for Reviewer#3's suggestion. The referenced study highlights the current paradigm that largely focus on skin-restricted mechanism and overlook potential cross-organ interaction in the psoriasis inflammation. Our findings provide a new insight into the skin-bone marrow crosstalk in the disease context. In addition, the suggested reference underscores the key roles of diverse innate immune cells including neutrophils, eosinophils, dendritic cells, etc. which is fundamental for our study and might also guide future exploration of additional innate cell subsets beyond neutrophils. We will therefore include the mentioned reference to our revised manuscript.

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

It is all good. May add graphical-abstract.

Author's response: Thank you for the reviewer's input, we agree that a graphical-abstract will help the readers more clearly grasp the key messages of our manuscript. We will include it in the revised manuscript.

Major comments:

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

No. It is very solid.

Author's response: We appreciate the reviewer's view that the claims in our paper are solid.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Such a discovery clearly opens many options, and it is fascinating to suggest additional experiments for future studies. It is a complete study, best to publish as-is and let many to read and proceed with this new concept.

Author's response: We thank the reviewer for noting that the current experimental evidence is complete that no additional experiments are necessary at this stage. We agree that the discovery opens prospective directions for future studies.

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

N/A - I suggest no additional experiments at this point. Get it published and see how many will follow this new direction!

Author's response: We thank the reviewer for recognizing that the experimental data has been sufficient to be a foundation for the future research.

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

Yes.

Author's response: We thank the reviewer for recognizing that our methods are reproducible.

• Are the experiments adequately replicated, and is the statistical analysis adequate?

Yes. The data are of very high quality.

Author's response: We are grateful that the reviewer view our replication strategy and statistical analysis are of a high quality.

Minor comments:

• Specific experimental issues that are easily addressable.

None. It is good as-is. One may always suggest minor things- but this one is better published so many laboratories may rush for this new direction. I think it will be interesting studying some long-term impacts, and changes not only of neutrophils but also of other innate cells, such as DCs, Macrophages, and Eosinophils - so it is best to let laboratories that focus on these cells know of the discovery and pursue independent studies.

Author's response: We appreciate the reviewer's assessment that our paper is already well set for the community to explore the newly proposed direction.

• Are the text and figures clear and accurate?

Yes.

Author's response: We thank the reviewer's evaluation. We have ensured that the text and figures in our manuscript are clear and accurate. Once again, we thank the reviewer for the encouraging and constructive appraisal. We are pleased that the reviewer find the manuscript has already been strong and suitable for publication.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

Study titled: "Skin-derived G-CSF activates pathological granulopoiesis upon psoriasis" by Kosasih and Takizawa. Paper show establishment of psoriasis model in C57BL/6 mice. They focus on neutrophils infiltration following the Imiquimod cream induction. Importantly, authors show that the induction of psoriasis in the skin cause a robust enhancement of granulopoiesis in the bone marrow. Mechanistically, G-CSF is produced in the skin, especially by endothelial cells. Blocking of G-CSF gained clear inhibition of psoriatic pathology. They further add human data showing that patient with psoriasis have more neutrophils and more G-CSF in their skin endothelial cells.

Parts of the study are simply in line with previous knowledge (e.g.- neutrophils infiltration into psoriatic skin, IL17a). authors show some data that largely confirm the model used. Major discovery: skin endothelial cells are secreting G-CSF that induce granulopoiesis in the bone-marrow. This is a conceptual advancement of this study: psoriatic skin not only recruit neutrophils from the blood, but also enhance the generation of new neutrophils in the bone-marrow. That a major- psoriasis at the level of the model used must not be considered as a confined-pathology. It affect systematically, and might also benefit new systemic treatments. There are plenty of follow-up experiments to pursue now, so it is critical to publish this finding and let many laboratories to know of this new direction. I expect this study to attract high interest and many citations.

Major comments:

• Are the key conclusions convincing?

Yes. The study has excellent data, with good quantification, and very solid support for the discovery and interpretations. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

No. It is very solid. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Such a discovery clearly opens many options, and it is fascinating to suggest additional experiments for future studies. It is a complete study, best to publish as-is and let many to read and proceed with this new concept. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

N/A - I suggest no additional experiments at this point. Get it published and see how many will follow this new direction! - Are the data and the methods presented in such a way that they can be reproduced?

Yes. - Are the experiments adequately replicated, and is the statistical analysis adequate?

Yes. The data are of very high quality.

Minor comments:

• Specific experimental issues that are easily addressable.

None. It is good as-is. One may always suggest minor things- but this one is better published so many laboratories may rush for this new direction. I think it will be interesting studying some long-term impacts, and changes not only of neutrophils but also of other innate cells, such as DCs, Macrophages, and Eosinophils - so it is best to let laboratories that focus on these cells know of the discovery and pursue independent studies. - Are prior studies referenced appropriately?

Yes. I may suggest adding a recent review by Park and Jung, 2024, https://doi.org/10.1016/j.mam.2024.101306 to cover current concepts of innate immunity in psoriasis. - Are the text and figures clear and accurate?

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

It is all good. May add graphical-abstract.

Significance

• Describe the nature and significance of the advance (e.g., conceptual, technical, clinical) for the field.

Conceptual advancement - discovery of a major impact of psoriasis on bone-marrow granulopoiesis. Explicit finding of endothelial-cells G-CSF as a major communication moiety.

• Place the work in the context of the existing literature (provide references, where appropriate). Psoriasis is extensively studied, a good recent reference- https://doi.org/10.1016/j.mam.2024.101306

Neutrophil recruitment and IL17A are well established. G-CSF of endothelial cells brings the conceptual advancement- psoriasis at the level induced by IMQ develops local pathology, but is tightly linked to systemic changes. The impact on bone-marrow granulopoiesis may have many implications. So far, it was largely considered that chronic inflammation may affect hematopoiesis, but this study reveals an acute and specific communication between skin and bone marrow. The neutrophils are not only recruited from blood- they are made anew, so the disease is enhanced significantly! This discovery led to a novel basic understanding and suggests novel therapeutic options. - State what audience might be interested in and influenced by the reported findings.

Dermatologist, immunologist, haematologist - this one goes for a broad audience. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Immunology and hematology. I am not an expert of dermatology.

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Referee #2

Evidence, reproducibility and clarity

General assessment

This is a well-written and carefully executed study that identifies skin-derived G-CSF as a key driver of pathological emergency granulopoiesis in an imiquimod-induced mouse model of psoriasis. The authors convincingly show that endothelial cells are the dominant source of G-CSF in inflamed skin, and that this cytokine mediates systemic hematopoietic skewing and neutrophil accumulation, ultimately aggravating psoriatic pathology. The eanalysis of human transcriptomic datasets strengthens the translational relevance of the findings. Overall, the conclusions are well supported by the data. However, several mechanistically relevant aspects remain underexplored, particularly regarding the functional state of psoriatic neutrophils and the human data integration. Addressing these points would substantially enhance the impact of the study.

Major points

1. Interpretation of neutrophil transcriptomic changes (Figure 2)

The RNA-seq analysis reveals substantial downregulation of several canonical proinflammatory pathways in neutrophils from psoriatic skin, including IL-6, IL-1, and type II interferon signaling. The authors should discuss the functional relevance of this unexpected transcriptional repression. For example, does this indicate a shift toward specialized effector functions rather than classical cytokine responsiveness? More importantly, the most striking transcriptional change is the upregulation of NADPH oxidase-related genes (e.g., Nox1, Nox3, Nox4, Enox2). This suggests an oxidativestress-driven pathogenic mechanism, potentially more relevant than IL-17A production. Yet this aspect is not explored in the manuscript. Assessing ROS levels or oxidative neutrophil effector functions in this model would considerably strengthen the mechanistic link.

Conversely, although IL-17A is upregulated in neutrophils, neutrophil depletion reduces total Il17a expression in skin only partially. This indicates that neutrophils are unlikely to be the dominant IL-17A source in the lesion. The authors' focus on neutrophil-derived IL17A therefore seems overstated. A more rigorous assessment-e.g., conditional deletion of Il17a specifically in neutrophils-would be required to establish its true contribution. Taken together, the data suggest that oxidative programs, rather than IL-17A production, may represent the principal pathogenic axis downstream of neutrophils, and this deserves deeper discussion. 2. Human data reanalysis (Figure 6):

The re-analysis of bulk and single-cell RNA-seq datasets is valuable but incomplete.

Several mechanistically relevant questions could be addressed with the available data:

2.1. GM-CSF (CSF2) is also strongly upregulated in psoriatic lesions (bulk RNA-seq). It would be informative to determine whether endothelial cells also express CSF2 in the scRNA-seq dataset, as this would suggest coordinated regulation of myeloid-supporting cytokines.

2.2. Myeloid cell subsets should be examined more closely. A comparison of human myeloid transcriptomes with the mouse neutrophil RNA-seq would clarify whether similar IL-17A-related or NADPH oxidase-related signatures occur in human disease. In particular, which cell types express IL17A in human lesions?

2.3. Chemokine production should be attributed to specific cell types. Bulk RNA-seq confirms strong induction of CXCL1, CXCL2, CXCL5, but the scRNA-seq dataset allows determining whether these chemokines originate from endothelial cells or other stromal/immune populations. This information is important for defining whether endothelial cells coordinate both neutrophil recruitment and granulopoiesis. Addressing these points would make the human-mouse comparison substantially stronger.

Minor points

1. Line 319: the text likely refers to Figure S4, not S3.
2. Line 338: "psoriatic" is misspelled.

Referees cross-commenting

I agree with Reviewer 1 that the contribution of EC-derived G-CSF to circulating G-CSF levels and to emergency myelopoiesis requires additional genetic or neutralization experiments to be fully established.

Significance

The study is solid and potentially impactful, particularly for audiences working in inflammation and hematopoiesis, as it uncovers a cross-organ mechanism linking skinderived G-CSF to emergency granulopoiesis in psoriasis. My expertise lies in inflammation and hematopoiesis, and from this perspective several essential mechanistic issues remain insufficiently addressed. In particular, the neutrophil transcriptomic data highlight strong induction of NADPH oxidase-related pathways, which appears more biologically meaningful than the modest Il17a upregulation emphasized by the authors. Likewise, the human RNA-seq reanalyses leave open key questions regarding CSF2 expression, myeloid heterogeneity, and chemokine cellular sources. These issues affect the strength and interpretation of the central claims. For these reasons, I recommend major revision before the manuscript can be considered further.

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Referee #1

Evidence, reproducibility and clarity

Summary:

A role of neutrophils in psoriasis pathogenesis has been highlighted by several past studies; however, how the neutrophils are recruited to the affected skin has not been fully understood. The work by Kosasih et al. tackles a relevant question and has investigated the effect of psoriatic skin inflammation on BM myelopoiesis. Using an IMQ-induced acute psoriasis mouse model, the authors derive 3 major conclusions: (1) skin ECs secrete G-CSF into circulation in response to psoriatic stress, (2) skin EC-derived G-CSF stimulates emergency granulopoiesis, and (3) skin EC-derived G-CSF induces infiltration and accumulation of pathogenic neutrophils in the affected skin. The authors provide many pieces of interesting data, but most of them remain correlative and insufficient to support the conclusions. Many of the experiments were performed in a small number of samples or mice (mostly with n=3), leaving the story still preliminary.

Major comments:

1. First, the authors have not convincingly shown that skin cells, or more specifically skin ECs, are a major source of circulating G-CSF in the psoriasis model as stated in the title and abstract. The data in Figure 4 show selective upregulation of Csf3 gene in skin ECs and their ability to secrete G-CSF upon IMQ treatment in vitro. However, the provided data do not address to what degree the skin EC-derived G-CSF contributes to the elevated level of circulating G-CSF. Additional experiments to selectively deplete G-CSF in skin ECs, or at least in skin cells of the affected site, are warranted to support the authors' claim. Does intradermal injection of G-CSF neutralizing antibody into the psoriatic skin reduce circulating levels of G-CSF?
2. Another concern is insufficient demonstration of G-CSF-mediated emergency granulopoiesis in the psoriasis model. All data in Figure 5 were obtained from experiments with only n=3, and adding more replicates, in particular to those in Figure 5B, which show quite some variation in MPP numbers, is recommended. The relatively small reduction of BM granulocyte numbers (Figure 5C) compared to greater depletion of circulating granulocytes (Figure S5A) raises the possibility that it is the mobilization effect rather than granulopoiesis-stimulating effect that skin-derived G-CSF exerts to promote supply of circulating neutrophils that eventually infiltrate into the affected skin. This could also explain the negligible effect of IL-1blockade (Figure S4), which selectively shut off myelopoiesis-stimulating effect of IL-1 (Pietras et al. Nat Cell Biol 2016, PMID: 27111842). Are the HSPCs in the psoriasis model more cycling? Do they show myeloid-skewed differentiation when cultured ex vivo or upon transplantation?
3. The authors' claim that skin-derived G-CSF "induces" neutrophil infiltration warrants further clarification. Alternative explanation is that the upregulated neutrophil-attracting chemokines (Figure S1D) could induce infiltration, whereas G-CSF increase the number of neutrophils to circulate in the vessels near the psoriatic skin. This notion seems supported elsewhere (Moos et al. J Invest Dermatol. 2019, PMID: 30684554). Can the infiltration be inhibited by systemically injecting neutralizing antibody of their receptor, CXCR2?
4. It remains unclear how skin-derived G-CSF accumulates pathogenic neutrophils. The authors state "pathogenic granulopoiesis," but are the circulating neutrophils in the psoriatic mice already "pathogenic" or do they acquire pathogenic phenotype after cutaneous infiltration? Additional RNA-seq to compare circulating and infiltrated neutrophils would answer this question.
5. In addition, how the accumulated pathogenic neutrophils exacerbate the psoriatic changes remains obscure. Although the authors have attempted to correlate Il17a gene expression in infiltrated neutrophils with psoriatic skin changes, the data do not address to what degree it contributes to cutaneous IL-17A protein levels. The data that cutaneous neutrophil depletion leads to subtle decrease in skin IL-17A expression (Figure 2H) rather supports alternative possibilities. For instance, as indicated elsewhere, IL-17A cutaneous tone could be enhanced by neutrophil-mediated augmentation of Th17 or gamma/delta T cell function (Lambert et al. J Invest Dermatol. 2019, PMID: 30528823). Does neutrophil depletion or G-CSF neutralization alter cell numbers or function of cutaneous Th17 and gamma/delta T cells?
6. Finally, as the above conclusions rely solely on the IMQ-induced acute psoriasis model, it would be informative if they could be derived from another psoriasis model. IMQ is known to induce unintended systemic inflammation due to grooming-associated ingestion (Gangwar et al. J Invest Dermatol. 2022, PMID: 34953514), and "pathological crosstalk between skin and BM in psoriatic inflammation" could be strengthened by an intradermal injection model.

Minor comments:

1. Figure 1E shows multiple elongated Ly6G+ structures in d0-2 control and d0 IMQ skins that do not appear to be neutrophils.
2. In Figure 2C, the bottom GSEA seems to be showing type II IFN response, not type I IFN, according to the text.
3. For the BM analysis in Figures 3, 5, S3, and S5, it would be informative if BM cellularity and numbers of committed myeloid progenitors (e.g., GMPs) are shown.
4. In Figures 6B, in which cluster of human skin cells IL-17A expression would be enriched?

Significance

Although quite a few studies have reported various examples of emergency myelopoiesis (Swann et al. Nat Rev Immunol. 2024, PMID: 38467802), there is limited evidence on its occurrence and involvement in locally restricted disease, such as periodontitis (Li et al. Cell 2022, PMID: 35483374; 35483374). As an HSC biologist, I see this study is conceptually interesting as it could extend the above concept to psoriasis, a non-infectious, local inflammatory disease in the skin, and describes a potential causal link between skin-derived G-CSF and emergency myelopoiesis. That said, as detailed in the first section, the conclusions, especially that related to emergency myelopoiesis driven by skin-derived G-CSF, need to be more convincingly supported before taking its value. The findings offer additional understanding of how psoriasis is developed in concert with aberrant hematopoiesis and will be relevant to those working in the field of dermatology, immunology, and hematology.

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Reply to the reviewers

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

Summary The manuscript by Aarts et al. explores the role of GRHL2 as a regulator of the progesterone receptor (PR) in breast cancer cells. The authors show that GRHL2 and PR interact in a hormone-independent manner and based on genomic analyses, propose that they co-regulate target genes via chromatin looping. To support this model, the study integrates both newly generated and previously published datasets, including ChIP-seq, CUT&RUN, RNA-seq, and chromatin interaction assays, in breast cancer cell models (T47DS and T47D).

Major comments: R1.1 Novelty of GRHL2 in steroid receptor biology The role of GRHL2 as a co-regulator of steroid hormone receptors has previously been described for ER (J Endocr Soc. 2021;5(Suppl 1):A819) and AR (Cancer Res. 2017;77:3417-3430). In the ER study, the authors also employed a GRHL2 ΔTAD T47D cell model. Therefore, while this manuscript extends GRHL2 involvement to PR, the contribution appears incremental rather than conceptual.

We are fully aware of the previously described role of GRHL2 as a co-regulator of steroid hormone receptors, particularly ER and AR. As acknowledged in our introduction (lines 104-108), we explicitly state: "Grainyhead-like 2 (GRHL2) has recently emerged as a potential pioneer factor in hormone receptor-positive cancers, including breast cancer21. However, nearly all studies to date have focused on GRHL2 in the context of ER and estrogen signaling, leaving its role in PR- and progesterone-mediated regulation unexplored22-26".

As for the specific publications that the reviewer refers to: The first refers to an abstract from an annual meeting of the Endocrine Society. As we have been unable to assess the original data underpinning the abstract - including the mentioned GRHL2 DTAD model - we prefer not to cite this particular reference. We do cite other work by the same authors (Reese et al. 2022, our ref. 25). We also cite the AR study mentioned by the reviewer (our ref. 55) in our discussion. As such, we think we do give credit to prior work done in this area.

By characterizing GRHL2 as a co-regulator of the progesterone receptor (PR), we expand on the current understanding of GRHL2 as a common transcriptional regulator within the broader context of steroid hormone receptor biology. Given that ER and PR are frequently co-expressed and active within the same breast cancer cells, our findings raise the important possibility that GRHL2 may actively coordinate or modulate the balance between ER- and PR-driven transcriptional programs, as postulated in the discussion paragraph.

Importantly, we also functionally link PR/GRHL2-bound enhancers to their target genes (Fig5), providing novel insights into the downstream regulatory networks influenced by this interaction. These results not only offer a deeper mechanistic understanding of PR signaling in breast cancer but also lay the groundwork for future comparative analyses between GRHL2's role in ER-, AR-, and PR-mediated gene regulation.

As such, we respectfully suggest that our work offers more than an incremental advance in our knowledge and understanding of GRHL2 and steroid hormone receptor biology.

R1.2 Mechanistic depth The study provides limited mechanistic insight into how GRHL2 functions as a PR co-regulator. Key mechanistic questions remain unaddressed, such as whether GRHL2 modulates PR activation, the sequential recruitment of co-activators/co-repressors, engages chromatin remodelers, or alters PR DNA-binding dynamics. Incorporating these analyses would considerably strengthen the mechanistic conclusions.

Although our RNA-seq data demonstrate that GRHL2 modulates the expression of PR target genes, and our CUT&RUN experiments show that GRHL2 chromatin binding is reshaped upon R5020 exposure, we acknowledge that we have not further dissected the molecular mechanisms by which GRHL2 functions as a PR co-regulator.

We did consider several follow-up experiments to address this, including PR CUT&RUN in GRHL2 knockdown cells, CUT&RUN for known co-activators such as KMT2C/D and P300, as well as functional studies involving GRHL2 TAD and DBD mutants. However, due to technical and logistical challenges, we were unable to carry out these experiments within the timeframe of this study.

That said, we fully recognize that such approaches would provide deeper mechanistic insight into the interplay between PR and GRHL2. We have therefore explicitly acknowledged this limitation in our limitations of the study section (line 502-507) and mention this as an important avenue for future investigation.

R1.3 Definition of GRHL2-PR regulatory regions (Figure 2) The 6,335 loci defined as GRHL2-PR co-regulatory regions are derived from a PR ChIP-seq performed in the presence of hormone and a GRHL2 ChIP-seq performed in its absence. This approach raises doubts about whether GRHL2 and PR actually co-occupy these regions under ligand stimulation. GRHL2 ChIP-seq experiments in both hormone-treated and untreated conditions are necessary to provide stronger support for this conclusion.

Although bulk ChIP-seq cannot definitively demonstrate simultaneous binding of PR and GRHL2 at the same genomic regions, we agree that the ChIP-seq experiments we present do not provide a definitive answer on if GRHL2 and PR co-occupy these regions under ligand stimulation. As a first step to address this, we performed CUT&RUN experiments for both GRHL2 and PR under untreated and R5020-treated conditions. These experiments revealed a subset of overlapping PR and GRHL2 binding sites (approximately {plus minus}5% of the identified PR peaks under ligand stimulation).

We specifically chose CUT&RUN to minimize artifacts from crosslinking and sonication, thereby reducing background and enabling the mapping of high-confidence direct DNA-binding events: Given that a fraction of GRHL2 physically interacts with PR (Fig1D), it is possible that ChIP-seq detects indirect binding of GRHL2 at PR-bound sites and vice versa. CUT&RUN, by contrast, allows us to identify direct binding sites with higher confidence.

Nonetheless, although outside the scope of the current manuscript, we agree that a dedicated GRHL2 ChIP with and without ligand stimulation would provide additional insight, and we have accordingly added this suggestion to the discussion (line 502-507).

R1.4 Cell model considerations The manuscript relies heavily on the T47DS subclone, which expresses markedly higher PR levels than parental T47D cells (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Kalkhoven et al., Int J Cancer 1995). This raises concerns about physiological relevance. Key findings, including co-IP and qPCR-ChIP experiments, should be validated in additional breast cancer models such as parental T47D, BT474, and MCF-7 cells to generalize the conclusions. Furthermore, data obtained from T47D (PR ChIP-seq, HiChIP, CTCF and Rad21 ChIP-seq) and T47DS (RNA-seq, CUT&RUN) are combined along the manuscript. Given the substantial differences in PR expression between these cell lines, this approach is problematic and should be reconsidered.

We agree that physiological relevance is important to consider. Here, all existing model systems have some limitations. In our experience, it is technically challenging to robustly measure gene expression changes in parental T47D cells (or MCF7 cells, for that matter) in response to progesterone stimulation (Aarts et al., J Mammary Gland Biol Neoplasia 2023). As we set out to integrate PR and GRHL2 binding to downstream target gene induction, we therefore opted for the most progesterone responsive model system (T47DS cells). We agree that observations made in T47D and T47DS cells should not be overinterpreted and require further validation. We have now explicitly acknowledged this and added it to the discussion (line 507-509).

As for the reviewer's suggestion to use MCF7 cells: apart from its suboptimal PR-responsiveness, this cell line is also known to harbor GRHL2 amplification, resulting in elevated GRHL2 levels (Reese et al., Endocrinology2019). By that line of reasoning, the use of MCF7 cells would also introduce concerns about physiological relevance. That being said, and as noted in the discussion (line 390-391), the study by Mohammed et al. which identified GRHL2 as a PR interactor using RIME, was performed in both MCF7 and T47D cells. This further supports the notion that the PR-GRHL2 interaction is not limited to a single cell line.

R1.5 CUT&RUN vs ChIP-seq data The CUT&RUN experiments identify fewer than 10% of the PR binding sites reported in the ChIP-seq datasets. This discrepancy likely results from methodological differences (e.g., absence of crosslinking, potential loss of weaker binding events). The overlap of only 158 sites between PR and GRHL2 under hormone treatment (Figure 3B) provides limited support for the proposed model and should be interpreted with greater caution.

We acknowledge the discrepancy between the number of binding sites between ChIP-seq and CUT&RUN. Indeed, methodological differences likely contribute to the differences in PR binding sites reported between the ChIP-seq and CUT&RUN datasets. As the reviewer correctly notes, the absence of crosslinking and sonication in CUT&RUN reduces detection of weaker binding events. However, it also reduces the detection of indirect binding events which could increase the reported number of peaks in ChIPseq data (e.g. the common presence of "shadow peaks").

As also discussed in our response to R1.3, we deliberately chose the CUT&RUN approach to enable the identification of high-confidence direct DNA-binding events. Since GRHL2 physically interacts with PR, ChIP-seq could potentially capture indirect binding of GRHL2 at PR-bound sites, and vice versa. By contrast, CUT&RUN primarily captures direct DNA-protein interactions, offering a more specific binding profile. Thus, while the number of CUT&RUN binding sites is much smaller than previously reported by ChIP-seq, we are confident that they represent true, direct binding events.

We would also like to emphasize that the model presented in figure 6 does not represent a generic or random gene, but rather a specific gene that is co-regulated by both GRHL2 and PR. In this specific case, regulation is proposed to occur via looping interactions from either individual TF-bound sites (e.g., PR-only or GRHL2-only) or shared GRHL2/PR sites. We do not propose that only shared sites are functionally relevant, nor do we assume that GRHL2 and PR must both be directly bound to DNA at these shared sites. Therefore, overlapping sites identified by ChIP-seq-potentially reflecting indirect binding events-could indeed be missed by CUT&RUN, yet still contribute to gene regulation. To clarify this, we have revised the main text (line 331-334) and the legend of Figure 6 to explicitly state that the model refers to a gene with established co-regulation by both GRHL2 and PR.

R1.6 Gene expression analyses (Figure 4) The RNA-seq analysis after 24 hours of hormone treatment likely captures indirect or secondary effects rather than the direct PR-GRHL2 regulatory program. Including earlier time points (e.g., 4-hour induction) in the analysis would better capture primary transcriptional responses. The criteria used to define PR-GRHL2 co-regulated genes are not convincing and may not reflect the regulatory interactions proposed in the model. Strong basal expression changes in GRHL2-depleted cells suggest that much of the transcriptional response is PR-independent, conflicting with the model (Figure 6). A more straightforward approach would be to define hormone-regulated genes in shControl cells and then examine their response in GRHL2-depleted cells. Finally, integrating chromatin accessibility and histone modification datasets (e.g., ATAC-seq, H3K27ac ChIP-seq) would help establish whether PR-GRHL2-bound regions correspond to active enhancers, providing stronger functional support for the proposed regulatory model.

We thank the reviewer for pointing this out. We now recognize that our criteria for selecting PR/GRHL2 co-regulated genes were not clearly described. To address this, we have revised our approach as per the reviewer's suggestion: we first identified early and sustained PR target genes based on their response at 4 and 24 hours of induction and subsequently overlaid this list with the gene expression changes observed in GRHL2-depleted cells. This revised approach reduced the amount of PR-responsive, GRHL2 regulated target genes from 549 to 298 (46% reduction). We consequently updated all following analyses, resulting in revised figures 4 and 5 and supplementary figures 2,3 and 4. As a result of this revised approach, the number of genes that are transcriptionally regulated by GRHL2 and PR (RNAseq data) that also harbor a PR loop anchor at or near their TSS after 30 minutes of progesterone stimulation (PR HiChIP data) dropped from 114 to 79 (30% reduction). We thank the reviewer for suggesting this more straightforward approach and want to emphasize that our overall conclusions remain unaltered.

As above in our response to R1.3, we want to emphasize that the model presented in figure 6 does not depict a generic or randomly chosen gene, but a gene that is specifically co-regulated by both GRHL2 and PR. We also want to emphasize that the majority of GRHL2's transcriptional activity is PR-independent. This is consistent with the limited fraction of GRHL2 that co-immunoprecipitated with PR (Figure 1D), and with the well-established roles of GRHL2 beyond steroid receptor signaling. In fact, the overall importance of GRHL2 for cell viability in T47D(S) cells is underscored by our inability to generate a full knockout (multiple failed attempts of CRISPR/Cas mediated GRHL2 deletion in T47D(S) and MCF7 cells), and by the strong selection we observed against high-level GRHL2 knockdown using shRNA.

As for the reviewer's suggestion to assess whether GRHL2/PR co-bound regions correspond to active enhancers by integrating H3K27ac and ATAC-seq data: We have re-analyzed publicly available H3K27ac and ATAC-seq datasets from T47D cells (references 42 and 43). These analyses are now added to figure 2 (F and G). The H3K27Ac profile suggests that GRHL2-PR overlapping sites indeed correspond to more active enhancers (Figure 2F), with a proposed role for GRHL2 since siGRHL2 affects the accessibility of these sites (Figure 2G).

Minor comments Page 19: The statement that "PR and GRHL2 trigger extensive chromatin reorganization" is not experimentally supported. ATAC-seq would be an appropriate method to test this directly.

We agree with the reviewer and have removed this sentence, as it does not contribute meaningfully to the flow of the manuscript.

Prior literature on GRHL2 as a steroid receptor co-regulator should be discussed more thoroughly.

We now added additional literature on GRHL2 as a steroid hormone receptor co-regulator in the discussion (line 397-401) and we cite the papers suggested by R1 in R1.1 (references 25 and 54).

Reviewer #1 (Significance (Required)):

The identification of novel PR co-regulators is an important objective, as the mechanistic basis of PR signaling in breast cancer remains incompletely understood. The main strength of this study lies in highlighting GRHL2 as a factor influencing PR genomic binding and transcriptional regulation, thereby expanding the repertoire of regulators implicated in PR biology.

That said, the novelty is limited, given the established roles of GRHL2 in ER and AR regulation. Mechanistic insight is underdeveloped, and the reliance on an engineered T47DS model with supra-physiological PR levels reduces the general impact. Without validation in physiologically relevant breast cancer models and clearer separation of direct versus indirect effects, the overall advance remains modest.

The manuscript will be of interest to a specialized audience in the fields of nuclear receptor signaling, breast cancer genomics, and transcriptional regulation. Broader appeal, including translational or clinical relevance, is limited in its current form.

We have addressed all of these points in our response above and agree that with our implemented changes, this study should reach (and appeal to) an audience interested in transcriptional regulation, chromatin biology, hormone receptor signaling and breast cancer.

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

The authors present a study investigating the role of GRHL2 in hormone receptor signaling. Previous research has primarily focused on GRHL2 interaction with estrogen receptor (ER) and androgen receptor (AR). In breast cancer, GRHL2 has been extensively studied in relation to ER, while its potential involvement with the progesterone receptor (PR) remains largely unexplored. This is the rationale of this study to investigate the relation between PR and GRHL2. The authors demonstrate an interaction between GRHL2 and PR and further explore this relationship at the level of genomic binding sites. They also perform GRHL2 knockdown experiments to identify target genes and link these transcriptional changes back to GRHL2-PR chromatin occupancy. However, several conceptual and technical aspects of the study require clarification to fully support the authors' conclusions.

R2.1 Given the high sequence similarity among GRHL family members, this raises questions about the specificity of the antibody used for GRHL2 RIME. The authors should address whether the antibody cross-reacts with GRHL1 or GRHL3. For example, GRHL1 shows a higher log fold change than GRHL2 in the RIME data.

Indeed, GRHL1, GRHL2, and GRHL3 are structurally related. They share a similar domain organization and are all {plus minus}70kDa in size. Sequence similarity is primarily confined to the DNA-binding domain, with GRHL2 and GRHL3 showing 81% similarity in this region, and GRHL1 showing 63% similarity to GRHL2/3 (Ming, Nucleic Acids Res 2018).

The antibody used, sourced from the Human Protein Atlas, is widely used in the field. It targets an epitope within the transactivation domain (TAD) of GRHL2-a region with relatively low sequence similarity to the corresponding domains in GRHL1 and GRHL3.

We assessed the specificity of the antibody using western blotting (Supplementary Figure 2A) in T47DS wild-type and GRHL2 knockdown cells. As expected, GRHL2 protein levels were reduced in the knockdown cells providing convincing evidence that the antibody recognizes GRHL2. The remaining signal in shGRHL2 knockdown cells could either be due to remaining GRHL2 protein or due to the antibody detecting GRHL1/3. Furthermore, the observed high log-fold enrichment of GRHL1 in our RIME may reflect known heterodimer formation between GRHL1 and GRHL2, rather dan antibody cross-reactivity. As such, we cannot formally rule out cross-reactivity and have mentioned this in the limitations section (line 497-501).

R2.2 In addition, in RIME experiments, one would typically expect the bait protein to be among the most highly enriched proteins compared to control samples. If this is not the case, it raises questions about the efficiency of the pulldown, antibody specificity, or potential technical issues. The authors should comment on the enrichment level of the bait protein in their data to reassure readers about the quality of the experiment.

We agree with the reviewer that this information is crucial for assessing the quality of the experiment. We have therefore added the enrichment levels (log₂ fold change of IgG control over pulldown) to the methods section (line 592).

As the reviewer notes, GRHL2 was not among the top enriched proteins in our dataset. This is due to unexpectedly high background binding of GRHL2 to the IgG control antibody/beads, for which we currently have no explanation. As a result, although we detected many unique GRHL2 peptides, observed high sequence coverage (>70%), and GRHL2 ranked among the highest in both iBAQ and LFQ values, its relative enrichment was reduced due to the elevated background. During our RIME optimization, Coomassie blue staining of input and IP samples revealed a band at the expected molecular weight of GRHL2 in the pull down samples that was absent in the IgG control (see figure 1 for the reviewer below, 4 right lanes), supporting the conclusion that GRHL2 is specifically enriched in our GRHL2 RIME samples. Combined with enrichment of some of the expected interacting proteins (e.g. KMT2C and KMT2D), we are convinced that the experiment of sufficient quality to support our conclusions.

Figure 1 for reviewer: Coomassie blue staining of input and IP GRHL2 and IgG RIME samples. NT = non-treated, T = treated.

R2.3 The authors report log2 fold changes calculated using iBAQ values for the bait versus IgG control pulldown. While iBAQ provides an estimate of protein abundance within samples, it is not specifically designed for quantitative comparison between samples without appropriate normalization. It would be helpful to clarify the normalization strategy applied and consider using LFQ intensities.

We understand the reviewer's concern. Due to the high background observed in the IgG control sample (see R2.2), the LFQ-based normalization did not accurately reflect the enrichment of GRHL2, which was clearly supported by other parameters such as the number of unique peptides (see rebuttal Table 1). After discussions with our Mass Spectrometry facility, we decided to consider the iBAQ values-which reflect the absolute protein abundance within each sample-as a valid and informative measure of enrichment. In the context of elevated background levels, iBAQ provides an alternative and reliable metric for assessing protein enrichment and was therefore used for our interactor analysis.

Unique peptides

IBAQ GRHL2

IBAQ IgG

LFQ GRHL2

LFQ IgG

GRHL2

52

1753400.00

155355.67

5948666.67

3085700.00

GRHL1

23

56988.33

199.03

334373.33

847.23

*Table 1. Unique peptide, IBAQ and LFQ values of the GRHL2 and IgG pulldowns for GRHL2 and GRHL1 *

R2.4 Other studies have reported PR RIME, which could be a valuable source to investigate whether GRHL proteins were detected.

We thank the reviewer for pointing this out. We are aware of the PR RIME, generated by Mohammed et al., which we refer to in the discussion (lines 390-391). This study indeed identified GRHL2 as a PR-interacting protein in MCF7 and T47D cells. Although they do not mention this interaction in the text, the interaction is clearly indicated in one of the figures from their paper, which supports our findings. To our knowledge, no other PR RIME datasets in MCF7 or T47D cells have been published to date.

R2.5 In line 137, the term "protein score" is mentioned. Could the authors please clarify what this means and how it was calculated.

We agree that this point was not clearly explained in the original text. The scores presented reflect the MaxQuant protein identification confidence, specifically the sum of peptide-level scores (from Andromeda), which indicates the relative confidence in protein detection. We have now added this clarification to line 137 and to the legend of Figure 1.

R2.6 In line 140-141. The fact that GRHL2 interacts with chromatin remodelers does not by itself prove that GRHL2 acts as a pioneer factor or chromatin modulator. Demonstrating pioneer function typically requires direct evidence of chromatin opening or binding to closed chromatin regions (e.g., ATAC-seq, nucleosome occupancy assays). I recommend revising this statement or providing supporting evidence.

We agree that the fact that GRHL2 interacts with chromatin remodelers does not by itself prove that GRHL2 acts as a pioneer factor or chromatin modulator. However, a previous study (Jacobs et al, Nature genetics, 2018) has shown directly that the GRHL family members (including GRHL2) have pioneering function and regulate the accessibility of enhancers. We adapted line 140-141 to state this more clearly. In addition, our newly added data in Figure 2G also support the fact that GRHL2 has a role in regulating chromatin accessibility in T47D cells.

R2.7 The pulldown Western blot lacks an IgG control in panel D.

This is correct. As the co-IP in Figure 1D served as a validation of the RIME and was specifically aimed at determining the effect of hormone treatment on the observed PR/GRHL2 interaction, we did not perform this control given the scale of the experiment. However, during RIME optimization, we performed GRHL2 staining of the IgG controls by western blot, shown in figure 2 for the reviewer below. As stated above, some background GRHL2 signal was observed in the IgG samples, but a clear enrichment is seen in the GRHL2 IP.

Taken together, we believe that the well-controlled RIME, combined with the co-IP presented, provides strong evidence that the observed signal reflects a genuine GRHL-PR interaction.

Figure 2 for reviewer: WB of input and IP GRHL2 and IgG RIME samples stained for GRHL2. NT = non-treated, T = treated

R2.8 Depending on the journal and target audience, it may be helpful to briefly explain what R5020 is at its first mention (line 146).

Thank you. We have adapted this accordingly.

R2.9 The authors state that three technical replicates were performed for each experimental condition. It would be helpful to clarify the expected level of overlap between biological replicates of RIME experiments. This clarification is necessary, especially given the focus on uniquely enriched proteins in untreated versus treated cells, and the observation that some identified proteins in specific conditions are not chromatin-associated. Replicates or validations would strengthen the findings.

We use the term technical rather than biological replicates because for cell lines, defining true biological replicates is challenging, as most variability arises from experimental rather than biological differences. To introduce some variation, we split our T47DS cells into three parallel dishes 5 days prior to starting the treatment. We purposely did this, to minimize to minimize the likelihood that proteins identified as uniquely enriched are artifacts. Each of the three technical replicates comes from one of these three parallel splits (so equal passage numbers but propagated in parallel dishes for 5 days before the start of the experiment).

To generate the three technical replicates for our RIME, we plated cells from the parallel grown splits. Treatments for the three replicates were performed per replicate. Samples were crosslinked, harvested and lysed for subsequent RIME analysis, the three replicates were processed in parallel, for technical and logistical reasons. To clarify the experimental setup, we have updated the methods section accordingly (lines 566-568).

As for the detection of non-chromatin-associated proteins: We cannot rule out that these are artifacts, as they may arise from residual cytosolic lysate during nuclear extraction. Alternatively, they could reflect a more dynamic subcellular localization of these proteins than currently annotated or appreciated.

R2.10 The volcano plot for the RIME experiment appears to show three distinct clusters of proteins on the right, which is unusual for this type of analysis. The presence of these apparent groupings may suggest an artifact from the data processing, such as imputation. Can the authors clarify the origin of these groupings? If it is due to imputation or missing values, I recommend applying a stricter threshold, such as requiring detection in all three replicates (3/3) to improve the robustness of the enrichment analysis and increase confidence in the identified interactors.

We thank the reviewer for pointing this out. As suggested, we re-evaluated the imputation and applied a stricter threshold, requiring detection in all three replicates. Indeed, the separate clusters were due to missing values, therefore we now revised the imputation method by imputing values based on the normal distribution. Using this revised analysis, we identify 2352 GRHL2 interactors instead of 1140, but the number of interacting proteins annotated as transcription factors or chromatin-associated/modifying proteins was still 103. Figure 1B, 1E, and Supplementary Figure 4A have been updated accordingly. We also revised the methods section to reflect this change. We think this suggestion has improved our analysis of the data and we thank the reviewer for pointing this out.

R2.11 The statement that "PR and GRHL2 frequently overlap" may be overstated given that only ~700 overlapping sites are reported (cut&run).

We have replaced "frequently overlap" by "can overlap" (line 229-230).

R2.12 The model in Figure 6 suggests limited chromatin occupancy of PR and GRHL2 in hormone-depleted conditions, consistent with the known requirement of ligand for stable PR-DNA binding. However, Figure 1 shows no major difference in GRHL2-PR interaction between untreated and hormone-treated cells. This raises questions about where and how this interaction occurs in the absence of hormone. Since PR binding to chromatin is typically minimal without ligand, can the authors clarify this given that RIME data reflect chromatin-bound interactions.

Indeed, the model in figure 6 suggests limited chromatin occupancy of PR and GRHL2 under hormone-depleted conditions. It is, however, important to note that the locus shown represents a gene regulated by both PR and GRHL2 - and not just any gene. We recognize that this was not sufficiently clear in the original version, and we have now clarified this in both the main text (line 331-334) and the figure legend.

We propose that PR and GRHL2 bind or become enriched at enhancer sites associated with their target genes upon ligand stimulation. This is consistent with the known requirement of ligand for stable PR-DNA binding and with our observation that PR/GRHL2 overlapping peaks are detected only in the ligand-treated condition of the CUT&RUN experiment. Given the broader role of GRHL2, it also binds chromatin independently of progesterone and the progesterone receptor, which is why we included-but did not focus on-GRHL2-only binding events in our model.

We would also like to clarify that, although RIME includes a nuclear enrichment step that enriches for chromatin-associated proteins, the pulldown is performed on nuclear lysates. Therefore, it captures both chromatin-bound protein complexes and freely soluble nuclear complexes, which unfortunately cannot be distinguished. GRHL2 is well established as a nuclear protein (Zeng et al., Cancers 2024; Riethdorf et al., International Journal of Cancer 2015), and although PR is classically described as translocating to the nucleus upon hormone stimulation, several studies-including our own-have shown that PR is continuously present in the nucleus (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Frigo et al., Essays Biochem. 2021).

We therefore propose that PR and GRHL2 may already interact in the nucleus without directly binding to chromatin. Given our observation that GRHL2 binding sites on the chromatin are redistributed upon R5020 mediated signaling activation, we hypothesize that such pre-formed PR-GRHL2 nuclear complexes may assist the rapid recruitment of GRHL2 to progesterone-responsive chromatin regions.

We have expanded the discussion to include a dedicated section addressing this point (line 376-388).

R2.13 It would be of interest to assess the overlap between the proteins identified in the RIME experiment and the motif analysis results.

In the discussion section of our original manuscript, we highlighted some overlapping proteins in the RIME and motif analysis, including STAT6 and FOXA1. However, we had not yet systematically analyzed overlap in both analyses. To address this, we now compared all enriched motifs (so not only the top 5 as displayed in our figures) under GRHL2, PR, and GRHL2/PR shared sites from both the CUT&RUN and ChIP-seq datasets with the proteins identified as GRHL2 interactors in our RIME. Although we identified numerous GRHL2-associated proteins, relatively few of them were transcription factors whose binding motifs were also enriched under GRHL2 peaks.

In our revised manuscript we have added a section in the discussion highlighting our systematic overlap of the results of our RIME experiment and the motif enrichment of the ChIP-seq and CUT&RUN analysis (line 415-436).

R2.14 The authors chose CUT&RUN to assess chromatin binding of PR and GRHL2. Given that RIME is also based on chromatin immunoprecipitation - ChIP protocol, it would be helpful to clarify why CUT&RUN was selected over ChIP-seq for the DNA-binding assays. What is the overlap with published data?

As also mentioned in our response to R1.3 and R1.5, we deliberately chose the CUT&RUN approach to minimize artifacts introduced by crosslinking and sonication, thereby reducing background and allowing the identification of high-confidence, direct DNA-binding events. Since GRHL2 physically interacts with PR, ChIP-seq could potentially capture indirect binding of GRHL2 at PR-bound sites (and vice versa). In contrast, CUT&RUN primarily detects direct DNA-protein interactions, providing a more specific and accurate binding profile. Additionally, CUT&RUN serves as an independent validation method for data obtained using ChIP-like protocols.

Since CUT&RUN, similar to ChIP, can show limited reproducibility (Nordin et al., Nucleic Acids Research, 2024), and to our knowledge few PR CUT&RUN and no GRHL2 CUT&RUN datasets are currently available, it is challenging to directly compare our data with published datasets. Nevertheless, studies performing PR or ER CUT&RUN (Gillis et al., Cancer Research, 2024; Reese et al., Molecular and Cellular Biology, 2022) report a comparable number of peaks-in the same range of thousands-as observed in our data. This suggests that a single CUT&RUN experiment in general may detect fewer events than a single ChIP-seq experiment, but that the peaks that are found are likely to reflect direct binding events.

Reviewer #2 (Significance (Required)):

General Assessment: This study investigates the role of the transcription factor GRHL2 in modulating PR function, using RIME and CUT&RUN to explore protein-protein and protein-chromatin interactions. GRHL2 have been implicated in epithelial biology and transcriptional regulation and interaction with steroid hormone receptors has been reported. This study extends the field by showing a functional link between GRHL2 and PR, which has implications for understanding hormone-dependent gene regulation.

The research will primarily interest a specialized audience in transcriptional regulation, chromatin biology, and hormone receptor signaling.

Key words for this reviewer: chromatin biology, transcription factor function, epigenomics, and proteomics.

We agree that with our implemented changes, this study should reach (and appeal to) an audience interested in transcriptional regulation, chromatin biology, hormone receptor signaling and breast cancer.

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

This study explores the important transcriptional coordination role of Grainyhead-like 2 (GRHL2) on the transcriptional regulatory function of progesterone receptor (PR). In this paper, the authors start with their recruitment characteristics, take into account their regulatory effects on downstream genes and their effects on the occurrence and development of breast cancer, and further clarify the coordination between them in three-dimensional space. The interaction between GRHL2 and PR, and the subsequent important influence on the co-regulated genes by GRHL2 and PR are analyzed. The overall framework of this study is mainly by RNA seq and CUT-TAG analysis, the molecular mechanism underlying the association between GRHL2 and PR and regulation function of two proteins in breast cancer is not clearly clarified. Some details need to be further improved：

Major comments: R3.1 For Fig.1D, the molecular weight of each protein should be marked in the diagram, and the expression of GRHL2 in the input group should be supplemented.

We apologize for not including molecular weights in our initial submission. We are not entirely clear what the reviewer means with their statement that "the expression of GRHL2 in the input group should be supplemented". The blot depicted in Figure 1D shows both the input signal and the IP. For the reviewer's information, the full Western blot is depicted below.

Figure 3 for reviewer: Full WBs of input and IP GRHL2 samples stained for GRHL2 or PR. NT = non-treated, T = treated

R3.2 In Fig.2B and Fig 5C, it should be describe well whether GRHL2 recruitment is in the absence or presence of R5020? How about the co-occupancy of PR and GRHL2 region, Promoter or enhancer region? It would be better to show histone marks such as H3K27ac and H3K4me1 to annotate the enhancer region.

As also stated in our response to R1.3, we acknowledge that the ChIP-seq experiments cannot definitively determine whether GRHL2 and PR co-occupy genomic regions under ligand-stimulated conditions, since the GRHL2 dataset was generated in the absence of progesterone stimulation (as indicated in lines 167-169). To clarify this, we have now specified this detail in the legend of figure 2 by noting "untreated GRHL2 ChIP." To directly assess GRHL2 chromatin binding under progesterone-stimulated conditions, we performed CUT&RUN experiments for both GRHL2 and PR under untreated and R5020-treated conditions. These experiments revealed a subset of overlapping PR and GRHL2 binding sites (approximately 5% of all identified PR peaks.

In our original manuscript, we performed genomic annotation of the GRHL2, PR, and GRHL2/PR overlapping peaks (Figure 2E) and found that most of these sites were located in intergenic regions, where enhancers are typically found, with ~20% located in promoter regions. We appreciate the reviewer's suggestion to further overlap the ChIP-seq peaks with histone marks such as H3K27ac and H3K4me1. We have now incorporated publicly available ATAC-seq and H3K27ac ChIP datasets in our revised manuscript (as also suggested by Reviewer 1) and find that shared GRHL2/PR sites are indeed located in active enhancer regions marked by H3K27ac (see Figure 2F). Additionally, as expected, we find that GRHL2/PR overlapping sites are enriched at open chromatin (Figure 2G).

R3.3 What is the biological function analysis by KEGG or GO analysis for the overlapping genes from VN plots of RNA-seq with CUT-TAG peaks. The genes co-regulated by GRH2L and PR are further determined.

For us, it is not entirely clear what reviewer 3 is asking here, but we can explain the following: as it is challenging to integrate HiChIP with CUT&RUN, due to the fundamentally different nature of the two techniques, we chose not to directly assign genes to CUT&RUN peaks. However, we did carefully link the GRHL2, PR, and GRHL2/PR ChIP-seq peaks to their target genes by integrating chromatin looping data from a PR HiChIP analysis. The result from this analysis is depicted in Figure 4B.

As suggested by this reviewer, we also performed a GO-term analysis on the 79 genes that are regulated by both GRHL2 and PR (we now have 79 genes after the re-analysis as suggested in R1.6). The corresponding results are provided for the reviewer in figure 3 of this rebuttal (below). As this additional analysis does not provide further biological insight beyond what is already presented in Figure 4C, we decided to not include this figure in the manuscript.

Figure 4 for reviewer: GO-term analysis on the 79 GRHL2-PR co-regulated genes that are transcriptionally regulated by GRHL2 and PR and that also harbor a PR HiChIP loop anchor at or near their TSS

R3.4 Western blotting should be performed to determine the protein levels of downstream genes co-regulated genes by GRH2L and PR in the absence or presence of R5020.

We agree that determining the response of co-regulated is important. Therefore, in Figure 4D, we present three representative examples of genes that are directly co-regulated by GRHL2 and PR-specifically, genes that are differentially expressed after 4 hours of R5020 exposure. Although protein levels of the targets are of functional importance, GRHL2 and PR are of transcription factors whose immediate effects are primarily exerted at the level of gene transcription. Therefore, in our opinion, changes in mRNA abundance provide the most direct and mechanistically relevant readout of their regulatory activity.

R3.5 The author mentioned that this study positions that GRHL2 acts as a crucial modulator of steroid hormone receptor function, while the authors do not provide the evidences that how does GRHL2 regulate PR-mediated transactivation, and how about these two proteins subcellular distribution in breast cancer cells.

We agree that while our RNA-seq data demonstrate that GRHL2 modulates the expression of PR target genes, and our CUT&RUN experiments show that GRHL2 chromatin binding is reshaped upon R5020 exposure, we have not yet further dissected the molecular mechanism by which GRHL2 functions as a PR co-regulator.

As also mentioned in our response to R1.2, we did consider several follow-up experiments to address this, including PR CUT&RUN in GRHL2 knockdown cells, CUT&RUN for known co-activators such as KMT2C/D and P300, as well as functional studies involving GRHL2 TAD and DBD mutants. However, due to technical and logistical challenges, we were unable to carry out these experiments within the timeframe of this study.

That said, we fully recognize that such approaches would provide deeper mechanistic insight into the interplay between PR and GRHL2. We have therefore explicitly acknowledged this limitation in our limitations of the study section (lines 502-507) and consider it an important avenue for future investigation.

Regarding the subcellular distribution in breast cancer cells: As also mentioned in our response to R2.12, GRHL2 is well established as a nuclear protein (Zeng et al., Cancers 2024; Riethdorf et al., International Journal of Cancer 2015), and although PR is classically described as translocating to the nucleus upon hormone stimulation, several studies-including our own-have shown that PR is continuously present in the nucleus (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Frigo et al., Essays Biochem. 2021). Thus, both proteins mostly reside in the nucleus in breast (cancer) cells both in the absence and presence of hormone stimulation, but dynamic subcellular shuttling is likely to occur.

Minor comments: Please describe in more detail the relationship between PR and GRHL2 binding independent of the hormone in the discussion section.

As also mentioned in our response to R2.12, we have expanded the discussion to include a dedicated section addressing this point (lines 376-388).

Reviewer #3 (Significance (Required)):

Advance: Compare the study to existing published knowledge, it fills a gap. The authors provide RNA seq and CUT-TAG sequence analysis to show the recruitment of GRHL2 and PR and the co-regulated genes in the absence or presence of progesterone.

Audience: breast surgery will be interested, and the audiences will cover clinical and basic research.

My expertise is focused on the epigenetic modulation of steroid hormone receptors in the related cancers, such as breast cancer, prostate cancer, and endometrial carcinoma.

We agree that with our implemented changes, this study should reach (and appeal to) an audience interested in transcriptional regulation, chromatin biology, hormone receptor signaling and breast cancer.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

This study explores the important transcriptional coordination role of Grainyhead-like 2 (GRHL2) on the transcriptional regulatory function of progesterone receptor (PR). In this paper, the authors start with their recruitment characteristics, take into account their regulatory effects on downstream genes and their effects on the occurrence and development of breast cancer, and further clarify the coordination between them in three-dimensional space. The interaction between GRHL2 and PR, and the subsequent important influence on the co-regulated genes by GRHL2 and PR are analyzed. The overall framework of this study is mainly by RNA seq and CUT-TAG analysis, the molecular mechanism underlying the association between GRHL2 and PR and regulation function of two proteins in breast cancer is not clearly clarified. Some details need to be further improved：

Major comments:

1. For Fig.1D, the molecular weight of each protein should be marked in the diagram, and the expression of GRHL2 in the input group should be supplemented.
2. In Fig.2B and Fig 5C, it should be describe well whether GRHL2 recruitment is in the absence or presence of R5020? How about the co-occupancy of PR and GRHL2 region, Promoter or enhancer region? It would be better to show histone marks such as H3K27ac and H3K4me1 to annotate the enhancer region.
3. What is the biological function analysis by KEGG or GO analysis for the overlapping genes from VN plots of RNA-seq with CUT-TAG peaks. The genes co-regulated by GRH2L and PR are further determined.
4. Western blotting should be performed to determine the protein levels of downstream genes co-regulated genes by GRH2L and PR in the absence or presence of R5020.
5. The author mentioned that this study positions that GRHL2 acts as a crucial modulator of steroid hormone receptor function, while the authors do not provide the evidences that how does GRHL2 regulate PR-mediated transactivation, and how about these two proteins subcellular distribution in breast cancer cells.

Minor comments:

Please describe in more detail the relationship between PR and GRHL2 binding independent of the hormone in the discussion section.

Significance

Advance: Compare the study to existing published knowledge, it fills a gap. The authors provide RNA seq and CUT-TAG sequence analysis to show the recruitment of GRHL2 and PR and the co-regulated genes in the absence or presence of progesterone.

Audience: breast surgery will be interested, and the audiences will cover clinical and basic research.

My expertise is focused on the epigenetic modulation of steroid hormone receptors in the related cancers, such as breast cancer, prostate cancer, and endometrial carcinoma.

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

The authors present a study investigating the role of GRHL2 in hormone receptor signaling. Previous research has primarily focused on GRHL2 interaction with estrogen receptor (ER) and androgen receptor (AR). In breast cancer, GRHL2 has been extensively studied in relation to ER, while its potential involvement with the progesterone receptor (PR) remains largely unexplored. This is the rational of this study to investigate the relation between PR and GRHL2. The authors demonstrate an interaction between GRHL2 and PR and further explore this relationship at the level of genomic binding sites. They also perform GRHL2 knockdown experiments to identify target genes and link these transcriptional changes back to GRHL2-PR chromatin occupancy. However, several conceptual and technical aspects of the study require clarification to fully support the authors' conclusions.

1. Given the high sequence similarity among GRHL family members, this raises questions about the specificity of the antibody used for GRHL2 RIME. The authors should address whether the antibody cross-reacts with GRHL1 or GRHL3. For example, GRHL1 shows a higher log fold change than GRHL2 in the RIME data.
2. In addition, in RIME experiments, one would typically expect the bait protein to be among the most highly enriched proteins compared to control samples. If this is not the case, it raises questions about the efficiency of the pulldown, antibody specificity, or potential technical issues. The authors should comment on the enrichment level of the bait protein in their data to reassure readers about the quality of the experiment.
3. The authors report log2 fold changes calculated using iBAQ values for the bait versus IgG control pulldown. While iBAQ provides an estimate of protein abundance within samples, it is not specifically designed for quantitative comparison between samples without appropriate normalization. It would be helpful to clarify the normalization strategy applied and consider using LFQ intensities.
4. Other studies have reported PR RIME, which could be a valuable source to investigate whether GRHL proteins were detected.
5. In line 137, the term "protein score" is mentioned. Could the authors please clarify what this means and how it was calculated.
6. In line 140-141. The fact that GRHL2 interacts with chromatin remodelers does not by itself prove that GRHL2 acts as a pioneer factor or chromatin modulator. Demonstrating pioneer function typically requires direct evidence of chromatin opening or binding to closed chromatin regions (e.g., ATAC-seq, nucleosome occupancy assays). I recommend revising this statement or providing supporting evidence.
7. The pulldown Western blot lacks an IgG control in panel D.
8. Depending on the journal and target audience, it may be helpful to briefly explain what R5020 is at its first mention (line 146).
9. The authors state that three technical replicates were performed for each experimental condition. It would be helpful to clarify the expected level of overlap between biological replicates of RIME experiments. This clarification is necessary, especially given the focus on uniquely enriched proteins in untreated versus treated cells, and the observation that some identified proteins in specific conditions are not chromatin-associated. Replicates or validations would strengthen the findings.
10. The volcano plot for the RIME experiment appears to show three distinct clusters of proteins on the right, which is unusual for this type of analysis. The presence of these apparent groupings may suggest an artifact from the data processing, such as imputation. Can the authors clarify the origin of these groupings? If it is due to imputation or missing values, I recommend applying a stricter threshold, such as requiring detection in all three replicates (3/3) to improve the robustness of the enrichment analysis and increase confidence in the identified interactors.
11. The statement that "PR and GRHL2 frequently overlap" may be overstated given that only ~700 overlapping sites are reported (cut&run).
12. The model in Figure 6 suggests limited chromatin occupancy of PR and GRHL2 in hormone-depleted conditions, consistent with the known requirement of ligand for stable PR-DNA binding. However, Figure 1 shows no major difference in GRHL2-PR interaction between untreated and hormone-treated cells. This raises questions about where and how this interaction occurs in the absence of hormone. Since PR binding to chromatin is typically minimal without ligand, can the authors clarify this given that RIME data reflect chromatin-bound interactions.
13. It would be of interest to assess the overlap between the proteins identified in the RIME experiment and the motif analysis results.
14. The authors chose CUT&RUN to assess chromatin binding of PR and GRHL2. Given that RIME is also based on chromatin immunoprecipitation - ChIP protocol, it would be helpful to clarify why CUT&RUN was selected over ChIP-seq for the DNA-binding assays. What is the overlap with published data?

Significance

General Assessment:

This study investigates the role of the transcription factor GRHL2 in modulating PR function, using RIME and CUT&RUN to explore protein-protein and protein-chromatin interactions. GRHL2 have been implicated in epithelial biology and transcriptional regulation and interaction with steroid hormone receptors has been reported. This study extends the field by showing a functional link between GRHL2 and PR, which has implications for understanding hormone-dependent gene regulation.

The research will primarily interest a specialized audience in transcriptional regulation, chromatin biology, and hormone receptor signaling.

Key words for this reviewer: chromatin biology, transcription factor function, epigenomics, and proteomics.

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 manuscript by Aarts et al. explores the role of GRHL2 as a regulator of the progesterone receptor (PR) in breast cancer cells. The authors show that GRHL2 and PR interact in a hormone-independent manner and, based on genomic analyses, propose that they co-regulate target genes via chromatin looping. To support this model, the study integrates both newly generated and previously published datasets, including ChIP-seq, CUT&RUN, RNA-seq, and chromatin interaction assays, in breast cancer cell models (T47DS and T47D).

Major comments:

1. Novelty of GRHL2 in steroid receptor biology The role of GRHL2 as a co-regulator of steroid hormone receptors has previously been described for ER (J Endocr Soc. 2021;5(Suppl 1):A819) and AR (Cancer Res. 2017;77:3417-3430). In the ER study, the authors also employed a GRHL2 ΔTAD T47D cell model. Therefore, while this manuscript extends GRHL2 involvement to PR, the contribution appears incremental rather than conceptual.
2. Mechanistic depth The study provides limited mechanistic insight into how GRHL2 functions as a PR co-regulator. Key mechanistic questions remain unaddressed, such as whether GRHL2 modulates PR activation, the sequential recruitment of co-activators/co-repressors, engages chromatin remodelers, or alters PR DNA-binding dynamics. Incorporating these analyses would considerably strengthen the mechanistic conclusions.
3. Definition of GRHL2-PR regulatory regions (Figure 2) The 6,335 loci defined as GRHL2-PR co-regulatory regions are derived from a PR ChIP-seq performed in the presence of hormone and a GRHL2 ChIP-seq performed in its absence. This approach raises doubts about whether GRHL2 and PR actually co-occupy these regions under ligand stimulation. GRHL2 ChIP-seq experiments in both hormone-treated and untreated conditions are necessary to provide stronger support for this conclusion.
4. Cell model considerations The manuscript relies heavily on the T47DS subclone, which expresses markedly higher PR levels than parental T47D cells (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Kalkhoven et al., Int J Cancer 1995). This raises concerns about physiological relevance. Key findings, including co-IP and qPCR-ChIP experiments, should be validated in additional breast cancer models such as parental T47D, BT474, and MCF-7 cells to generalize the conclusions. Furthermore, data obtained from T47D (PR ChIP-seq, HiChIP, CTCF and Rad21 ChIP-seq) and T47DS (RNA-seq, CUT&RUN) are combined along the manuscript. Given the substantial differences in PR expression between these cell lines, this approach is problematic and should be reconsidered.
5. CUT&RUN vs ChIP-seq data The CUT&RUN experiments identify fewer than 10% of the PR binding sites reported in the ChIP-seq datasets. This discrepancy likely results from methodological differences (e.g., absence of crosslinking, potential loss of weaker binding events). The overlap of only 158 sites between PR and GRHL2 under hormone treatment (Figure 3B) provides limited support for the proposed model and should be interpreted with greater caution.
6. Gene expression analyses (Figure 4) The RNA-seq analysis after 24 hours of hormone treatment likely captures indirect or secondary effects rather than the direct PR-GRHL2 regulatory program. Including earlier time points (e.g., 4-hour induction) in the analysis would better capture primary transcriptional responses. The criteria used to define PR-GRHL2 co-regulated genes are not convincing and may not reflect the regulatory interactions proposed in the model. Strong basal expression changes in GRHL2-depleted cells suggest that much of the transcriptional response is PR-independent, conflicting with the model (Figure 6). A more straightforward approach would be to define hormone-regulated genes in shControl cells and then examine their response in GRHL2-depleted cells. Finally, integrating chromatin accessibility and histone modification datasets (e.g., ATAC-seq, H3K27ac ChIP-seq) would help establish whether PR-GRHL2-bound regions correspond to active enhancers, providing stronger functional support for the proposed regulatory model.

Minor comments

Page 19: The statement that "PR and GRHL2 trigger extensive chromatin reorganization" is not experimentally supported. ATAC-seq would be an appropriate method to test this directly.

Prior literature on GRHL2 as a steroid receptor co-regulator should be discussed more thoroughly.

Significance

The identification of novel PR co-regulators is an important objective, as the mechanistic basis of PR signaling in breast cancer remains incompletely understood. The main strength of this study lies in highlighting GRHL2 as a factor influencing PR genomic binding and transcriptional regulation, thereby expanding the repertoire of regulators implicated in PR biology. That said, the novelty is limited, given the established roles of GRHL2 in ER and AR regulation. Mechanistic insight is underdeveloped, and the reliance on an engineered T47DS model with supra-physiological PR levels reduces the general impact. Without validation in physiologically relevant breast cancer models and clearer separation of direct versus indirect effects, the overall advance remains modest.

The manuscript will be of interest to a specialized audience in the fields of nuclear receptor signaling, breast cancer genomics, and transcriptional regulation. Broader appeal, including translational or clinical relevance, is limited in its current form.

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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

Summary

The authors report the construction and validation of a novel SOX2-TBXT dual-reporter mouse embryonic stem cell (mESC) line, a tool enabling the simultaneous, live visualization of SOX2 and TBXT expression. Using this line, they established an in vitro differentiation system that generates populations of SOX2/TBXT co-expressing cells which mimic neuromesodermal progenitors (NMPs). The authors combined clonal analysis to assess the fate potential of these cells and applied gastruloid models to dissect the functional consequences of gene expression dynamics on axis elongation. The central finding is that the level of TBXT expression predicts and directs lineage potential. This work identifies specific expression thresholds that bias progenitors toward a mesodermal fate.

Major comments

The study's conclusions would be substantially strengthened by more direct validation in an embryonic context. Could the authors quantify endogenous SOX2 and TBXT protein levels of the NMPs in the mouse embryos with immunofluorescence? This would test whether a similar heterogeneity in TBXT expression exists in vivo and whether it correlates with the cells' spatial position.

The role of SOX2 in the quantitative model seems underdeveloped. To justify the authors' claim, could the authors analyze their existing imaging data in more detail to disentangle if the absolute TBXT level is essential rather than the ratio of Sox2 to Tbxt is the driving factor for determining NMP fate?

It seems that SOX2 expression also appears heterogeneous from both in vitro differentiation and gastruloid models. Quantifications, and a discussion of this heterogeneity and whether it influences the fate-decision process would be helpful.

To support the authors' claim that the reporter line recapitulates endogenous protein expression in vivo (lines 121-128), please include a control immunostaining of wild-type embryo for SOX2 and TBXT to compare expression patterns side-by-side with those embryos shown in Figure 1B, Suppl. Fig. 1C, D. To substantiate the claims regarding cellular expression patterns within the embryo (line 125-128), the use of higher-resolution imaging, such as confocal microscopy, is recommended.

The differentiation trajectory described culminates in a double-negative (Sox2-mCherry-negative, Tbxt-GFP-negative) population (lines 246-247). To provide a more complete picture of this fate progression, could the authors perform qPCR for relevant lineage markers to validate the molecular identity of this terminal population?

Minor comments

Scale bars for micrographs are missing in Figure 1B, Suppl. Fig. 1C, and D. The claims regarding the dynamics of TBXT and SOX2 expression in gastruloids following WNT/NOTCH inhibition (Figure 4B, 4D, 4E) would be more compelling if the authors include supplementary videos of the time-lapse imaging.

In lines 322-324, the authors conclude that Tbxt-cells are the driving cells. Please elaborate on the interpretation that this is a cell-autonomous effect driven by TBXT levels. The observation that Sox2 levels increase ~10-15 hours after WNT/NOTCH inhibition is interesting (Figure 4D, 4E). Could the authors discuss this upregulation?

Significance

General Assessment

In the development of a novel dual Sox2/Tbxt reporter cell line, which provides a powerful tool for quantitatively understanding the dynamics of cell fate specification during gastrulation and potentially in other developmental contexts. However, a key limitation is the study's primary focus on in vitro models. The findings will require further validation in an in vivo context.

Advance

This study provides a technical advance that provides a new resource available to the field for stem cell and developmental biology.

Audience

This paper will primarily interest a specialized audience, particularly developmental and stem cell biologists who study the fundamental mechanisms of embryogenesis, cell fate specification, and axis elongation.

Field of expertise

Stem cell biology and developmental biology. I do not have the expertise to evaluate their mathematical modeling.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors generate a novel reporter mouse ESC line to track SOX2 and TBXT dynamics in neuromesodermal progenitors. The authors leverage multiple systems (in vitro differentiation, chimeric embryos and gastruloids) to address how SOX2/TBXT levels impact the contribution of neuromesodermal progenitors towards neural versus mesodermal fates. They show that the levels of TBXT can predict differentiation outcomes, whereby certain thresholds of TBXT influence the differentiation towards a mesodermal identity. In gastruloids, perturbing either WNT or NOTCH signalling coincides with diminished axial elongation. In vitro, the bias mediated by TBXT is also somewhat influenced by the substrate.

Major comments:

There are some key items to clarify that are important to resolve the interpretation of the results and clarify the main advances for a broader readership.

With respect to the mESC differentiation into NMPs (using an established protocol from Gouti et al 2014), after Day 3, cells are cultured in conditions where they are exposed to both CHIR and FGF for a further two days. As these extended CHIR/FGF conditions don't appear to be characterised by Gouti et al., 2014, what proportions and progenitors are generated in the dish under these conditions? The loss of SOX2 by day 5 suggests mesodermal progenitors are the main derivatives but further characterization (eg Meox1/Msgn1) would be needed to verify this claim.

Further validation of the generated derivatives would also be useful in the re-plating experiments (Figure 3) to test whether the double negative cells are transitioning to a mesodermal (eg Meox1/Msgn1) or neural derivative (eg Sox1/Pax6). Similarly, at day 5 and 6 of the differentiation, there appears to be a loss of Sox2 expression in some of the replated cells from the Sox2-positive population (see Figure 3D). Could the authors please clarify whether the double negative cells represent neural progenitors, and/or alternative cell types? Do the replated cells transiently adopt Tbxt? This would be possible by staining with neural (SOX1), or (pre)somitic mesoderm genes (MSGN1,MEOX1) or adjusting the text to reflect the uncertainty.

At line 172 "The cells posterior to the node expressed only TBXT." Do these cells have low SOX2 expression that is hard to detect? Are these TBXT-positive cells derived from the primitive streak? Would staining with the primitive streak marker TBX6 enable visualization of these distinct cell types, and/or could the authors please label the figure in more detail.

Could the authors please comment on the design of the reporter system in a bit more detail? For example, please clarify the necessity to generate a TBXT reporter that includes a H2B-GFP, unlike Sox2, which does not include a H2B. Can the authors distinguish between an increase in the threshold of TBXT, versus an increase detected due to the stability of the H2B-GFP? The low versus high TBXT cells may reflect early versus late TBXT expressing cells. Are the changes in TBXT expression (eg Supplementary Figure 2) significantly changed between the low versus high GFP populations? Additionally, why is the level of GFP similar across low and high GFP populations in Sup Fig 2? Could the in vivo data be used to quantify differences in TBXT (similar to what has been shown previously in Ivanovitch et al., 2021 PMID: 33999917)?

Optional

• Altering extrinsic cues (such as RA/CHIR) could clarify how reversible the high TBXT state is as cells progress towards mesoderm. Can you redirect the TBXT-high cells to a neural fate or are they already irreversibly committed?
• Line 283: Flk1 is also expressed in TBXT-low cells. It would be interesting to test whether the TBXT-low cells and the SOX2neg/TBXTpos can generate lateral plate mesoderm or whether this competence to generate lateral plate mesoderm is limited to TBXT-high cells.
• Line 324: The lack of elongation in gastruloids following the inhibition of WNT/NOTCH is clear. Do the authors expect that the reintroduction of TBXT would rescue axis elongation in the WNT/NOTCH inhibited gastruloids?

Minor comments:

Figure 3B - The SOX2+/TBXT- population only shows a moderate level of SOX1 by RT-qPCR. Using pre-neural markers (e.g. NKX1-2) might be helpful here to show progression towards a neural progenitor identity.

Line 310 - Can you comment on the general efficiency in generating elongating gastruloids compared to WT cells and/or previous literature?

Line 236 - Add "at constant SOX2 levels" (when comparing orange and yellow populations)

Figure 5

Fig5C and E take time to understand. Potentially expanding the figure legend slightly could be helpful to the reader.

Supplementary Figure 2

Line 864 - refer to Fig3A

Line 350 - The link with testing the different substrates is a bit abrupt. Please can you make it clearer by modifying the text to explain the hypothesis being tested here.

Line 363 - Could you comment in relation to what happens in the embryo to future mesoderm progenitors that seem to have a more motile phenotype compared to neural progenitors (eg Romanos et al 2021 PMID: 34607629)?

Significance

In this work, the authors have explored how the dynamics of SOX2/TBXT impact the decision process of neuromesodermal progenitors (NMPs). They have engineered and validated a novel dual fluorescent reporter ESC line to track SOX2 and TBXT. The work combines in vitro, in vivo and modelling approaches to understand how NMPs make decisions - a highly relevant and important question for multiple fields spanning developmental and quantitative biology, and the engineering of cell types in vitro from pluripotent cells. The authors propose a critically important finding: that discrete thresholds of TBXT influence the outcome of NMPs. However, further clarification is required to solidify these claims (discussed above).

The data generated from this study also suggests that in contrast to Tbxt, the level of Sox2 does not appear to impact the NMP fate decision. While these are interesting and important findings, it is not entirely clear in this version of the manuscript how these advances relate with previous studies that have highlighted critical roles mediated by Sox2 and its level of expression (including the work of Koch et al 2017 - PMID: 28826820 and Blassberg et al PMID: 35550614). We expect that a broader discussion will in turn broaden the general interest and value of the work to a wider readership.

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Referee #1

Evidence, reproducibility and clarity

The work of Binagui-Casas, Granes and colleagues, investigates in a rigorous way the origin and potential of murine NMPs. The authors first validated a dual reporter system, which monitors Sox2 and Tbxt expression. Next, they identified the location in the embryo and the sequence of gene activation (Sox2 first, then Tbxt) leading to NMPs specification. Importantly, the in vitro model faithfully mimics the in vivo ontogeny of NMPs. Among Sox2+ NMCs, the authors observed different levels of Tbxt, which they proposed mark different stages of mesoderm maturation, with high Tbxt corresponding to more mature mesodermal state. Through sorting and replating of different populations, the authors convincingly showed that Sox2+/Tbxt-low cells are still bipotent, while Sox2+/Tbxt-high are committed towards the mesoderm lineage. Using a gastruloid model, the authors then showed that Tbxt expression correlates with axis elongation, as both are reduced upon inhibition of either WNT or NOTCH Finally, single-cell sorting followed by differentiation in FGF/CHIR and high throughput microscopy confirmed that double Sox2/Tbxt positive cells behave as NMPs and that high levels of Tbxt predispose cells towards mesoderm differentiation. These conclusions were further supported by mathematical modelling. The manuscript is easy to read, and figures are very clear. I have only minor suggestions, as I find the manuscript quite solid and complete.

Minor points:

1. The reporter system is based on stable fluorescent proteins, whose half-life is generally much longer than the endogenous proteins. This could generate a discrepancy between expression of reporters and the endogenous proteins. I find this relevant for Tbxt, as it is very clear that Tbxt reporter levels dictates the differentiation propensity, but I wonder whether, Tbxt low cells actually express TBXT protein or not. It might be the case that only a fraction of Tbxt low cells actually express TBXT protein, or none. It would enough to sort the populations showed in Figure 3A and perform immunostaining for endogenous SOX2 and TBXT. This could reveal even better correlations between their levels and cell behaviour.
2. In the experiments in which IWP2 and LY411575 are used, I would suggest to asses cell viability, as the two inhibitors could induce toxicity. Staining for cleaved caspase-3 or a TUNEL assay would be enough. It would also be important to confirm that IWP2 blocks WNT signalling (by looking at WNT target genes or staining for active beta-cateinin) and that LY411575 blocks NOTCH signalling.
3. I would define in the figure legends what the black line in figure 5E represents.

Referees cross-commenting

I agree with Reviewer #2 comment about "Further validation of the generated derivatives" by staining for additional markers.

I also made a comment related to GFP stability, as Reviewer #2 did (i.e. The low versus high TBXT cells may reflect early versus late TBXT expressing cells ).

Significance

Overall, the manuscript uses an elegant approach and address an important question about NMPs behaviour. The results presented are an important advance in knowledge of NMP biology. I am confident that both stem cell and developmental biologist would be interested in this manuscript. I am an expert of pluripotency, signaling and models of early mammalian development.

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Reply to the reviewers

Manuscript number: RC-2025-03174

Corresponding author(s): Cristina, Tocchini and Susan, Mango

1. General Statements

We thank the reviewers for their thoughtful and constructive comments. We were pleased that the reviewers found our study “rigorous”, “well presented”, “technically strong”, and “novel”. We are also grateful for their recognition that our work identifies a function for a HOT region in gene regulation and provides new insights into the role of the uHOT in controlling dlg-1 expression.

Point-by-point description of the revisions

We have addressed the reviewers’ concerns by clarifying and refining the text, particularly regarding the intron 1 results, improving the quantitation and statistical analyses, and making adjustments and additions to text and figures.

Specific responses to each point are provided below in blue.

Reviewer #1

1. • The results fully support the authors conclusions regarding the significant role of the upstream HOT region ("uHOT") with strong fluorescence activity and substantial phenotypic effects (i.e., the animals have very low brood sizes and rarely progress through hatching). This data is well presented and technically well done.* Thank you.

2. In my view, their conclusions regarding the intronic HOT region are speculative and unconvincing. See below for main criticisms.*

We agree, and have made changes throughout the manuscript to make this point clearer. Specifically, we contextualize the role of intron 1 as a putative enhancer in reporter assays, but not in endogenous, physiological conditions. Some examples are:

Abstract: “(…) In contrast, the intronic region displays weak enhancer-like activity when tested in transcriptional reporter assays but is dispensable in transcriptional control when studied at the endogenous locus. Our findings reveal how HOT regions contribute to gene regulation during animal development and illustrate how regulatory potential identified in isolated contexts can be selectively deployed or buffered within the native genomic architecture.”

Background: “(…) The HOT region in the first intron possesses weak transcriptional capabilities that are restricted to epidermal cells as observed in transcriptional reporters, but seem to not be employed in physiological contexts.” As it will become clear reading this updated version of the manuscript, we cannot exclude at present a functional role during non-physiological conditions (e.g., stress)

Results and discussion: “(…) This is in contrast with what the reporter experiments showed, where intron 1 alone was permissive for transcription and slightly enhanced the FL transgene expression levels (Figure 1F,G and S4). (…)”

Other changes can be found highlighted in yellow in the manuscript.

• Furthermore, their conclusions about interactions between the two tested regions is speculative and they show no strong evidence for this claim.*

We thank the reviewer for raising this concern. To avoid overstating our conclusions, we now frame the potential interaction between the two studied HOT regions strictly in the context of previously published ARC-C data (Huang et al., 2022). We clarify in the revised text that these interactions have been observed in earlier work during larval stages (Huang et al., 2022), but remain to be validated during embryogenesis, and we present them solely as contextual information rather than as a central conclusion.

In Results and discussion section we wrote: “(…) Although the presence of a fountain at this locus remains to be confirmed during embryogenesis, Accessible Region Conformation Capture (ARC-C), a method that maps chromatin contacts anchored at accessible regulatory elements, showed that the putative HOT region interacts with other DNA sequences, including the first intron of dlg-1 (1). (…)”

* The authors claim that not all the phenotypic effects seen from deleting the uHOT region are specific to the dlg-1 gene. This is an interesting model, but the authors show essentially no data to support this or any explanation of what other gene might be regulated.*

We appreciate the reviewer’s comment and have revised the manuscript to ensure that the possibility of additional regulatory effects from the uHOT region is presented as a hypothesis rather than a claim. Our study was designed to investigate HOT-region–based transcriptional regulation rather than chromatin interactions, and we now make this scope more explicit in the text. The revised discussion highlights that, although ARC-C data suggest the uHOT region may contact other loci, the idea that these interactions contribute to the observed phenotypes remains speculative and will require dedicated future work.

In Results and discussion section we wrote: “(…) Because, as previously shown, the upstream HOT region exhibits chromatin interactions with other genomic loci (1), its depletion might affect gene expression of beyond dlg-1 alone. An intriguing hypothesis is that these phenotypes do not arise only from the reduction in dlg-1 mRNA and DLG-1 protein levels, but also from synergistic, partial loss-of-function phenotypes involving other genes (24). (…)”

* Finally, some of the hypotheses in the text could be more accurately framed by the authors. They claim HOT regions are often considered non-functional (lines 189-191). Also, they claim that correct expression levels and patterning is usually regulation by elements within a few hundred basepairs of the CDS (lines 78-80). These claims are not generally accepted in the field, despite a relatively compact genome. Notably, both claims were tested and disproven by Chen et al (2014), Genome Research, where the authors specifically showed strong transcriptional activity from 10 out of 10 HOT regions located up to 4.7 kb upstream of their nearest gene. Chen et al. 2014 is cited by Tocchini et al. and it is, therefore, surprisingly inconsistent with the claims in this manuscript.*

We thank the reviewer for this comment and have revised the text to clarify our intended meaning and avoid framing discussion points as absolute claims. We changed “often” to “frequently” in both sentences so that they better reflect general trends rather than universal rules.

The revised text now reads: “Controversially, C. elegans sequences that dictate correct expression levels and patterning are frequently located within a few hundred base-pairs (bp) (maximum around 1,000–1,500 bp) from a gene’s CDS (3,13–15),”;

And: “HOT regions in C. elegans, as well as other systems, have been predominantly associated with promoters and were frequently considered non-functional or simply reflective of accessible chromatin (25).”

Regarding the comparison to Chen et al., 2014, we note that their reporters did not include a reference baseline for “strong” transcriptional activity, and only five of the ten tested HOT regions were located more than 1.5 kb from the nearest TSS. Therefore, our phrasing is consistent with their findings while describing general trends observed in the C. elegans genome rather than absolute rules. We have also ensured that these sentences are presented as discussion points rather than definitive claims. We hope these revisions make the framing and context clearer to the reader. The fluorescence expression from the intronic HOT region is not visible by eye and the quantification shows very little expression, suggestive of background fluorescence. Although the authors show statistical significance in Figure 1G, I would argue this is possibly based on inappropriate comparisons and/or a wrong choice statistical test. The fluorescence levels should be compared to a non-transgenic animal and/or to a transgenic animal with the tested region shuffled but in an equivalent

We understand the reviewer’s concern regarding the low fluorescence levels observed for the intronic HOT reporter. To address this, we have now included a Figure S4 with higher-exposure versions of the embryos shown in Figure 1. These panels confirm that the nuclear signal is genuine: embryos without a functional transcriptional transgene do not display any comparable fluorescence, aside from the characteristic cytoplasmic granules associated with embryonic autofluorescence. Similar reference images have also been added to Figure S3 to clarify the appearance of autofluorescence under the same imaging conditions.

Regarding the quantitation analyses, as suggested by the reviewers, we now consistently quantify fluorescence by calculating the mean intensity for each embryo (biological replicates) and performing statistical analyses on these values. This approach ensures that the statistical tests are applied to independent biological measurements.

* I would suggest the authors remove their claims about the intronic enhancer and the interaction between the two regions. And I would suggest softening the claims about the uHOT regulation of another putatitive gene.*

We have revised the manuscript to avoid definitive claims regarding the presence of an interaction between the two studied HOT regions. These points are now presented strictly as hypotheses within the discussion, suggested by previously published ARC-C data rather than by our own experimental evidence. Likewise, we have softened our statements regarding the possibility that the uHOT region may regulate additional gene(s). This idea is now framed as a speculative model that will require dedicated future studies, rather than as a conclusion of the present work. Quotes can be found in the previous points (#3 and #4) raised by Reviewer 1.

* The authors would need to demonstrate several things to support their current claims. The major experiments necessary are:*

1. • Insert single-copy transgene with a minimal promoter and the intronic sequence scrambled to generate a proper baseline control. It is very possible that the intronic sequence does drive some expression, but the current control is not appropriate for statistical comparison (e.g., only the transgene with intron 1 contains the minimal promoter from pes-10, which may have baseline transcriptional activity even without the intron placed in front of the transgene).* We thank the reviewer for this suggestion. We agree that a scrambled-sequence control can be informative in some contexts; however, in this case we believe the existing data already address the concern. In our dataset, all uHOT reporter constructs—each containing the same minimal promoter—show consistent background levels in the absence of regulatory input, providing an internal baseline for comparison. For this reason, we consider the current controls sufficient to interpret the effects of the intronic region in reporter assays.

In general, the minimal Δpes-10 promoter is specifically designed to have negligible basal transcriptional activity on its own, and this property has been extensively validated in previous studies (reference included in the revised manuscript).

* It is not very clear why the authors did not test intron 1 within the H2B of the transgene and just the minimal promoter in front of the transgene, but only in the context of the full-length promoter. The authors show a minor difference in expression levels for the full-length (FL) and full-length with intron 1 (FL-INT1) but show a large statistical differnce. The authors use an inappropriate statistical test (T-test) for this experiment and treat many datapoints from the same embryo as independent, which is clearly not the case. Even minor differences in staging, transgene silencing in early development, or variability would potentially bias their data collection.*

We thank the reviewer for this comment. Our goal was to assess the potential contribution of intron 1 in two complementary contexts: (i) on its own, upstream of a minimal promoter, to test whether it can in principle support transcription, and (ii) within the full-length promoter construct, which more closely reflects the endogenous configuration. For this reason, we did not generate an additional construct placing intron 1 within the H2B reporter driven only by the minimal promoter, as we considered this redundant with the information provided by the existing INT1 and FL-INT1 reporters.

Regarding the statistical analysis, we agree that treating multiple measurements from the same embryo as independent is not appropriate. In the revised manuscript, we now use the mean fluorescence intensity per embryo as a single biological replicate and perform all statistical tests on these independent values. This approach avoids pseudo-replication and ensures that the analysis is robust to variability in staging or transgene behavior. The conclusions remain the same.

* The authors claim, based on ARC-C data previously published by their lab (Huang et al. 2022) that the dlg-1 HOT region interacts with "other" genomic regions. This is potentially interesting but the evidence for this should be included in the manuscript itself, perhaps by re-analyzing data from the 2022 manuscript?*

We thank the reviewer for this suggestion. The chromatin-interaction data referred to in the manuscript originate from the work of Huang et al., 2022, published by the Ahringer lab. As these ARC-C datasets are already publicly available and thoroughly analyzed in the original publication, we felt that reproducing them in our manuscript was not necessary for supporting the limited contextual point we make. Our intent is simply to note that previous work reported contacts between the uHOT region and additional loci. To address the reviewer’s concern, we have revised the manuscript to make clear that we are referencing previously published ARC-C observations and that we do not present these interactions as new findings from our study.

For example, in Results and discussion section we wrote: “(…) Because, as previously shown, the upstream HOT region exhibits chromatin interactions with other genomic loci (1), its depletion might affect gene expression beyond dlg-1 alone. An intriguing hypothesis is that these phenotypes do not arise only from the reduction in dlg-1 mRNA and DLG-1 protein levels, but also from a synergistic, partial loss-of-function phenotypes involving other genes (24). (…)”

* The fluorescence quantification is difficult to interpret from the attached data file (Table S1). For the invidividual values, it is unclear how many indpendent experiments (different embryos) were conducted. The authors should clarify if every data value is from an independent embryo or if they used several values from the same embryo. If they did use several values from the same embryo, how did they do this? Did they take very cell? Or did they focus on specific cells? How did they ensure embryo staging?*

We thank the reviewer for pointing this out. To clarify the quantification procedure, we have expanded the description in the Methods section (“Live imaging: microscopy, quantitation, and analysis”). The revised text now specifies that each data point represents the normalized fluorescence value obtained from three nuclei (or five junctions, depending on the construct), all taken from the same anatomical positions across embryos. Two independent biological replicates were performed for each experiment, with each embryo contributing a single averaged value.

As noted in the figure legends, the specific nuclei used for quantification are indicated in each panel (with dashed outlines), and a reference nucleus marked with an asterisk allows unambiguous identification of the same positions across all conditions. We are happy to further refine this description if additional clarification is needed.

* The authors also do not describe how they validated single-copy insertions (partial transgene deletions in integrants are not infrequent and they only appear to use a single insertion for each strain). This should be described and or added as a caveat if no validation was performed.*

The authors also do not describe any validation for the CRISPR alleles, either deletions or insertion of the synthetic intron into dlg-1. How were accurate gene edits verified.

We thank the reviewer for highlighting the importance of validating the genetic constructs. We have now clarified this more explicitly in the revised Methods section and in Table S1. All single-copy transgene insertions and all CRISPR-generated alleles were verified by genotyping and Sanger sequencing to confirm correct integration and the absence of unintended rearrangements.

• *

I am not convinced the statistical analysis of the fluorescence data is correct. Unless the authors show that every datapoint in the fluorescence quantification is independent, then I would argue they vastly overestimate the statistical significance. Even small differences are shown to have "***" levels of significance, which does not appear empirically plausible.

We thank the reviewer for highlighting this point. To ensure that each data point represents an independent measurement, we now calculate the mean fluorescence per embryo (from three nuclei or five junctions) and use these per-embryo means as biological replicates for statistical testing. Two independent experiments were performed for each condition. Statistical differences were evaluated using a one-tailed t-test on the per-embryo means, as indicated in the revised Methods section.

After this adjustment, the differences remain statistically significant, although less extreme than in the initial analysis (now p * *

This study is so closely related to the Chen et al study, that I believe this study should be discussed in more detail to put the data into context.

We thank the reviewer for this suggestion. While we refer to Chen et al., 2014 as a relevant prior study for context, we believe that our work addresses distinct questions and experimental approaches. Specifically, our study focuses on HOT region-based transcriptional regulation in the dlg-1 locus and its functional dissection in vivo, which is conceptually and methodologically different from the scope of Chen et al., 2014 where the author tested the functionality of HOT region-containing promoters in the context of single-copy integrated transcriptional reporters. We hope this is clearer to the reader in the revised manuscript.

* Add H2B to the mNG in Figure 1 in order to understand where the first intron was inserted.*

We thank the reviewer for this suggestion. A schematic representation of the transgene is already provided above the corresponding images to indicate the location of the first intron.

For additional clarity, we have now added the following sentence in the main text: “In the other, intron 1 was inserted in the FL transgene within the H2B coding sequence (at position 25 from the ATG), preserving the canonical splice junctions with AG at the end of the first exon and a G at the beginning of the second exon, so that it acted as a bona fide intron (FL-INT1) (Figure 1F).”

This should help readers understand the placement of the intron without requiring modifications to the figure itself.__ __

Reviewer #2

1) The authors suggest that the region upstream of the dlg-1 gene is a HOT region. Although they highlight that other broad studies pick up this region as a HOT region, it would be good that the authors dive into the HOT identity of the region and characterize it, as it is a major part of their study. In addition to multiple TFs binding to the site, there are different criteria by which a region would be considered a HOT region. E.g. is there increased signal on this region in the IgG ChIP-seq tracks? Is the area CpG dense?

We thank the reviewer for this suggestion. In the manuscript and Figure S1, we show several features of HOT regions, including transcription factor binding and chromatin marks. To further characterize the dlg-1 uHOT region, we have added the following sentence to the text: “The conserved region is positioned approximately four Kb from the CDS of dlg-1 in a CpG-dense sequence (2), and is overlapping and bordered by chromatin marks typically found in enhancers (5,16).”

This addition provides additional evidence supporting the identity of the region as a HOT region, complementing the features already presented.

* 2) When describing the HOT region, they refer to Pol II binding as 'confirming its role as a promoter': non-promoter regions can also have Pol II binding, especially enhancers. Having binding of Pol II does not confirm its role as promoter. On the contrary, seeing the K27ac and K4me1 would point towards it being an enhancer.*

The sentence has been revised to clarify the interpretation of Pol II binding: “This HOT site also contains RNA Pol II peaks during embryogenesis (Figure S1C), supporting its role as a promoter or enhancer (9).” This wording avoids overinterpreting Pol II binding alone, while acknowledging that the HOT region may have both promoter and enhancer characteristics.

We would like to note that the relevant chromatin marks (H3K27ac and H3K4me1), which are indicative of enhancer activity, are described in the text: “(…) Specifically, it is enriched in acetylated lysine 27 (H3K27ac) and mono- and di-methylated lysine 4 of histone H3 (H3K4me1/2), and depleted from tri-methylated lysine 4 of histone H3 (H3K4me3) (Figure S1D) (5,16). (…)”

These changes clarify that the HOT region may have enhancer characteristics and avoid overinterpreting the Pol II signal.

* 3) In S1B, the authors show TF binding tracks. They also have a diagram of the region subsets (HOT1-4) that were later tested. What is their criteria for dividing the HOT region into those fragments? From looking at Fig S1, the 'proper' HOT region (ie. Where protein binding occurs) seems to be divided into two (one chunk as part of HOT3 and one chunk as part of HOT4). Can the authors comment on the effects of this division?*

To clarify the criteria for dividing the HOT region into subregions, we have added the following sentence to the main text: “The subregions were chosen taking into account (i) enrichment of putative TF binding sites (uHOT1 for PHA-4, uHOT2 for YAP-1 and NHR-25, uHOT3 for ELT-3, and uHOT4 for PHA-4 and others (e.g., ELT-1 and ELT-3)), (ii) Pol II binding peaks, and (iii) histone modification peaks (Fig. S1C,D).”

This description explains the rationale behind the division and clarifies why the HOT region was split into these four fragments for functional testing.

* 4) For the reporter experiments, the first experiments carry the histone H2B sequence and the second set of experiments (where the HOT region is dissected) carry a minimal promoter Δ*pes-10 (MINp). The results could be affected by the addition of these sequences. Is there a reason for this difference? Can the authors please justify it?

The difference in reporter design reflects the distinct goals of the two sets of experiments. The H2B sequence, coupled to mNG, is used as a coding sequence throughout the first part of the study (reporter analysis). This is commonly used to (i) concentrate the fluorescence signal (mNG) into nuclei (H2B) and (ii) be able to identify specific cells more accurately for quantitation reasons (intensity and consistency). The Δpes-10 promoter is instead used to analyze whether specific sequences possess enhancer potential: this promoter alone possesses the sequences that can allow transcription only in the presence of transcription factors that bind to the studied sequence placed upstream it.

To clarify this distinction in the manuscript, we have added the following sentence: “(…) Each region was paired with the minimal promoter Δpes-10 (MINp) (Figure 1D) and generated four transcriptional reporters. Δpes-10 is commonly used to generate transcriptional reporter aimed at assessing candidate regulatory enhancer sequences (20). The minimal promoter drives expression only when transcription factors bind to the tested upstream sequence and test enhancer activity. (…)”

5) Regarding the H2B sequence: ' 137: first intron [...] inserted in the FL transgene within the H2B sequence, acting as an actual intron (FL-INT1)': how was the location of the insertion chosen? Does it disrupt H2B? can it be that the H2B sequence contributed to dampening down the expression of mNG and disrupting it makes it stronger? It would be important to run the first experiments with minimal promoters and not with the H2B sequence.

The location of the intron insertion within the H2B coding sequence was chosen to preserve proper splicing and avoid disrupting H2B protein. We added the following sentence to clarify this point: “(…) In the other, the intron was inserted in the FL transgene within the H2B coding sequence (at position 25 from the ATG), preserving the canonical splice junctions with AG at the end of the first exon and a G at the beginning of the second exon, so that it acted as a bona fide intron (FL-INT1) (Figure 1F). (…)”

* 6) Have the authors explored the features of the sequences underlying the different HOT subregions? (e.g. running a motif enrichment analysis)? Is there anything special about HOT3 that could make it a functional region? It would be good to compare uHOT3 vs the others that do not drive the correct pattern. Since it's a HOT region, it may not have a special feature, but it is important to look into it.*

We thank the reviewer for this suggestion. To clarify the rationale for dividing the HOT region into four subregions, we have added the following sentence to the main text: “(…) The subregions were chosen taking into account (i) enrichment of putative TF binding sites (uHOT1 for PHA-4, uHOT2 for YAP-1 and NHR-25, uHOT3 for ELT-3, and uHOT4 for PHA-4 and others (e.g., ELT-1 and ELT-3)), (ii) Pol II binding peaks, and (iii) histone modification peaks (Fig. S1C,D). (…)”

While uHOT3 does not appear to possess unique sequence features beyond these general HOT-region characteristics, this approach allowed us to systematically test which fragments contribute to transcriptional activity and patterning.

7) For comparisons, the authors run t-tests. Is the data parametric? Otherwise, it would be more suitable to use a non-parametric test.

To ensure that each data point represents an independent biological replicate, we now calculate the mean fluorescence intensity per embryo and perform statistical tests on these per-embryo means. The data meet the assumptions of parametric tests, and we use a one-tailed t-test as indicated in the Methods.

* 1) The authors work with C. elegans embryos at comma stage, according to the methods section. It would be good if the authors mentioned it in the main text so that the reader is informed.*

Thanks for this suggestion. We added this sentence in the main text: “(…) Live imaging and quantitation analyses on embryos at the comma stage (used throughout the study for consistency purposes) showed (…)”.

* 2) 'Notably, the upstream HOT region is located more than four kilo-bases (Kb) away the CDS, and the one in the first intron contains enhancer sites, too.': what do they mean by 'enhance sites, too'. Is the region known as a functional enhancer? If so, could you please provide the reference?*

Here the clarification from the revised text: “(…) Notably, the upstream HOT region is located more than four kilo-bases (Kb) away the CDS, and the one in the first intron does not only contain two TSS but also three enhancer sites (8). (…)”

* 3) 'We hypothesized the upstream HOT region is the main driver of dlg-1 transcriptional regulation.': this sentence needs more reasoning. What led to this hypothesis? Is it the fact of seeing multiple TFs binding there? The chromatin marks?*

The reasoning behind the hypothesis is described in the preceding paragraph, and to make this connection clearer, we have revised the sentence to begin with: “Considering all of this information, we hypothesized the upstream HOT region is the main driver of dlg-1 transcriptional regulation. (…)”.

This change explicitly links the hypothesis to the observed TF binding and chromatin marks described above.

* 4) The labels of S1B are too wide, as if they have stretched the image. Could the authors please correct this?*

Yes, we agree with Reviewer 2. We corrected this.

* 5) This sentence does not flow with the rest of the text '84 - cohesins have been shown to organize the DNA in a way that active enhancers make contacts in the 3D space forming "fountains" detectable in Hi-C data (17,18).': is there a reason to explain this? I would remove it if not, as it can confuse the reader.*

We thank the reviewer for this comment. We agree that the sentence could potentially interrupt the flow; however, it is important for introducing the concept of “fountains” in 3D genome organization, which is necessary to understand the subsequent statement: “(…) Although the presence of a fountain at this locus remains to be confirmed during embryogenesis, Accessible Region Conformation Capture (ARC-C), a method that maps chromatin contacts anchored at accessible regulatory elements, showed that the putative HOT region interacts with other DNA sequences, including the first intron of dlg-1 (1). (…)”.

Therefore, we have retained this sentence to provide the necessary background for readers.

* 6) The authors mentioned that 'ARC-C data showed the putative HOT region interacts with other DNA sequences, including the first intron of dlg': have the authors analysed the data from the previous paper? A figure with the relevant data could illustrate this interaction so that the reader knows which specific region has been shown to interact with which. This would also bring clarity as to why they chose intron1 for additional experiments.*

We thank the reviewer for this suggestion. We have examined the relevant ARC-C data from the previous publication (Huang et al., 2022). However, as these results are already published, we do not feel it is necessary to reproduce them in our manuscript. The mentioning of these interactions is intended only to introduce the concept for discussion and to provide context for why intron 1 was considered in subsequent experiments

* 7) 'two deletion sequences spanning from the beginning (uHOT) or the end (Short) of the HOT region until the dlg-1 CDS': From the diagrams of the figure, I understand that uHOT has the distal region deleted, and the short HOT has the distal and the upstream regions deleted. Is this correct? Could you clarify this in the text? E.g. 'we designed two reporters - one containing the sequence starting at the HOT region and ending at the dlg-1 CDS, and the other without the HOT region, but rather starting downstream of it until the dlg-1 CDS'.*

To clarify the design of the reporters, we have revised the text as follows: “(…) To test this idea, we generated three single-copy, integrated transcriptional reporters carrying a histone H2B sequence fused to an mNeon-Green (mNG) fluorescent protein sequence under the transcriptional control of the following dlg-1 upstream regions: (i) a full-length sequence (“FL” = Distal + uHOT + Proximal sequences), (ii) one spanning from the beginning of the HOT region to the dlg-1 CDS (“uHOT” = uHOT + Proximal sequences), and (iii) one starting at the end of the HOT region and ending at the dlg-1 CDS (“Short” = Proximal sequence) (Figure 1A-C). (…)”

This description clarifies which parts of the upstream region are included in each reporter and matches the schematics in Figure 1.

* 8) 'Specifically, it spanned from bp 5,475,070 to 5,475,709 on chromosome X and removed HOT2 and HOT2 sequences' - this is unclear to me. What sequences are removed? HOT2 and 3?*

Thanks for spotting this typo. It has now been corrected.

* 9) 'ARC-C' is not introduced. Please spell out what this is. Accessible Region Conformation Capture (ARC-C). It would be helpful to include a sentence of what it is, as it will not be known by many readers.*

You are right, we changed into: “(…) Although the presence of a fountain at this locus remains to be confirmed during embryogenesis, Accessible Region Conformation Capture (ARC-C), a method that maps chromatin contacts anchored at accessible regulatory elements, showed that the putative HOT region interacts with other DNA sequences, including the first intron of dlg-1 (1). (...)”

* 10) Fig 1 B, diagram on the right: the H2B sequence is missing. I see that is indicated in the legend as part of mNG but this can be misleading. Could the authors add it to the diagram for clarification?*

Yes, you are right. We added this in the figure.__ __

Reviewer #3

The authors' claims are generally supported by the data, thoug the last sentence of the abstract was a bit overstated. They state that they "reveal the function of HOT regions in animals development...."; it would be more accurate to state that they linked the role of an upstream HOT region to dlg-1 regulation, and their findings hint that this element could have additional regulatory functions. The authors can either temper their conclusions or try RNA-seq experiments to find additional genes that are misregulated by the delta-uHOT deletion allele. [OPTIONAL]. Another [OPTIONAL] experiment that would strengthen the claims is to perform RNAi knockdown or DLG-1 protein depletion and link that to phenotype to show that the dlg-1 mRNA and DLG-1 protein changes seen in the uHOT mutant do not explain the lethality observed.

We thank the reviewer for this comment. We have studied HOT region function in the context of a model organism, C. elegans; therefore, we believe that describing our findings as revealing a function of HOT regions in animal development is accurate. The sentence aims at noting that these observations may provide broader insights into HOT region regulation. We changed the last sentence of the abstract into: “(…) Our findings reveal how HOT regions contribute to gene regulation during animal development and illustrate how regulatory potential identified in isolated contexts can be selectively deployed or buffered within the native genomic architecture. (…)”.

We note that RNA-seq is beyond the scope of this study; our discussion of potential effects on other genes is intended only as a hypothesis for future work. RNAi of dlg-1 has been previously reported and is cited in the manuscript, providing context for the phenotypes observed and discussed.

1. * When printed out I cannot read what the tracks are in Fig S1. Adding larger text to indicate what those tracks are is necessary.* Yes, you are right. We changed this in the figure.

2. *

3. Line 79. I would change the word "usually" to "frequently" in the discussion about regulatory element position. While promoters ranging from a few hundred to 2000 basepairs are frequently used, there are numerous examples where important enhancers can be further away.*

Corrected.

* Line 93-95. The description of the reporters was very confusing. When referring to the deletion sequences it sounds like that is what is missing rather than what is included. Rather, if I understand correctly the uHOT is the sequence from the start of the uHOT to the CDS and Short starts at the end of uHOT (omitting it). Adding the promoter fragments to the figure would improve clarity.*

To clarify the design of the reporters, we have revised the text as follows: “(…) To test this idea, we generated three single-copy, integrated transcriptional reporters carrying a histone H2B sequence fused to an mNeon-Green (mNG) fluorescent protein sequence under the transcriptional control of the following dlg-1 upstream regions: (i) a full-length sequence (“FL” = Distal + uHOT + Proximal sequences), (ii) one spanning from the beginning of the HOT region to the dlg-1 CDS (“uHOT” = uHOT + Proximal sequences), and (iii) one starting at the end of the HOT region and ending at the dlg-1 CDS (“Short” = Proximal sequence) (Figure 1A-C). (…)”

This description clarifies which parts of the upstream region are included in each reporter and matches the schematics in Figure 1.

* Line 108. Re-work the phrase "increase majorly". Majorly increase would be better.*

We thank the reviewer for this suggestion. The verb is used here as an infinitive (“to increase majorly”), and in standard English the infinitive is usually not split. Therefore, we have kept the phrasing as it currently appears in the manuscript.

* Line 153-154. The deletion indicates that HOT2 and HOT2 were removed. Was one supposed to be HOT3?*

Thanks for spotting this typo. It has now been corrected.

* In the figure legends the number of animals scored and the number of biological repeats is missing.*

Added.

* Figure 1 title in the legend. Should read "main driver" not "man driver".*

Thanks for spotting this typo. It has now been corrected.

* The references need to be gone through carefully and cleaned up. There are numerous gene and species names that are not italicized. There are also extra elements added by the reference manager such as [Internet].*

Thanks for pointing it out. We used Zotero and the requested formatting from the journal of our choice. We will discuss with their team how to go through this issue.

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Referee #3

Evidence, reproducibility and clarity

High occupancy target (HOT) regions are genomic sequences in C. elegans that are bound by large numbers of transcription factors and emerged from systematic ChIP-seq studies. Whether they play physiologically important roles in gene regulation is not clear. in In this manuscript, Tocchini et al. examine the function of two HOT regions using a combination of promoter reporters, genome editing, and smFISH. One HOT region is upstream of the dlg-1 gene and other is in the first intron of dlg-1.

The claims about the impact of the upstream HOT region on dlg-1 expression are convincing. Omitting the sequence in a promoter reporter reduces expression, the element is sufficient to drive expression from a MINp::mNG reporter, and deletion of the element reduces dlg-1 expression and causes developmental defects. The claims about the intronic HOT region need to be tempered slightly. The element drives weak expression in a MINp::mNG reporter but the replacement of the dlg-1 first intron with a syntron had no effect on expression, limiting the claims that be made about this regulatory element. The authors' claims are generally supported by the data, thoug the last sentence of the abstract was a bit overstated. They state that they "reveal the function of HOT regions in animals development...."; it would be more accurate to state that they linked the role of an upstream HOT region to dlg-1 regulation, and their findings hint that this element could have additional regulatory functions. The authors can either temper their conclusions or try RNA-seq experiments to find additional genes that are misregulated by the delta-uHOT deletion allele. [OPTIONAL]. Another [OPTIONAL] experiment that would strengthen the claims is to perform RNAi knockdown or DLG-1 protein depletion and link that to phenotype to show that the dlg-1 mRNA and DLG-1 protein changes seen in the uHOT mutant do not explain the lethality observed.

There are elements of the manuscript that must be improved for clarity/accuracy.

1. When printed out I cannot read what the tracks are in Fig S1. Adding larger text to indicate what those tracks are is necessary.
2. Line 79. I would change the word "usually" to "frequently" in the discussion about regulatory element position. While promoters ranging from a few hundred to 2000 basepairs are frequently used, there are numerous examples where important enhancers can be further away.
3. Line 93-95. The description of the reporters was very confusing. When referring to the deletion sequences it sounds like that is what is missing rather than what is included. Rather, if I understand correctly the uHOT is the sequence from the start of the uHOT to the CDS and Short starts at the end of uHOT (omitting it). Adding the promoter fragments to the figure would improve clarity.
4. Line 108. Re-work the phrase "increase majorly". Majorly increase would be better.
5. Line 153-154. The deletion indicates that HOT2 and HOT2 were removed. Was one supposed to be HOT3?
6. In the figure legends the number of animals scored and the number of biological repeats is missing.
7. Figure 1 title in the legend. Should read "main driver" not "man driver",
8. The references need to be gone through carefully and cleaned up. There are numerous gene and species names that are not italicized. There are also extra elements added by the reference manager such as [Internet].

Referee cross-commenting

I agree with the comments from the previous reviewers. The suggested experiments are reasonable. Reviewer 1's point about the Chen et al 2014 Genome Res paper is really important. I put the revision as unknown as it depended on whether they did the optional experiments I suggested. If they revise their text, tempering claims, adjusting statistical analyses, then that could be 1-3 months. If they did the RNA-seq that I suggested, that would be a longer timeline.

Significance

The study is generally rigorously done. Strengths are that this work finds a function for a HOT region in gene regulation. Limitations are that the work is currently very thorough regulatory element bashing. They convincingly demonstrate the role of uHOT in regulating dlg-1 and suggest that the reduction of DLG-1 levels does not explain the phenotype. This finding is of interest to basic researchers in gene regulation. Without going into that discrepancy more, the significance is limited. Linking HOT regions to novel regulatory mechanisms controlling multiple genes would be broadly interesting to the gene regulation and developmental biology.

I am a C. elegans molecular biologist with expertise in gene regulatory networks.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors investigate the functionality of a HOT region located upstream of the dlg-1 gene in Caenorhabditis elegans. This region is bound by multiple proteins and enriched for H3K27ac and H3K4me1, features characteristic of enhancers. Using reporter assays, they dissect the region and identify a sub-fragment, HOT3, as responsible for driving gene expression in epidermis, with a pattern similar to that of dlg-1 itself. Deletion of this region leads to downregulation of dlg-1 and lethality before or shortly after hatching, in contrast to complete dlg-1 knockouts, which die at mid-embryogenesis. They further examine the role of the gene's first intron, previously reported to physically interact with the HOT region. Incorporating intron 1 into the reporter construct slightly increases expression, suggesting an additive regulatory effect. However, replacing intron 1 with a synthetic sequence at the endogenous locus does not cause major changes. Overall, this study demonstrates that HOT regions can play a functional role in gene regulation, challenging the prevailing view that they are largely non-functional.

Major comments:

Overall, the paper lacks to explain their reasoning on choosing certain conditions and it also lacks on discussions on relevant topics, highlighted below.

1) The authors suggest that the region upstream of the dlg-1 gene is a HOT region. Although they highlight that other broad studies pick up this region as a HOT region, it would be good that the authors dive into the HOT identity of the region and characterize it, as it is a major part of their study. In addition to multiple TFs binding to the site, there are different criteria by which a region would be considered a HOT region. E.g. is there increased signal on this region in the IgG ChIP-seq tracks? Is the area CpG dense?

2) When describing the HOT region, they refer to Pol II binding as 'confirming its role as a promoter': non-promoter regions can also have Pol II binding, especially enhancers. Having binding of Pol II does not confirm its role as promoter. On the contrary, seeing the K27ac and K4me1 would point towards it being an enhancer.

3) In S1B, the authors show TF binding tracks. They also have a diagram of the region subsets (HOT1-4) that were later tested. What is their criteria for dividing the HOT region into those fragments? From looking at Fig S1, the 'proper' HOT region (ie. Where protein binding occurs) seems to be divided into two (one chunk as part of HOT3 and one chunk as part of HOT4). Can the authors comment on the effects of this division?

4) For the reporter experiments, the first experiments carry the histone H2B sequence and the second set of experiments (where the HOT region is dissected) carry a minimal promoter Δpes-10 (MINp). The results could be affected by the addition of these sequences. Is there a reason for this difference? Can the authors please justify it?

5) Regarding the H2B sequence: ' 137: first intron [...] inserted in the FL transgene within the H2B sequence, acting as an actual intron (FL-INT1)': how was the location of the insertion chosen? Does it disrupt H2B? can it be that the H2B sequence contributed to dampening down the expression of mNG and disrupting it makes it stronger? It would be important to run the first experiments with minimal promoters and not with the H2B sequence.

6) Have the authors explored the features of the sequences underlying the different HOT subregions? (e.g. running a motif enrichment analysis)? Is there anything special about HOT3 that could make it a functional region? It would be good to compare uHOT3 vs the others that do not drive the correct pattern. Since it's a HOT region, it may not have a special feature, but it is important to look into it.

7) For comparisons, the authors run t-tests. Is the data parametric? Otherwise, it would be more suitable to use a non-parametric test.

Minor comments:

1) The authors work with C. elegans embryos at comma stage, according to the methods section. It would be good if the authors mentioned it in the main text so that the reader is informed.

2) 'Notably, the upstream HOT region is located more than four kilo-bases (Kb) away the CDS, and the one in the first intron contains enhancer sites, too.': what do they mean by 'enhance sites, too'. Is the region known as a functional enhancer? If so, could you please provide the reference?

3) 'We hypothesized the upstream HOT region is the main driver of dlg-1 transcriptional regulation.': this sentence needs more reasoning. What led to this hypothesis? Is it the fact of seeing multiple TFs binding there? The chromatin marks?

4) The labels of S1B are too wide, as if they have stretched the image. Could the authors please correct this?

5) This sentence does not flow with the rest of the text '84 - cohesins have been shown to organize the DNA in a way that active enhancers make contacts in the 3D space forming "fountains" detectable in Hi-C data (17,18).': is there a reason to explain this? I would remove it if not, as it can confuse the reader.

6) The authors mentioned that 'ARC-C data showed the putative HOT region interacts with other DNA sequences, including the first intron of dlg': have the authors analysed the data from the previous paper? A figure with the relevant data could illustrate this interaction so that the reader knows which specific region has been shown to interact with which. This would also bring clarity as to why they chose intron1 for additional experiments.

7) 'two deletion sequences spanning from the beginning (uHOT) or the end (Short) of the HOT region until the dlg-1 CDS': From the diagrams of the figure, I understand that uHOT has the distal region deleted, and the short HOT has the distal and the upstream regions deleted. Is this correct? Could you clarify this in the text? E.g. 'we designed two reporters - one containing the sequence starting at the HOT region and ending at the dlg-1 CDS, and the other without the HOT region, but rather starting downstream of it until the dlg-1 CDS'.

8) 'Specifically, it spanned from bp 5,475,070 to 5,475,709 on chromosome X and removed HOT2 and HOT2 sequences' - this is unclear to me. What sequences are removed? HOT2 and 3?

9) 'ARC-C' is not introduced. Please spell out what this is. Accessible Region Conformation Capture (ARC-C). It would be helpful to include a sentence of what it is, as it will not be known by many readers.

10) Fig 1 B, diagram on the right: the H2B sequence is missing. I see that is indicated in the legend as part of mNG but this can be misleading. Could the authors add it to the diagram for clarification?

Significance

HOT regions are thought to be artifacts from ChIP-seq experiments. This study provides evidence that at least some HOT regions can have a functional role in gene regulation, emphasizing that they should not be dismissed outright.

The findings will be of interest to researchers investigating the biological nature of HOT regions, as well as to those who have encountered HOT regions in their own sequencing datasets. In addition, researchers studying the regulation of dlg-1 in C. elegans may find this work particularly relevant. I work on gene regulation during embryonic development and my technical expertise is omics and fluorescence microscopy. Since I do not work in C. elegans, I cannot evaluate if the patterns/location of the signal is where they claim it to be, I do not know if the cells marked are epidermal cells.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

In this manuscript, Tocchini et al. characterize two enhancer regions, one distal and one intronic, of the gene dlg-1 in C. elegans. The two enhancers are termed high-occupancy target (HOT) regions as defined by their binding of most transcription factors, as identified by the modENCODE project. The authors test transcriptional activity of the two HOT regions using single-copy transgene assays and assay their functional relevance by deleting the regions using CRISPR/Cas9 genome editing. The authors observe robust transcriptional activity and functional effects of the distal regulatory element and little evidence for enhancer activity from the intronic enhancer. From these assays, the authors conclude that the distal and intronic enhancers coordinate to fine tune gene expression in a cell-type specific manner.

Major comments:

• Are the key conclusions convincing?

• The results fully support the authors conclusions regarding the significant role of the upstream HOT region ("uHOT") with strong fluorescence activity and substantial phenotypic effects (i.e., the animals have very low brood sizes and rarely progress through hatching). This data is well presented and technically well done.

• In my view, their conclusions regarding the intronic HOT region are speculative and unconvincing. See below for main criticisms.
• Furthermore, their conclusions about interactions between the two tested regions is speculative and they show no strong evidence for this claim.
• The authors claim that not all the phenotypic effects seen from deleting the uHOT region are specific to the dlg-1 gene. This is an interesting model, but the authors show essentially no data to support this or any explanation of what other gene might be regulated.
• Finally, some of the hypotheses in the text could be more accurately framed by the authors. They claim HOT regions are often considered non-functional (lines 189-191). Also, they claim that correct expression levels and patterning is usually regulation by elements within a few hundred basepairs of the CDS (lines 78-80). These claims are not generally accepted in the field, despite a relatively compact genome. Notably, both claims were tested and disproven by Chen et al (2014), Genome Research, where the authors specifically showed strong transcriptional activity from 10 out of 10 HOT regions located up to 4.7 kb upstream of their nearest gene. Chen et al. 2014 is cited by Tocchini et al. and it is, therefore, surprisingly inconsistent with the claims in this manuscript.

The fluorescence expression from the intronic HOT region is not visible by eye and the quantification shows very little expression, suggestive of background fluorescence. Although the authors show statistical significance in Figure 1G, I would argue this is possibly based on inappropriate comparisons and/or a wrong choice statistical test. The fluorescence levels should be compared to a non-transgenic animal and/or to a transgenic animal with the tested region shuffled but in an equivalent - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

Yes, I would suggest the authors remove their claims about the intronic enhancer and the interaction between the two regions. And I would suggest softening the claims about the uHOT regulation of another putatitive gene. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Yes, the authors would need to demonstrate several things to support their current claims. The major experiments necessary are:

1. Insert single-copy transgene with a minimal promoter and the intronic sequence scrambled to generate a proper baseline control. It is very possible that the intronic sequence does drive some expression, but the current control is not appropriate for statistical comparison (e.g., only the transgene with intron 1 contains the minimal promoter from pes-10, which may have baseline transcriptional activity even without the intron placed in front of the transgene).
2. It is not very clear why the authors did not test intron 1 within the H2B of the transgene and just the minimal promoter in front of the transgene, but only in the context of the full-length promoter. The authors show a minor difference in expression levels for the full-length (FL) and full-length with intron 1 (FL-INT1) but show a large statistical differnce. The authors use an inappropriate statistical test (T-test) for this experiment and treat many datapoints from the same embryo as independent, which is clearly not the case. Even minor differences in staging, transgene silencing in early development, or variability would potentially bias their data collection.
3. The authors claim, based on ARC-C data previously published by their lab (Huang et al. 2022) that the dlg-1 HOT region interacts with "other" genomic regions. This is potentially interesting but the evidence for this should be included in the manuscript itself, perhaps by re-analyzing data from the 2022 manuscript?
4. Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

These experiments are not costly (two transgenes inserted by single-copy transgenesis) nor particularly time-consuming. With cloning, injection, and microscopy, these experiments can be conducted in 6 weeks with relatively few "hands on" hours. The cost should be very reasonably (reagents surely less than €500). - Are the data and the methods presented in such a way that they can be reproduced?

The data are not entirely clear and could benefit from additional details. This is a partial list but shows the general concern.

The fluorescence quantification is difficult to interpret from the attached data file (Table S1). For the invidividual values, it is unclear how many indpendent experiments (different embryos) were conducted. The authors should clarify if every data value is from an independent embryo or if they used several values from the same embryo. If they did use several values from the same embryo, how did they do this? Did they take very cell? Or did they focus on specific cells? How did they ensure embryo staging?

The authors also do not describe how they validated single-copy insertions (partial transgene deletions in integrants are not infrequent and they only appear to use a single insertion for each strain). This should be described and or added as a caveat if no validation was performed.

The authors also do not describe any validation for the CRISPR alleles, either deletions or insertion of the synthetic intron into dlg-1. How were accurate gene edits verified. - Are the experiments adequately replicated and statistical analysis adequate?

I am not convinced the statistical analysis of the fluorescence data is correct. Unless the authors show that every datapoint in the fluorescence quantification is independent, then I would argue they vastly overestimate the statistical significance. Even small differences are shown to have "***" levels of significance, which does not appear empirically plausible.

Minor comments:

• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately?

This study is so closely related to the Chen et al study, that I believe this study should be discussed in more detail to put the data into context. - Are the text and figures clear and accurate?

Yes, the text and figurea are clear - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Add H2B to the mNG in Figure 1 in order to understand where the first intron was inserted.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
• Place the work in the context of the existing literature (provide references, where appropriate).
• State what audience might be interested in and influenced by the reported findings.
• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

This manuscript shows an incremental advance in our understanding of HOT regions in C. elegans. The authors replicate similar data presented previously (enhancer assays on HOT regions, PMID: 24653213). Importantly, the authors funcationally validate their data with smFISH and CRISPR-mediated deletion of two enhancers (including the substitution of the intron for a synthetic intron), which is, to my knowledge, novel and advances the field. As such, the data presented validate and increase our confidence in prior results on HOT regions. Unfortunately, the more interesting conclusions about HOT region interactions and synergy to direct expression are less well supported. The work will likely be mainly of interest to C. elegans researchers working on transcriptional regulation. My own field of expertise is C. elegans gene regulation and my lab frequently uses transcriptional transgene assays to determine gene expression.

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Reply to the reviewers

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

This study explores chromatin organization around trans-splicing acceptor sites (TASs) in the trypanosomatid parasites Trypanosoma cruzi, T. brucei and Leishmania major. By systematically re-analyzing MNase-seq and MNase-ChIP-seq datasets, the authors conclude that TASs are protected by an MNase-sensitive complex that is, at least in part, histone-based, and that single-copy and multi-copy genes display differential chromatin accessibility. Altogether, the data suggest a common chromatin landscape at TASs and imply that chromatin may modulate transcript maturation, adding a new regulatory layer to an unusual gene-expression system.

I value integrative studies of this kind and appreciate the careful, consistent data analysis the authors implemented to extract novel insights. That said, several aspects require clarification or revision before the conclusions can be robustly supported. My main concerns are listed below, organized by topic/result section.

TAS prediction * Why were TAS predictions derived only from insect-stage RNA-seq data? Restricting TAS calls to one life stage risks biasing predictions toward transcripts that are highly expressed in that stage and may reduce annotation accuracy for lowly expressed or stage-specific genes. Please justify this choice and, if possible, evaluate TAS robustness using additional transcriptomes or explicitly state the limitation.

TAS predictions derived only from insect-stage RNA-seq data because in a previous study it was shown that there are no significant differences between stages in the 5'UTR procesing in T. cruzi life stages (https://doi.org/10.3389/fgene.2020.00166) We are not testing an additional transcriptome here, because the robustness of the software was already probed in the original article were UTRme was described (Radio S, 2018 doi:10.3389/fgene.2018.00671).

Results - "There is a distinctive average nucleosome arrangement at the TASs in TriTryps": * You state that "In the case of L. major the samples are less digested." However, Supplementary Fig. S1 suggests that replicate 1 of L. major is less digested than the T. brucei samples, while replicate 2 of L. major looks similarly digested. Please clarify which replicates you reference and correct the statement if needed.

The reviewer has a good point. We made our statement based on the value of the maximum peak of the sequenced DNA molecules, which in general is a good indicative of the extension of the digestion achieved by the sample (Cole H, NAR, 2011).

As the reviewer correctly points, we should have also considered the length of the DNA molecules in each percentile. However, in this case both, T. brucei's and L major's samples were gel purified before sequencing and it is hard to know exactly what fragments were left behind in each case. Therefore, it is better not to over conclude on that regard.

We have now comment on this in the main manuscript, and we have clarified in the figure legends which data set we used in each case in the figure legends and in Table S1.

* It appears you plot one replicate in Fig. 1b and the other in Suppl. Fig. S2. Please indicate explicitly which replicate is in each plot. For T. brucei, the NDR upstream of the TAS is clearer in Suppl. Fig. S2 while the TAS protection is less prominent; based on your digestion argument, this should correspond to the more-digested replicate. Please confirm.

The replicates used for the construction of each figure are explicitly indicated in Table S1. Although we have detailed in the table the original publication, the project and accession number for each data set, the reviewer is correct that in this case it was still not completely clear to which length distribution heatmap was each sample associated with. To avoid this confusion, we have now added the accession number for each data set to the figure legends and also clarified in Table S1. Regarding the reviewer's comment on the correspondence between the observed TAS protection and the extent of samples digestion, he/she is correct that for a more digested sample we would expect a clearer NDR. In this case, the difference in the extent of digestion between these two samples is minor, as observed the length of the main peak in the length distribution histogram for sequenced DNA molecules is the same. These two samples GSM5363006, represented in Fig1 b, and GSM5363007, represented in S2, belong to the same original paper (Maree et al 2017), and both were gel purified before sequencing. Therefore, any difference between them could not only be the result of a minor difference in the digestion level achieved in each experiment but could be also biased by the fragments included or not during gel purification. Therefore, I would not over conclude about TAS protection from this comparison. We have now included a brief comment on this, in the figure discussion

* The protected region around the TAS appears centered on the TAS in T. brucei but upstream in L. major. This is an interesting difference. If it is technical (different digestion or TAS prediction offset), explain why; if likely biological, discuss possible mechanisms and implications.

We appreciate the reviewer suggestion. We cannot assure if it is due to technical or biological reasons, but there is evidence that L. major 's genome has a different dinucleotide content and it might have an impact on nucleosome assembly. We have now added a comment about this observation in the final discussion of the manuscript.

Additionally, we analyzed DRIP-seq data for L. major, recently published doi: 10.1038/s41467-025-56785-y, and we observed that the R-loop footprint co-localized with the MNase-protected region upstream of the TAS (new S5 Fig), suggesting that the shift is not related to the MNase-seq technique.

Results - "An MNase sensitive complex occupies the TASs in T. brucei": * The definition of "MNase activity" and the ordering of samples into Low/Intermediate/High digestion are unclear. Did you infer digestion levels from fragment distributions rather than from controlled experimental timepoints? In Suppl. Fig. S3a it is not obvious how "Low digestion" was defined; that sample's fragment distribution appears intermediate. Please provide objective metrics (e.g., median fragment length, fraction 120-180 bp) used to classify digestion levels.

As the reviewer suggests, the ideal experiment would be to perform a time course of MNase reaction with all the samples in parallel, or to work with a fixed time point adding increasing amounts of MNase. However, even when making controlled experimental timepoints, you need to check the length distribution histogram of sequenced DNA molecules to be sure which level of digestion you have achieved.

In this particular case, we used public available data sets to make this analysis. We made an arbitrary definition of low, intermediate and high level of digestion, not as an absolute level of digestion, but as a comparative output among the tested samples. We based our definition on the comparison of __the main peak in length distribution heatmaps because this parameter is the best metric to estimate the level of digestion of a given sample. It represents the percentage of the total DNA sequenced that contains the predominant length in the sample tested. __Hence, we considered:

low digestion: when the main peak is longer than the expected protection for a nucleosome (longer than 150 bp). We expect this sample to contain additional longer bands that correspond to less digested material.

intermediate digestion, when the main peak is the expected for the nucleosome core-protection (˜146-150bp).

high digestion, when the main peak is shorter than that (shorter than 146 bp). This case, is normally accompanied by a bigger dispersion in fragment sizes.

To do this analysis, we chose samples that render different MNase protection of the TAS when plotting all the sequenced DNA molecules relative to this point and we used this protection as a predictor of the extent of sample digestion (Figure 2). To corroborate our hypothesis, that the degree of TAS protection was indeed related to the extent of the MNase digestion of a given sample, we looked at the length distribution histogram of the sequenced DNA molecules in each case. It is the best measurement of the extent of the digestion achieved, especially, when sequencing the whole sample without any gel purification and representing all the reads in the analysis as we did. The only caveat is with the sample called "intermediate digestion 1" that belongs to the original work of Mareé 2017, since only this data set was gel purified. To avoid this problem, we decided to remove this data from figures 2 and S3. In summary, the 3 remaining samples comes from the same lab, and belong to the same publication (Mareé 2022). These sample are the inputs of native MNase ChIp-seq, obtain the same way, totally comparable among each other.

* Several fragment distributions show a sharp cutoff at ~100-125 bp. Was this due to gel purification or bioinformatic filtering? State this clearly in Methods. If gel purification occurred, that can explain why some datasets preserve the MNase-sensitive region.

The sharp cutoff is neither due to gel purification or bioinformatic filtering, it is just due to the length of the paired-end read used in each case. In earlier works the most common was to sequence only 50bp, with the improvement of technologies it went up to 75,100 or 125 bp. We have now clarified in Table S1 the length of the paired-reads used in each case when possible.

* Please reconcile cases where samples labeled as more-digested contain a larger proportion of >200 bp fragments than supposedly less-digested samples; this ordering affects the inference that digestion level determines the loss/preservation of TAS protection. Based on the distributions I see, "Intermediate digestion 1" appears most consistent with an expected MNase curve - please confirm and correct the manuscript accordingly.

As explained above, it's a common observation in MNase digestion of chromatin that more extensive digestion can still result in a broad range of fragment sizes, including some longer fragments. This seemingly counter-intuitive result is primarily due to the non-uniform accessibility of chromatin and the sequence preference of the MNase enzyme, which has a preference for AT reach sequences.

The rationale of this is as follows: when you digest chromatin with MNase and the objective is to map nucleosomes genome-wide, the ideal situation would be to get the whole material contained in the mononucleosome band. Given that MNase is less efficient to digest protected DNA but, if the reaction proceeds further, it always ends up destroying part of it, the result is always far from perfect. The better situation we can get, is to obtain samples were ˜80% of the material is contained in the mononucloesome band. __And here comes the main point: __even in the best scenario, you always get some additional longer bands, such as those for di or tri nucleosomes. If you keep digesting, you will get less than 80 % in the nucleosome band and, those remaining DNA fragments that use to contain di and tri nucleosomes start getting digested as well, originating a bigger dispersion in fragments sizes. How do we explain persistence of Long Fragments? The longest fragments (di-, tri-nucleosomes) that persist in a highly digested sample are the ones that were originally most highly protected by proteins or higher-order structure, or by containing a poor AT sequence content, making their linker DNA extremely resistant to initial cleavage. Once the majority of the genome is fragmented, these few resistant longer fragments become a more visible component of the remaining population, contributing to a broader size dispersion. Hence, you end up observing a bigger dispersion in length distributions in the final material. Bottom line, it is not a good practice to work with under or over digested samples. Our main point, is to emphasize that especially when comparing samples, it important to compare those with comparable levels of digestion. Otherwise, a different sampling of the genome will be represented in the remaining sequenced DNA.

Results - "The MNase sensitive complexes protecting the TASs in T. brucei and T. cruzi are at least partly composed of histones": * The evidence that histones are part of the MNase-sensitive complex relies on H3 MNase-ChIP signal in subnucleosomal fragment bins. This seems to conflict with the observation (Fig. 1) that fragments protecting TASs are often nucleosome-sized. Please reconcile these points: are H3 signals confined to subnucleosomal fragments flanking the TAS while the TAS itself is depleted of H3? Provide plots that compare MNase-seq and H3 ChIP signals stratified by consistent fragment-size bins to clarify this.

What we learned from other eukaryotic organisms that were deeply studied, such as yeast, is that NDRs are normally generated at regulatory points in the genome. In this sense, yeast tRNA genes have a complex with a bootprint smaller than a nucleosome formed by TFIIIC-TFIIB (Nagarajavel, doi: 10.1093/nar/gkt611). On the other hand, many promotor regions have an MNase-sensitive complex with a nucleosome-size footprint, but it does not contain histones (Chereji, et al 2017, doi:10.1016/j.molcel.2016.12.009). The reviewer is right that from Figure 1 and S2 we could observe that the footprint of whatever occupies the TAS region, especially in T. brucei, is nucleosome-size. However, it only shows the size, but it doesn't prove the nature of its components. Nevertheless, those are only MNase-seq data sets. Since it does not include a precipitation with specific antibodies, we cannot confirm the protecting complex is made up by histones. In parallel, a complementary study by Wedel 2017, from Siegel's lab, shows that using a properly digested sample and further immunoprecipitating with a-H3 antibody, the TAS is not protected by nucleosomes at least not when analyzing nucleosome size-DNA molecules. Besides, Briggs et. al 2018 (doi: 10.1093/nar/gky928) showed that at least at intergenic regions H3 occupancy goes down while R-loops accumulation increases. We have now added a new figure 4 replotting R-loops and MNase-ChIP-seq for H3 relative to our predicted TAS showing this anti-correlation and how it partly correlates with MNase protection as well. As a control we show that Rpb9 trends resembles H3 as Siegel's lab have shown in Wedel 2018. Moreover, we analyzed redate from a recently published paper (doi: 10.1038/s41467-025-56785-y) added a new supplemental figure 5 showing that a similar correlation between MNase protection and R-loop footprint occurs in L. major (S5 Fig).

* Please indicate which datasets are used for each panel in Suppl. Fig. S4 (e.g., Wedel et al., Maree et al.), and avoid calling data from different labs "replicates" unless they are true replicates.

In most of our analysis we used real replicated experiments. Such is the case MNase-seq data used in Figure 1, with the corresponding replicate experiments used in Figure S2; T. cruzi MNase-ChIP-seq data used in Figure 3b and 4a with the respective replicate used in Figures S4 and S5 (now S6 in the revised manuscript). The only case in which we used experiments coming from two different laboratories, is in the case of MNase-ChIP-seq for H3 from T. brucei. Unfortunately, there are only two public data sets coming each of them from different laboratories. The samples used in Fig 3 (from Siegel's lab) whether the IP from H3 represented in S4 and S5 (S6 n the updated version) comes from another lab (Patterton's). To be more rigorous, we now call them data 1 and 2 when comparing these particular case.

The reviewer is right that in this particular case one is native chromatin (Pattertons') while the other one is crosslinked (Siegel's). We have now clarified it in the main text that unfortunately we do not count on a replicate but even under both condition the result remains the same, and this is compatible with my own experience, were crosslinking does not affect the global nucleosome patterns (compared nucleosome organization from crosslinked chromatin MNAse-seq inputs Chereji, Mol Cell, 2017 doi: 10.1016/j.molcel.2016.12.009 and native MNase-seq from Ocampo, NAR, 2016 doi: 10.1093/nar/gkw068).

* Several datasets show a sharp lower bound on fragment size in the subnucleosomal range (e.g., ~80-100 bp). Is this a filtering artifact or a gel-size selection? Clarify in Methods and, if this is an artifact, consider replotting after removing the cutoff.

We have only filtered adapter dimmer or overrepresented sequences when needed. In Figures 2 and S3 we represented all the sequenced reads. In other figures when we sort fragments sizes in silico, such as nucleosome range, dinucleosome or subnucleosome size, we make a note in the figure legends. What the reviewer points is related to the length of the sequence DNA fragment in each experiment. As we explained above, the older data-sets were performed with 50 bp paired-end reads, the newer ones are 75, 100 or 125bp. This is information is now clarified in Table S1.

__Results - "The TASs of single and multi-copy genes are differentially protected by nucleosomes": __

__ __* Please include T. brucei RNA-seq data in Suppl. Fig. S5b as you did for T. cruzi.

We have shown chromatin organization for T. brucei in previous S5b to illustrate that there is a similar trend. Unfortunately, we did not get a robust list of multi-copy genes for T. brucei as we did get for T. cruzi, therefore we do not want to over conclude showing the RNA-seq for these subsets of genes. The limitation is related to the fact that UTRme restrict the search and is extremely strict when calling sites at repetitive regions. Additionally, attending to the request of one reviewer we have now changed the UTR predictions for T. brucei using a different RNA-seq data set from Lister 427(detail in method section). Given that with the new predictions it was even harder to obtain the list of multicopy genes for T. brucei, we decided to remove that figure in the updated version of the manuscript.

* Discuss how low or absent expression of multigene families affects TAS annotation (which relies on RNA-seq) and whether annotation inaccuracies could bias the observed chromatin differences.

The mapping of occurrence and annotations that belong to repetitive regions has great complexity. UTRme is specially designed to avoid overcalling those sites. In other words, there is a chance that we could be underestimating the number of predicted TASs at multi-copy genes. Regarding the impact on chromatin analysis, we cannot rule out that it might have an impact, but the observation favors our conclusion, since even when some TASs at multi-copy genes can remain elusive, we observe more nucleosome density at those places.

* The statement that multi-copy genes show an "oscillation" between AT and GC dinucleotides is not clearly supported: the multi-copy average appears noisier and is based on fewer loci. Please tone down this claim or provide statistical support that the pattern is periodic rather than noisy.

We have fixed this now in the preliminary revised version

* How were multi-copy genes defined in T. brucei? Include the classification method in Methods.

This classification was done the same way it was explained for T. cruzi. However, decided to remove the supplemental figure that included this sorting.

Genomes and annotations: * If transcriptomic data for the Y strain was used for T. cruzi, please explain why a Y strain genome was not used (e.g., Wang et al. 2021 GCA_015033655.1), or justify the choice. For T. brucei, consider the more recent Lister 427 assembly (Tb427_2018) from TriTrypDB. Use strain-matched genomes and transcriptomes when possible, or discuss limitations.

The most appropriate way to analyze high throughput data, is to aline it to the same genome were the experiments were conducted. This was clearly illustrated in a previous publication from our group were we explained how should be analyzed data from the hybrid CL Brener strain. A common practice in the past was to use only Esmeraldo-like genome for simplicity, but this resulted in output artifacts. Therefore, we aligned it to CL Brener genome, and then focused the main analysis on the Esmeraldo haplotype (Beati Plos ONE, 2023). Ideally, we should have counted on transcriptomic data for the same strain (CL Brener or Esmeraldo). Since this was not the case at that moment, we used data from Y strain that belongs to the same DTU with Esmeraldo.

In the case of T. brucei, when we started our analysis and the software code for UTRme was written, the previous version of the genome was available. Upon 2018 version came up, we checked chromatin parameters and observed that it did not change the main observations. Therefore, we continue working with our previous setups.

Reproducibility and broader integration: * Please share the full analysis pipeline (ideally on GitHub/Zenodo) so the results are reproducible from raw reads to plots.

We are preparing a full pipeline in GitHub. We will make it available before manuscript full revision

* As an optional but helpful expansion, consider including additional datasets (other life stages, BSF MNase-seq, ATAC-seq, DRIP-seq) where available to strengthen comparative claims.

We are now including a new figure 4 and a supplemental figure 5 including DRIP-seq and Rp9 ChIP-seq for T. brucei (revised Fig 4) and DRIP-seq for L. major (S5 Fig). Additionally, we added FAIRE-seq data to previous Fig 4 now Fig 5 (revised Fig 5C).

We are analyzing ATAC-seq data for T. brucei.

Regarding BSF MNase-seq, the original article by Mareé 2017 claims that there is not significant difference for average chromatin organization between the two life forms; therefore, is not worth including that analysis.

Optional analyses that would strengthen the study: * Stratify single-copy genes by expression (high / medium / low) and examine average nucleosome occupancy at TASs for each group; a correlation between expression and NDR depth would strengthen the functional link to maturation.

We have now included a panel in suplemental figure 5 (now revised S6), showing the concordance for chromatin organization of stratified genes by RNA-seq levels relative to TAS.

__Minor / editorial comments: __ * In the Introduction, the sentence "transcription is initiated from dispersed promoters and in general they coincide with divergent strand switch regions" should be qualified: such initiation sites also include single transcription start regions.

We have clarified this in the preliminary revised version

* Define the dotted line in length distribution plots (if it is not the median, please clarify) and consider placing it at 147 bp across plots to ease comparison.

The dotted line is just to indicate where the maximum peak is located. It is now clarified in figure legends.

* In Suppl. Fig. 4b "Replicate2" the x-axis ticks are misaligned with labels - please fix.

We have now fixed the figure. Thanks for noticing this mistake.

* Typo in the Introduction: "remodellingremodeling" → "remodeling

Thanks for noticing this mistake, it is fixed in the current version of the manuscript

**Referee cross-commenting** Comment 1: I think Reviewer #2 and Reviewer #3 missed that they authors of this manuscript do cite and consider the results from Wedel at al. 2017. They even re-analysed their data (e.g. Figure 3a). I second Reviewer #2 comment indicating that the inclusion of a schematic figure to help readers visualize and better understand the findings would be an important addition.

Comment 2: I agree with Reviewer #3 that the use of different MNase digestion procedures in the different datasets have to be considered. On the other hand, I don't think there is a problem with figure 1 showing an MNase-protected TAS for T. brucei as it is based on MNase-seq data and reproduces the reported results (Maree et al. 2017). What the Siegel lab did in Wedel et al. 2017 was MNase-ChIPseq of H3 showing nucleosome depletion at TAS, but both results are not necessary contradictory: There could still be something else (which does not contain H3) sitting on the TAS protecting it from MNase digestion.

Reviewer #1 (Significance (Required)):

This study provides a systematic comparative analysis of chromatin landscapes at trans-splicing acceptor sites (TASs) in trypanosomatids, an area that has been relatively underexplored. By re-analyzing and harmonizing existing MNase-seq and MNase-ChIP-seq datasets, the authors highlight conserved and divergent features of nucleosome occupancy around TASs and propose that chromatin contributes to the fidelity of transcript maturation. The significance lies in three aspects: 1. Conceptual advance: It broadens our understanding of gene regulation in organisms where transcription initiation is unusual and largely constitutive, suggesting that chromatin can still modulate post-transcriptional processes such as trans-splicing. 2. Integrative perspective: Bringing together data from T. cruzi, T. brucei and L. major provides a comparative framework that may inspire further mechanistic studies across kinetoplastids. 3. Hypothesis generation: The findings open testable avenues about the role of chromatin in coordinating transcript maturation, the contribution of DNA sequence composition, and potential interactions with R-loops or RNA-binding proteins. Researchers in parasitology, chromatin biology, and RNA processing will find it a useful resource and a stimulus for targeted experimental follow-up.

My expertise is in gene regulation in eukaryotic parasites, with a focus on bioinformatic analysis of high-throughput sequencing data

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

Siri et al. perform a comparative analysis using publicly available MNase-seq data from three trypanosomatids (T. brucei, T. cruzi, and Leishmania), showing that a similar chromatin profile is observed at TAS (trans-splicing acceptor site) regions. The original studies had already demonstrated that the nucleosome profile at TAS differs from the rest of the genome; however, this work fills an important gap in the literature by providing the most reliable cross-species comparison of nucleosome profiles among the tritryps. To achieve this, the authors applied the same computational analysis pipeline and carefully evaluated MNase digestion levels, which are known to influence nucleosome profiling outcomes.

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. The manuscript could be improved with some clarifications and adjustments:

1. The authors state from the beginning that available MNase data indicate altered nucleosome occupancy around the TAS. However, they could also emphasize that the conclusions across the different trypanosomatids are inconsistent and even contradictory: NDR in T. cruzi versus protection-in different locations-in T. brucei and Leishmania.

We start our manuscript by referring to the first MNase-seq data sets publicly available for each TriTryp and we point that one of the main observations, in each of them, is the occurrence of a change in nucleosome density or occupancy at intergenic regions. In T. cruzi, in a previous publication from our group, we stablished that this intergenic drop in nucleosome density occurs near the trans-splicing acceptor site. In this work, we extend our study to the other members of TriTryps: T. brucei and L. major.

In T. brucei the papers from Patterton's lab and Siegel's lab came out almost simultaneously in 2017. Hence, they do not comment on each other's work. The first one claims the presence of a well-positioned nucleosome at the TAS by using MNase-seq, while the second one, shows an NDR at the TAS by using MNase-ChIP-seq. However, we do not think they are contradictory, or they have inconsistency. We brought them together along the manuscript because we think these works can provide complementary information.

On one hand, we infer data from Pattertons lab is slightly less digested than the sample from Siegel's lab. Therefore, we discuss that this moderate digestion must be the reason why they managed to detect an MNase protecting complex sitting at the TAS (Figure 1). On the other hand, Sigel's lab includes an additional step by performing MNase-ChIP-seq, showing that when analyzing nucleosome size fragments, histones are not detected at the TAS. Here, we go further in this analysis on figure 3, showing that only when looking at subnucleosome-size fragments, we can detect histone H3. And this is also true for T. cruzi.

By integrating every analysis in this work and the previous ones, we propose that TASs are protected by an MNase-sensitive complex (proved in Figure 2). This complex most likely is only partly formed by histones, since only when analyzing sub-nucleosomes size DNA molecules we can detect histone H3 (Figure 3). To be sure that the complex is not entirely made up by histones, future studies should perform an MNse-ChIP-seq with less digested samples. However, it was previously shown that R-loops are enriched at those intergenic NDRs (Briggs, 2018 doi: 10.1093/nar/gky928) and that R-loops have plenty of interacting proteins (Girasol, 2023 10.1093/nar/gkad836). Therefore, most likely, this MNase-sensitive complexed have a hybrid nature made up by H3 and some other regulatory molecules, possibly involved in trans-splicing. We have now added a new figure 4 showing R-loop co-localization with the NDR.

Regarding the comparison between different organisms, after explaining the sensitivity to MNase of the TAS protecting complex, we discuss that when comparing equally digested samples T. cruzi and T. brucei display a similar chromatin landscape with a mild NDR at the TAS (See T. cruzi represented in Figure 1 compared to T. brucei represented in Intermediate digestion 2 in Figure 2, intermediate digestion in the revised manuscript). Unfortunately, we cannot make a good comparison with L. major, since we do not count on a similar level of digestion. However, by analyzing a recently published DRIP-seq data-set for L. major we show that R-loop signal co localize with MNase-protection in a similar way (new S5 Fig).

Another point that requires clarification concerns what the authors mean in the introduction and discussion when they write that trypanosomes have "...poorly organized chromatin with nucleosomes that are not strikingly positioned or phased." On the other hand, they also cite evidence of organization: "...well-positioned nucleosome at the spliced-out region.. in Leishmania (ref 34)"; "...a well-positioned nucleosome at the TASs for internal genes (ref37)"; "...a nucleosome depletion was observed upstream of every gene (ref 35)." Aren't these examples of organized chromatin with at least a few phased nucleosomes? In addition, in ref 37, figure 4 shows at least two (possibly three to four) nucleosomes that appear phased. In my opinion, the authors should first define more precisely what they mean by "poorly organized chromatin" and clarify that this interpretation does not contradict the findings highlighted in the cited literature.

For a better understanding of nucleosome positioning and phasing I recommend the review: Clark 2010 doi:10.1080/073911010010524945, Figure 4. Briefly, in a cell population there are different alternative positions that a given nucleosome can adopt. However, some are more favorable. When talking about favorable positions, we refer to the coordinates in the genome that are most likely covered by a nucleosome and are predominant in the cell population. Additionally, nucleosomes could be phased or not. This refers not only the position in the genome, but to the distance relative to a given point. In yeast, or in highly transcribed genes of more complex eukaryotes, nucleosomes are regularly spaced and phased relative to the transcription start site (TSS) or to the +1 nucleosome (Ocampo, NAR, 2016, doi:10.1093/nar/gkw068). In trypanosomes, nucleosomes have some regular distribution when making a browser inspection but, given that they are not properly phased with respect to any point, it is almost impossible to make a spacing estimation from paired-end data. This is also consistent with a chromatin that is transcribed in an almost constitutive manner.

As the reviewer mention, we do site evidence of organization. We think the original observations are correct, but we do not fully agree with some of the original statements. In this manuscript our aim is to take the best we learned from their original works and to make a constructive contribution adding to the original discussions. In this regard, in trypanosomes there are some conserved patterns in the chromatin landscape, but their nucleosomes are far from being well-positioned or phased. For a better understanding, compare the variations observed in the y axis when representing av. nucleosome occupancy in yeast with those observed in trypanosomes and you will see that the troughs and peaks are much more prominent in yeast than the ones observed in any TryTryp member.

Following the reviewer's suggestion we have now clarified this in the main text.

The paper would also benefit from the inclusion of a schematic figure to help readers visualize and better understand the findings. What is the biological impact of having nucleosomes, di-nucleosomes, or sub-nucleosomes at TAS? This is not obvious to readers outside the chromatin field. For example, the following statement is not intuitive: "We observed that, when analyzing nucleosome-size (120-180 bp) DNA molecules or longer fragments (180-300 bp), the TASs of either T. cruzi or T. brucei are mostly nucleosome-depleted. However, when representing fragments smaller than a nucleosome-size (50-120 bp) some histone protection is unmasked (Fig. 3 and Fig. S4). This observation suggests that the MNase sensitive complex sitting at the TASs is at least partly composed of histones." Please clarify.

We appreciate the reviewer's suggestion to make a schematic figure. We have now added a new Figure 6.

Regarding the biological impact of having mono, di or subnucleosome fragments, it is important to unveil the fragment size of the protected DNA to infer the nature of the protecting complex. In the case of tRNA genes in yeast, at pol III promoters they found footprints smaller than a nucleosome size that ended up being TFIIB-TFIIC (Nagarajavel, doi: 10.1093/nar/gkt611). Therefore, detecting something smaller than a nucleosome might suggest the binding of trans-acting factors different than histones or involving histones in a mixed complex. These mixed complexes are also observed, and that is the case of the centromeric nucleosome which has a very peculiar composition (Ocampo and Clark, Cells Reports, 2015). On the other hand, if instead we detect bigger fragments, it could be indicative of the presence of bigger protecting molecules or that those regions are part of higher order chromatin organization still inaccessible for MNase linker digestions.

Here we show on 2Dplots, that complex or components protecting the TAS have nucleosome size, but we cannot assure they are entirely made up by histones, since, only when looking at subnucleosome-size fragments, we are able to detect histone H3. We have now added part of this explanation to the discussion.

By integrating every analysis in this work and the previous ones, we propose that the TAS is protected by an MNase-sensitive complex (Figure 2). This complex most likely is only partly formed by histones, since only when analyzing sub-nucleosomes size DNA molecules we can detect histone H3 (Figure 3). As explained above, to be sure that the complex is not entirely made up by histones, future studies should perform an MNse-ChIP-seq with less digested samples. However, it was previously shown that R-loops are enriched at those intergenic NDRs (Briggs 2018) and that R-loops have plenty of interacting proteins (Girasol, 2023). Therefore, most likely, this MNase-sensitive complexed have a hybrid nature made up by H3 and some other regulatory molecules. We have now added a new figure 4 showing R-loop partial co-localization with MNase protection.

Some references are missing or incorrect:

we will make a thorough revision

"In trypanosomes, there are no canonical promoter regions." - please check Cordon-Obras et al. (Navarro's group). Thank you for the appropiate suggestion.

Thank you for the appropriate suggestion. We have now added this reference

Please, cite the study by Wedel et al. (Siegel's group), which also performed MNase-seq analysis in T. brucei.

We understand that reviewer number 2# missed that we cited this reference and that we did used the raw data from the manuscript of Wedel et. al 2017 form Siegel's group. We used the MNase-ChIP-seq data set of histone H3 in our analysis for Figures 3, S4 and S6 (in the revised version), also detailed in table S1. To be even more explicit, we have now included the accession number of each data set in the figure legends.

Figure-specific comments: Fig. S3: Why does the number of larger fragments increase with greater MNase digestion? Shouldn't the opposite be expected?

This a good observation. As we also explained to reviewer#1:

It's a common observation in MNase digestion of chromatin that more extensive digestion can still result in a broad range of fragment sizes, including some longer fragments. This seemingly counter-intuitive result is primarily due to the non-uniform accessibility of chromatin and the sequence preference of the MNase enzyme.

The rationale of this is as follows: when you digest chromatin with MNase and the objective is to map nucleosomes genome-wide, the ideal situation would get the whole material contained in the mononucleosome band. Given that MNase is less efficient to digest protected DNA but, if the reaction proceeds further, it always ends up destroying part of it, the result is always far from perfect. The better situation we can get, is to obtain samples were ˜80% of the material is contained in the mononucloesome band. __And here comes the main point: __even in the best scenario, you always have some additional longer bands, such as those for di or tri nucleosomes. If you keep digesting, you will get less than 80 % in the nucleosome band and, those remaining DNA fragments that use to contain di and tri nucleosomes start getting digested as well originating a bigger dispersion in fragments sizes. How do we explain persistence of Long Fragments? The longest fragments (di-, tri-nucleosomes) that persist in a highly digested sample are the ones that were originally most highly protected by proteins or higher-order structure, making their linker DNA extremely resistant to initial cleavage. Once most of the genome is fragmented, these few resistant longer fragments become a more visible component of the remaining population, contributing to a broader size dispersion. Hence, there you end up having a bigger dispersion in length distributions in the final material. Bottom line, it is not a good practice to work with under or overdirected samples. Our main point is to emphasize that especially when comparing samples, it important to compare those with comparable levels of digestion. Otherwise, a different sampling of the genome will be represented in the remaining sequenced DNA.

Minor points:

There are several typos throughout the manuscript.

Thanks for the observation. We will check carefully.

Methods: "Dinucelotide frecuency calculation."

We will add a code in GitHub

Reviewer #2 (Significance (Required)):

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. Audience: basic science and specialized readers.

Expertise: epigenetics and gene expression in trypanosomatids.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

The authors analysed publicly accessible MNase-seq data in TriTryps parasites, focusing on the chromatin structure around trans-splicing acceptor sites (TASs), which are vital for processing gene transcripts. They describe a mild nucleosome depletion at the TAS of T. cruzi and L. major, whereas a histone-containing complex protects the TASs of T. brucei. In the subsequent analysis of T. brucei, they suggest that a Mnase-sensitive complex is localised at the TASs. For single-copy versus multi-copy genes, the authors show different di-nucleotide patterns and chromatin structures. Accordingly, they propose this difference could be a novel mechanism to ensure the accuracy of trans-splicing in these parasites.

Before providing an in- depth review of the manuscript, I note that some missing information would have helped in assessing the study more thoroughly; however, in the light of the available information, I provide the following comments for consideration.

The numbering of the figures, including the figure legends, is missing in the PDF file. This is essential for assessing the provided information.

We apologized for not including the figure numbers in the main text, although they are located in the right place when called in the text. The omission was unwillingly made when figure legends were moved to the bottom of the main text. This is now fixed in the updated version of the manuscript.

The publicly available Mnase- seq data are manyfold, with multiple datasets available for T. cruzi, for example. It is unclear from the manuscript which dataset was used for which figure. This must be clarified.

This was detailed in Table S1. We have now replaced the table by an improved version, and we have also included the accession number of each data set used in the figure legends.

Why do the authors start in figure 1 with the description of an MNase- protected TAS for T.brucei, given that it has been clearly shown by the Siegel lab that there is a nucleosome depletion similar to other parasites?

We did not want to ignore the paper from Patterton's lab because it was the first one to map nucleosomes genome-wide in T. brucei and the main finding of that paper claimed the existence of a well-positioned nucleosome at intergenic regions, what we though constitutes a point worth to be discussed. While Patterton's work use MNase-seq from gel-purified samples and provides replicated experiments sequenced in really good depth; Siegel's lab uses MNase-ChIP-seq of histone H3 but performs only one experiment and its input was not sequenced. So, each work has its own caveats and provides different information that together contributes to make a more comprehensive study. We think that bringing up both data sets to the discussion, as we have done in Figures 1 and 3, helps us and the community working in the field to enrich the discussion.

If the authors re- analyse the data, they should compare their pipeline to those used in the other studies, highlighting differences and potential improvements.

We are working on this point. We will provide a more detail description in the final revision.

Since many figures resemble those in already published studies, there seems little reason to repeat and compare without a detailed comparison of the pipelines and their differences.

Following the reviewer advice, we are now working on highlighting the main differences that justify analyzing the data the way we did and will be added in the finally revised method section.

At a first glance, some of the figures might look similar when looking at the original manuscripts comparing with ours. However, with a careful and detailed reading of our manuscripts you can notice that we have added several analyses that allow to unveil information that was not disclosed before.

First, we perform a systematic comparison analyzing every data set the same way from beginning to end, being the main difference with previous studies the thorough and precise prediction of TAS for the three organisms. Second, we represent the average chromatin organization relative to those predicted TASs for TriTryps and discuss their global patterns. Third, by representing the average chromatin into heatmaps, we show for the very first time, that those average nucleosome landscape are not just an average, they keep a similar organization in most of the genome. These was not done in any of the previous manuscripts except for our own (Beati, PLOS One 2023). Additionally, we introduce the discussion of how the extension of MNase reaction can affect the output of these experiments and we show 2D-plots and length distribution heatmaps to discuss this point (a point completely ignored in all the chromatin literature for trypanosomes). Furthermore, we made a far-reaching analysis by considering the contributions of each publish work even when addressed by different techniques. Finally, we discuss our findings in the context of a topic of current interest in the field, such as TriTryp's genome compartmentalization.

Several previous Mnase- seq analysis studies addressing chromatin accessibility emphasized the importance of using varying degrees of chromatin digestion, from low to high digestion (30496478, 38959309, 27151365).

The reviewer is correct, and this point is exactly what we intended to illustrate in figure number 2. We appreciate he/she suggests these references that we are now citing in the final discussion. Just to clarify, using varying degrees of chromatin digestion is useful to make conclusions about a given organism but when comparing samples, strains, histone marks, etc. It is extremely important to do it upon selection of similar digested samples.

No information on the extent of DNA hydrolysis is provided in the original Mnase- seq studies. This key information can not be inferred from the length distribution of the sequenced reads.

The reviewer is correct that "No information on the extent of DNA hydrolysis is provided in the original Mnase-seq studies" and this is another reason why our analysis is so important to be published and discussed by the scientific community working in trypanosomes. We disagree with the reviewer in the second statement, since the level of digestion of a sequenced sample is actually tested by representing the length distribution of the total DNA sequenced. It is true that before sequencing you can, and should, check the level of digestion of the purified samples in an agarose gel and/or in a bioanalyzer. It could be also tested after library preparation, but before sequencing, expecting to observe the samples sizes incremented in size by the addition of the library adapters. But, the final test of success when working with MNase digested samples is to analyze length of DNA molecules by representing the histograms with length distribution of the sequenced DNA molecules. Remarkably, on occasions different samples might look very similar when run in a gel, but they render different length distribution histograms and this is because the nucleosome core could be intact but they might have suffered a differential trimming of the linker DNA associated to it or even be chewed inside (see Cole Hope 2011, section 5.2, doi: 10.1016/B978-0-12-391938-0.00006-9, for a detailed explanation).

As the input material are selected, in part gel- purified mono- nucleosomal DNA bands. Furthermore the datasets are not directly comparable, as some use native MNase, while others employ MNase after crosslinking; some involve short digestion times at 37 {degree sign} C, while others involve longer digestion at lower temperatures. Combining these datasets to support the idea of an MNase- sensitive complex at the TAS of T. brucei therefore may not be appropriate, and additional experiments using consistent methodologies would strengthen the study's conclusions.

In my opinion, describing an MNase- sensitive complex based solely on these data is not feasible. It requires specifically designed experiments using a consistent method and well- defined MNase digestion kinetics.

As the reviewer suggests, the ideal experiment would be to perform a time course of MNase reaction with all the samples in parallel, or to work with a fix time point adding increasing amounts of MNase. However, the information obtained from the detail analysis of the length distribution histogram of sequenced DNA molecules the best test of the real outcome. In fact, those samples with different digestion levels were probably not generated on purpose.

The only data sets that were gel purified are those from Mareé 2017 (Patterton's lab), used in Figures 1, S1 and S2 and those from L. major shown in Fig 1. It was a common practice during those years, then we learned that is not necessary to gel purify, since we can sort fragment sizes later in silico when needed.

As we explained to reviewer #1, to avoid this conflict, we decided to remove this data from figures 2 and S3. In summary, the 3 remaining samples comes from the same lab, and belong to the same publication (Mareé 2022). These sample are the inputs of native MNase ChIp-seq, obtain the same way, totally comparable among each other.

Reviewer #3 (Significance (Required)):

Due to the lack of controlled MNase digestion, use of heterogeneous datasets, and absence of benchmarking against previous studies, the conclusions regarding MNase-sensitive complexes and their functional significance remain speculative. With standardized MNase digestion and clearly annotated datasets, this study could provide a valuable contribution to understanding chromatin regulation in TriTryps parasites.

As we have explained in the previous point our conclusions are valid since we do not compare in any figure samples coming from different treatments. The only exception to this comment could be in figure 3 when talking about MNase-ChIP-seq. We have now added a clear and explicit comment in the section and the discussion that despite having subtle differences in experimental procedures we arrive to the same results. This is the case for T. cruzi IP, run from crosslinked chromatin, compared to T. brucei's IP, run from native chromatin.

Along the years it was observed in the chromatin field that nucleosomes are so tightly bound to DNA that crosslinking is not necessary. However, it is still a common practice specially when performing IPs. In our own hands, we did not observe any difference at the global level neither in T. cruzi (unpublished) nor in my previous work with yeast (compared nucleosome organization from crosslinked chromatin MNAse-seq inputs Chereji, Mol Cell, 2017 doi:10.1016/j.molcel.2016.12.009 and native MNase-seq from Ocampo, NAR, 2016 doi: 10.1093/nar/gkw068).

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Referee #3

Evidence, reproducibility and clarity

The authors analysed publicly accessible MNase-seq data in TriTryps parasites, focusing on the chromatin structure around trans-splicing acceptor sites (TASs), which are vital for processing gene transcripts. They describe a mild nucleosome depletion at the TAS of T. cruzi and L. major, whereas a histone-containing complex protects the TASs of T. brucei. In the subsequent analysis of T. brucei, they suggest that a Mnase-sensitive complex is localised at the TASs. For single-copy versus multi-copy genes, the authors show different di-nucleotide patterns and chromatin structures. Accordingly, they propose this difference could be a novel mechanism to ensure the accuracy of trans-splicing in these parasites.

Before providing an in- depth review of the manuscript, I note that some missing information would have helped in assessing the study more thoroughly; however, in the light of the available information, I provide the following comments for consideration.

The numbering of the figures, including the figure legends, is missing in the PDF file. This is essential for assessing the provided information. The publicly available Mnase- seq data are manyfold, with multiple datasets available for T. cruzi, for example. It is unclear from the manuscript which dataset was used for which figure. This must be clarified. Why do the authors start in figure 1 with the description of an MNase- protected TAS for T.brucei, given that it has been clearly shown by the Siegel lab that there is a nucleosome depletion similar to other parasites? If the authors re- analyse the data, they should compare their pipeline to those used in the other studies, highlighting differences and potential improvements. Since many figures resemble those in already published studies, there seems little reason to repeat and compare without a detailed comparison of the pipelines and their differences. Several previous Mnase- seq analysis studies addressing chromatin accessibility emphasised the importance of using varying degrees of chromatin digestion, from low to high digestion (30496478, 38959309, 27151365). No information on the extent of DNA hydrolysis is provided in the original Mnase- seq studies. This key information can not be inferred from the length distribution of the sequenced reads. As the input material are selected, in part gel- purified mono- nucleosomal DNA bands. Furthermore the datasets are not directly comparable, as some use native MNase, while others employ MNase after crosslinking; some involve short digestion times at 37 {degree sign} C, while others involve longer digestion at lower temperatures. Combining these datasets to support the idea of an MNase- sensitive complex at the TAS of T. brucei therefore may not be appropriate, and additional experiments using consistent methodologies would strengthen the study's conclusions. In my opinion, describing an MNase- sensitive complex based solely on these data is not feasible. It requires specifically designed experiments using a consistent method and well- defined MNase digestion kinetics.

Significance

Due to the lack of controlled MNase digestion, use of heterogeneous datasets, and absence of benchmarking against previous studies, the conclusions regarding MNase-sensitive complexes and their functional significance remain speculative. With standardized MNase digestion and clearly annotated datasets, this study could provide a valuable contribution to understanding chromatin regulation in TriTryps parasites.

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Referee #2

Evidence, reproducibility and clarity

Siri et al. perform a comparative analysis using publicly available MNase-seq data from three trypanosomatids (T. brucei, T. cruzi, and Leishmania), showing that a similar chromatin profile is observed at TAS (trans-splicing acceptor site) regions. The original studies had already demonstrated that the nucleosome profile at TAS differs from the rest of the genome; however, this work fills an important gap in the literature by providing the most reliable cross-species comparison of nucleosome profiles among the tritryps. To achieve this, the authors applied the same computational analysis pipeline and carefully evaluated MNase digestion levels, which are known to influence nucleosome profiling outcomes.

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. The manuscript could be improved with some clarifications and adjustments:

1. The authors state from the beginning that available MNase data indicate altered nucleosome occupancy around the TAS. However, they could also emphasize that the conclusions across the different trypanosomatids are inconsistent and even contradictory: NDR in T. cruzi versus protection-in different locations-in T. brucei and Leishmania.
2. Another point that requires clarification concerns what the authors mean in the introduction and discussion when they write that trypanosomes have "...poorly organized chromatin with nucleosomes that are not strikingly positioned or phased." On the other hand, they also cite evidence of organization: "...well-positioned nucleosome at the spliced-out region.. in Leishmania (ref 34)"; "...a well-positioned nucleosome at the TASs for internal genes (ref37)"; "...a nucleosome depletion was observed upstream of every gene (ref 35)." Aren't these examples of organized chromatin with at least a few phased nucleosomes? In addition, in ref 37, figure 4 shows at least two (possibly three to four) nucleosomes that appear phased. In my opinion, the authors should first define more precisely what they mean by "poorly organized chromatin" and clarify that this interpretation does not contradict the findings highlighted in the cited literature.
3. The paper would also benefit from the inclusion of a schematic figure to help readers visualize and better understand the findings. What is the biological impact of having nucleosomes, di-nucleosomes, or sub-nucleosomes at TAS? This is not obvious to readers outside the chromatin field. For example, the following statement is not intuitive: "We observed that, when analyzing nucleosome-size (120-180 bp) DNA molecules or longer fragments (180-300 bp), the TASs of either T. cruzi or T. brucei are mostly nucleosome-depleted. However, when representing fragments smaller than a nucleosome-size (50-120 bp) some histone protection is unmasked (Fig. 3 and Fig. S4). This observation suggests that the MNase sensitive complex sitting at the TASs is at least partly composed of histones." Please clarify. Some references are missing or incorrect:

"In trypanosomes, there are no canonical promoter regions." - please check Cordon-Obras et al. (Navarro's group).

Please, cite the study by Wedel et al. (Siegel's group), which also performed MNase-seq analysis in T. brucei.

Figure-specific comments:

Fig. S3: Why does the number of larger fragments increase with greater MNase digestion? Shouldn't the opposite be expected?

Fig. S5B: Why not use MNase conditions under which T. cruzi and T. brucei display comparable profiles at TAS? This would facilitate interpretation.

Minor points:

There are several typos throughout the manuscript.

Methods: "Dinucelotide frecuency calculation."

Significance

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms.

Audience: basic science and specialized readers.

Expertise: epigenetics and gene expression in trypanosomatids.

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Referee #1

Evidence, reproducibility and clarity

This study explores chromatin organization around trans-splicing acceptor sites (TASs) in the trypanosomatid parasites Trypanosoma cruzi, T. brucei and Leishmania major. By systematically re-analyzing MNase-seq and MNase-ChIP-seq datasets, the authors conclude that TASs are protected by an MNase-sensitive complex that is, at least in part, histone-based, and that single-copy and multi-copy genes display differential chromatin accessibility. Altogether, the data suggest a common chromatin landscape at TASs and imply that chromatin may modulate transcript maturation, adding a new regulatory layer to an unusual gene-expression system.

I value integrative studies of this kind and appreciate the careful, consistent data analysis the authors implemented to extract novel insights. That said, several aspects require clarification or revision before the conclusions can be robustly supported. My main concerns are listed below, organized by topic/result section.

TAS prediction:

• Why were TAS predictions derived only from insect-stage RNA-seq data? Restricting TAS calls to one life stage risks biasing predictions toward transcripts that are highly expressed in that stage and may reduce annotation accuracy for lowly expressed or stage-specific genes. Please justify this choice and, if possible, evaluate TAS robustness using additional transcriptomes or explicitly state the limitation.

Results

• "There is a distinctive average nucleosome arrangement at the TASs in TriTryps":
• You state that "In the case of L. major the samples are less digested." However, Supplementary Fig. S1 suggests that replicate 1 of L. major is less digested than the T. brucei samples, while replicate 2 of L. major looks similarly digested. Please clarify which replicates you reference and correct the statement if needed.
• It appears you plot one replicate in Fig. 1b and the other in Suppl. Fig. S2. Please indicate explicitly which replicate is in each plot. For T. brucei, the NDR upstream of the TAS is clearer in Suppl. Fig. S2 while the TAS protection is less prominent; based on your digestion argument, this should correspond to the more-digested replicate. Please confirm. The protected region around the TAS appears centered on the TAS in T. brucei but upstream in L. major. This is an interesting difference. If it is technical (different digestion or TAS prediction offset), explain why; if likely biological, discuss possible mechanisms and implications.

Results

• "An MNase sensitive complex occupies the TASs in T. brucei":
• The definition of "MNase activity" and the ordering of samples into Low/Intermediate/High digestion are unclear. Did you infer digestion levels from fragment distributions rather than from controlled experimental timepoints? In Suppl. Fig. S3a it is not obvious how "Low digestion" was defined; that sample's fragment distribution appears intermediate. Please provide objective metrics (e.g., median fragment length, fraction 120-180 bp) used to classify digestion levels.
• Several fragment distributions show a sharp cutoff at ~100-125 bp. Was this due to gel purification or bioinformatic filtering? State this clearly in Methods. If gel purification occurred, that can explain why some datasets preserve the MNase-sensitive region.
• Please reconcile cases where samples labeled as more-digested contain a larger proportion of >200 bp fragments than supposedly less-digested samples; this ordering affects the inference that digestion level determines the loss/preservation of TAS protection. Based on the distributions I see, "Intermediate digestion 1" appears most consistent with an expected MNase curve - please confirm and correct the manuscript accordingly. Results - "The MNase sensitive complexes protecting the TASs in T. brucei and T. cruzi are at least partly composed of histones":
• The evidence that histones are part of the MNase-sensitive complex relies on H3 MNase-ChIP signal in subnucleosomal fragment bins. This seems to conflict with the observation (Fig. 1) that fragments protecting TASs are often nucleosome-sized. Please reconcile these points: are H3 signals confined to subnucleosomal fragments flanking the TAS while the TAS itself is depleted of H3? Provide plots that compare MNase-seq and H3 ChIP signals stratified by consistent fragment-size bins to clarify this.
• Please indicate which datasets are used for each panel in Suppl. Fig. S4 (e.g., Wedel et al., Maree et al.), and avoid calling data from different labs "replicates" unless they are true replicates.
• Several datasets show a sharp lower bound on fragment size in the subnucleosomal range (e.g., ~80-100 bp). Is this a filtering artifact or a gel-size selection? Clarify in Methods and, if this is an artifact, consider replotting after removing the cutoff. Results - "The TASs of single and multi-copy genes are differentially protected by nucleosomes":
• Please include T. brucei RNA-seq data in Suppl. Fig. S5b as you did for T. cruzi.
• Discuss how low or absent expression of multigene families affects TAS annotation (which relies on RNA-seq) and whether annotation inaccuracies could bias the observed chromatin differences.
• The statement that multi-copy genes show an "oscillation" between AT and GC dinucleotides is not clearly supported: the multi-copy average appears noisier and is based on fewer loci. Please tone down this claim or provide statistical support that the pattern is periodic rather than noisy.
• How were multi-copy genes defined in T. brucei? Include the classification method in Methods.

Genomes and annotations:

• If transcriptomic data for the Y strain was used for T. cruzi, please explain why a Y strain genome was not used (e.g., Wang et al. 2021 GCA_015033655.1), or justify the choice. For T. brucei, consider the more recent Lister 427 assembly (Tb427_2018) from TriTrypDB. Use strain-matched genomes and transcriptomes when possible, or discuss limitations.

Reproducibility and broader integration:

• Please share the full analysis pipeline (ideally on GitHub/Zenodo) so the results are reproducible from raw reads to plots.
• As an optional but helpful expansion, consider including additional datasets (other life stages, BSF MNase-seq, ATAC-seq, DRIP-seq) where available to strengthen comparative claims. Optional analyses that would strengthen the study:
• Stratify single-copy genes by expression (high / medium / low) and examine average nucleosome occupancy at TASs for each group; a correlation between expression and NDR depth would strengthen the functional link to maturation.

Minor / editorial comments:

• In the Introduction, the sentence "transcription is initiated from dispersed promoters and in general they coincide with divergent strand switch regions" should be qualified: such initiation sites also include single transcription start regions.
• Define the dotted line in length distribution plots (if it is not the median, please clarify) and consider placing it at 147 bp across plots to ease comparison.
• In Suppl. Fig. 4b "Replicate2" the x-axis ticks are misaligned with labels - please fix.
• Typo in the Introduction: "remodellingremodeling" → "remodeling."

Referee cross-commenting

Comment 1: I think Reviewer #2 and Reviewer #3 missed that they authors of this manuscript do cite and consider the results from Wedel at al. 2017. They even re-analysed their data (e.g. Figure 3a). I second Reviewer #2 comment indicating that the inclusion of a schematic figure to help readers visualize and better understand the findings would be an important addition.

Comment 2: I agree with Reviewer #3 that the use of different MNase digestion procedures in the different datasets have to be considered. On the other hand, I don't think there is a problem with figure 1 showing an MNase-protected TAS for T. brucei as it is based on MNase-seq data and reproduces the reported results (Maree et al. 2017). What the Siegel lab did in Wedel et al. 2017 was MNase-ChIPseq of H3 showing nucleosome depletion at TAS, but both results are not necessary contradictory: There could still be something else (which does not contain H3) sitting on the TAS protecting it from MNase digestion.

Significance

This study provides a systematic comparative analysis of chromatin landscapes at trans-splicing acceptor sites (TASs) in trypanosomatids, an area that has been relatively underexplored. By re-analyzing and harmonizing existing MNase-seq and MNase-ChIP-seq datasets, the authors highlight conserved and divergent features of nucleosome occupancy around TASs and propose that chromatin contributes to the fidelity of transcript maturation.

The significance lies in three aspects:

1. Conceptual advance: It broadens our understanding of gene regulation in organisms where transcription initiation is unusual and largely constitutive, suggesting that chromatin can still modulate post-transcriptional processes such as trans-splicing.
2. Integrative perspective: Bringing together data from T. cruzi, T. brucei and L. major provides a comparative framework that may inspire further mechanistic studies across kinetoplastids.
3. Hypothesis generation: The findings open testable avenues about the role of chromatin in coordinating transcript maturation, the contribution of DNA sequence composition, and potential interactions with R-loops or RNA-binding proteins. Researchers in parasitology, chromatin biology, and RNA processing will find it a useful resource and a stimulus for targeted experimental follow-up.

My expertise is in gene regulation in eukaryotic parasites, with a focus on bioinformatic analysis of high-throughput sequencing data

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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 #4

Evidence, reproducibility and clarity

Major criticisms

The manuscript by Chapa-y-Lazo et al. is confusing. It does not provide precise information about the three photostable monomers developed by different research groups. Please read the review (ref. 17) carefully. The monomeric version analyzed in this study was developed by Ivorra-Molla et al. and should be referred to as StayGold-E138D. This variant excels in dispersibility (monomericity), photostability, and molecular brightness (the product of the molar extinction coefficient and the fluorescence quantum yield). However, when analyzed in animal cells, StayGold-E138D is practically dim, and its brightness is poor. This can be seen in Figures 2, 3, S5, and S6 of the manuscript. The maturation efficiency of the chromophore is not so good in fly embryos. On the other hand, Ando et al. independently developed a monomeric version of StayGold called mStayGold at FPbase and Addgene. Therefore, I think that the authors should acknowledge that their analysis of StayGold monomer behavior is still incomplete. Additionally, the evolution tree of StayGold shown in Figure S2 is incorrect. The side-by side comparison of the three monomeric variants of StayGold, including StayGold-E138D and mStayGold, is documented in a recent preprint. Comparison of monomeric variants of StayGold | bioRxiv

Minor comments

Line 84 z-stacks were acquired using a spinning disc confocal microscope. Line 100 we collected a z-stack through each embryo. Line373 We analyzed the slices from 7 µm to 20.5 µm depth. Line 390 Depth 9 µm to 21 µm was analyzed. It is not clear what "z-stack" means in these sentences.

Significance

Nothing in particular.

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Referee #3

Evidence, reproducibility and clarity

Chapa-y-Lazo and colleagues report the detailed characterization of a number of different genetically-encoded fluorescent proteins in Drosophila embryos. The screening and selection of an appropriate fluorescent protein for imaging tasks is an important and often neglected part of experimental design, and datasets such as this one will be extremely useful in guiding decision making for other users. The manuscript is well-written and carefully controlled for different developmental stages and nicely compares the most pertinent properties of FPs such as brightness, photobleaching, and folding time. There would be a couple of additional experiments that would be nice to see but are not strictly necessary for improving the paper as-is, but might be helpful points to include in the discussion.

Comments:

1) All fluorophores in this study were fused to H2Av, at the same insertion site, which makes for a nice and easy comparison between lines. However, histone-binding proteins can sometimes behave unpredictably when tagged with different things and in addition it would be interesting to see if the fusion protein affects the FP properties in anyway. I.e. would sfGFP be brighter than mEmerald when bound to a CAAX sequence or some other organelle? It would be impractical for this study to re-do all the FPs, but the top two hits could be interesting and would potentially be quite interesting if there is a significant difference in behaviour between FPs when bound to different proteins/cellular compartments. Else maybe a mention in the discussion?

2) Another way to compare the fluorophore folding time would be to selectively bleach a portion of the embryo at the same developmental stage and measure the time it takes for each FP to recover to the same intensity as the rest of the embryo. This could potentially control for any delay for developmental reasons.

3) Some of the lines in the figure plots could be a bit thicker - purple and pink when overlapping are hard to distinguish.

Significance

This manuscript will be quite useful for those who are deciding between which fluorescent protein or combination to use for their live-imaging work, and additionally has created a number of useful fly strains in the process. It will hopefully also start a discussion about proper characterization and quantification of fluorescent reporters under different conditions, ideally before all the effort to generate an entirely new genetically modified animal is performed.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript Saunders and colleagues benchmark the brightness, folding speed and photostability of a variety of red (8 versions) and green fluorescent proteins (9 versions), which have been widely used for in vivo imaging. They fused each protein to histone2Av, cloned the fusion into attP constructs and inserted them in the Drosophila genome at the same genetic location. Thus, expression levels can be compared. Nuclei at embryonic cycle 14 were imaged, segmented and fluorescence was quantified. At this early stage the maturation kinetics of the fluorophore can particularly influence its fluorescence intensity.

Additionally, stage 15-16 embryos were imaged at the dorsal side to quantify brightness. As the histone promoter is active in all cells, the fluorescence in the nuclei of all cell types can be quantified. Brightness differences between the different proteins vary a bit between both experiments, likely taking folding versus brightness into account. Generally, sfGFP, mEGFP, mEmerald as well as mStrawberry and mScarlet are the brightest. Next, developmental movies were recorded starting at gastrulation to estimate the folding rates of the different proteins. No large differences of the relative fluorescence increase over time were reported. To estimate photostability, embryos were imaged ventrally shortly before the onset of gastrulation for 2 or 4 hours with high laser intensity and the fluorescence intensity was recorded. Consistent with data in the literature, StayGold is the most photostable green protein, although it is not the brightest from the start, likely to also slower folding. From the red proteins mRFP and mCherry are good choices for long-term imaging.

In summary, these results do not bring huge surprises but are still valuable for future choice of protein tagging for imaging. Best green proteins are mEGFP, mNeonGreen, mStayGold with differences in brightness vs stability. For red, no protein is the clear winner, mScarlet-I is good in folding and brightness but others are better for photostability.

Major comments:

1. Form the methods, it is not clear which promoter is used to drive expression of the histone2Av fusions. I assume this is not UAS but the histone promotor/enhancer. Please clarify.
2. From text is not always what the purpose of the experiment is. For example, it is not mentioned that developmental movies were recorded for the data related to Figure 3 to calculate folding, while bleaching was measured in the movies related to Figure 4. In contrast to simple single time points in Figures 1 and 2.

Minor comments:

1. Please add time to movie 2 and rotate it such that anterior is to the left and dorsal it up.
2. Lines 141 - 144 should refer to Figure 3D not 4D.
3. Movies 3 and 4, please insert time.

Significance

Experiments are well performed and the finding are useful to guide the future choice of fluorophores in Drosophila and possibly other model organisms. Results are not very surprising, as the major finding that StayGold is photostable (but not the brightest) is not entirely new but still reassuring. It is particularly nice to have the differences confirmed by well controlled side-by-side measurements in Drosophila. This will likely guide many Drosophila researchers to tag their favourite protein with StayGold in the future.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This is an outstanding study of high practical value, which provided the systematic performance evaluation of in vivo fluorophores under the same condition in the field of Drosophila developmental biology. By site-integrating 17 green and red fluorescent proteins into the same genomic locus and evaluating their fluorescent intensity (early/late embryos), folding time and photostability on the same imaging platform, this provides a powerful database for researchers.

Major comments:

Q1: All fluorescent proteins are fused with histone H2Av. Will this nuclear localization expression pattern mask the performance differences of fluorescent proteins in other subcellular structures (such as cell membranes, cytoplasm, and cytoskeleton)?

Q2: How do the authors ensure precise developmental synchrony among different embryos to avoid the influence of developmental time differences on fluorescence intensity and folding curves?

Q3: In this study, the authors conduct a quantitative screen of nine green and eight red fluorophore lines in Drosophila. A logical and valuable extension of this work would be a systematic evaluation of newer fluorescent proteins, including promising candidates like mBaoJin, mScarlet3, and mScarlet3-H.

Q4：The study does not discuss the potential for fluorescent proteins to interfere with biological function. Although the proteins were expressed from the identical genomic location, variations in their size, structure, or fusion design may influence the target protein's localization or activity.

Lines 145-147 "The only profile that did not fit well to this phenomenological function was mStayGold which did not display a clear reduction in its rate of intensity increase". What is the reason that causes mStayGold to fail to fit well? Is it related to the unique structure?

Lines 154-156 "For the red fluorophores, the intensity profiles were more varied (Fig. 3E). They could not be reduced to a single curve, unlike the green fluorophores (Fig. S7B). The phenomenological function I(t) did not fit the curves well". Compared with green fluorophores, the intensity profiles of red fluorophores vary greatly, what's the major factors drive this difference?

Lines 206 "Fluorophores including mEGFP and mEmerald displayed a secondary peak in intensity around an hour after experiment initiation. This is consistent with a change in the rate of protein production". What is the mechanism behind the secondary peak, and why is it distinctly observed only in mEGFP and mEmerald?

Minor comments:

Line 143 "curve I(t) = I0 tanh (t-tin/ts) (Fig. 4D, Methods)". It's not Fig. 4D, but Fig. 3D.

Line 145 "time is smallest for Superfolder GFP and longest for mNeonGreen (Fig. 4D)". Not Fig. 4D, but Fig. 3D.

Line159 "mScarlet" must be replaced with "mScarlet-I".

Significance

The systematic performance evaluation of in vivo fluorophores under the same condition will give a comprehensive guidence when choosing fluorescent proteins in the field of Drosophila developmental biology.

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Reply to the reviewers

Manuscript number: RC-2025-03195R

Point-by-Point Response to Reviewers

We thank the reviewers for their thoughtful and constructive evaluations, which have helped us substantially improve the clarity, rigor, and balance of our manuscript. We are grateful for their recognition that our integrated ATAC-seq and RNA-seq analyses provide a valuable and technically sound contribution to understanding soxB1-2 function and regenerative neurogenesis in planarians.

We have carefully addressed the reviewers' major points as follows:

1. Direct versus indirect regulation by SoxB1-2:____ In the revision, we explicitly acknowledge the limitations of inferring direct regulation from our current datasets and have revised statements throughout the Results and Discussion to emphasize that our findings are correlative.
2. Evidence for pioneer activity:____ Although the pioneer role of SoxB1 transcription factors in well established in other systems, we agree that additional binding or motif data would be required to formally demonstrate SoxB1-2 pioneer function. Accordingly, we performed motif analysis and revised the text throughout to frame SoxB1-2's proposed role as consistent with, rather than demonstrating transcriptional activator activity.
3. Motif enrichment and downstream regulatory interactions:____ In response to Reviewer #1's suggestion, we have included a new motif enrichment analysis in the supplement to contextualize possible co-regulators within the SoxB1-2 network.
4. Data reproducibility and peak-calling consistency:____ We have included sample correlations ____and peak overlaps for ATAC-seq samples in the revision, providing a clearer assessment of reproducibility.
5. Clarification of co-expression and downstream targets:____ We included co-expression plots for soxB1-2 with mecom and castor in the supplemental materials. These plots were generated from previously published scRNA-seq data and demonstrate that cells expressing soxB1-2 also express mecom and __ __We appreciate the reviewers' recognition that our methods are rigorous and our data accessible. We have incorporated all major revisions suggested and believe have strengthened the manuscript's precision, interpretations, and conclusions. Below, we respond to each comment in detail.

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

Summary

The authors of this interesting study take the approach of combining RNAi, RNA-seq and ATAC-seq to try to build a regulatory network surrounding the function of a planarian SoxB1 ortholog, broadly required for neural specification during planarian regeneration. They find a number of chromatin regions that differentially accessible (measured by ATAC-seq), associate these with potential genes by proximity to the TSS. They then compare this set of genes with those that are differentially regulated (using RNA-seq), after SoxB1 RNAi mediated knockdown. This allows them the authors some focus on potential directly regulated targets of the planarian SoxB1. Two of these downstream targets, the mecom and castor transcription factors are then studied in greater detail.

Major Comments

I have no suggestions for new experiments that fit sensibly with the scope of the current work. There are other analyses that could be appropriate with the ATAC-seq data, but may not make sense in the content of SoxB1 acting as pioneer factor.

I would like to see motif enrichment analysis under the set of peaks to see if SoxB1 is opening chromatin for a restricted set of other transcription factors to then bind. Much of this could be taken from Neiro et al, eLife 2022 (which also used ATAC-seq) and matched planarians TF families to likely binding motifs. This could add some breadth to the regulatory network. It could be revealing for example if downstream TF also help regulate other targets that SoxB1 makes available, this is pattern often seen for cell specification (as I am sure the authors are aware). Alternatively, it may reveal other candidate regulators.

Thank you for this suggestion. We agree with the reviewers that this analysis should be done. We ran the motif enrichment analysis using the same methods as outlined in Neiro et al. eLife, 2022. We have included a new motif enrichment analysis in the supplement to contextualize possible co-regulators within the SoxB1-2 network.

Overall peak calling consistency with ATAC-sample would be useful to report as well, to give readers an idea of noise in the data. What was the correlation between samples?

__Excellent point. In response to this comment, we ran a Pearson correlation test on replicates within gfp and soxB1-2 RNAi replicates to get an idea of overall correlation between replicates. Additionally, we calculated percent overlap of peaks for biological replicates and between treatment groups. __

While it is logical to focus on downregulated genes, it would also be interesting to look at upregulated genes in some detail. In simple terms would we expect to see the representation of an alternate set of fate decisions being made by neoblast progeny?

This is also an important point that we considered but initially did not pursue it due to the lack of tools to test upregulated gene function. However, the reviewer is correct that this is straightforward to perform computationally. Thus, we have performed Gene Ontology analysis on the upregulated genes in all RNA-seq datasets (soxB1-2 RNAi, mecom RNAi, and castor RNAi). Both mecom and castor datasets did not reveal enrichment within the upregulated portion of the dataset. Genes upregulated after soxB1-2 RNAi were enriched for metabolic, xenobiotic detoxification, potassium homeostasis, and endocytic programs. Rather than indicating a shift toward alternative lineages, including non-ectodermal fates, these signatures are consistent with stress-responsive and homeostatic programs activated following loss of soxB1-2. We did not detect enrichment patterns strongly associated with alternative cell fates. We conclude that this analysis does not formally exclude potential shifts in lineage-specific transcriptional programs, but does support our hypothesis that soxB1-2 functions as a transcriptional activator.

Can the authors be explicit about whether they have evidence for co-expression of SoxB1/castor and SoxB1/mecom? I could find this clearly and it would be important to be clear whether this basic piece of evidence is in place or not at this stage.

We included co-expression plots for soxB1-2 with mecom and castor in the supplemental material. These plots were generated from previously published scRNA-seq data and demonstrate that cells expressing soxB1-2 also express mecom and castor. We have not done experiments showing co-expression via in situ at this time.

Minor comments

Formally loss of castor and mecom expression does mean these cells are absent, strictly the cell absence needs an independent method. It might be useful to clarify this with the evidence of be clear that cells are "very probably" not produced.

We agree that loss of castor and mecom expression does not formally demonstrate the physical absence of these cells, and that independent methods would be required to definitively confirm their loss. In response, we have revised our wording to indicate that castor- and mecom-expressing cells are very likely not being produced, rather than stating that they are absent.

Reviewer #1 (Significance (Required)):

Significance

Strengths and limitations.

The precise exploitation of the planarian system to identify potential targets, and therefore regulatory mechanisms, mediated by SoxB1 is an interesting contribution to the fi eld. We know almost nothing about the regulatory mechanisms that allow regeneration and how these might have evolved, and this work is well-executed step in that direction.

Advance

The paper makes a clear advance in our understanding of an important process in animals (neural specification) and how this happens in the context in the context during an example of animal regeneration. The methods are state-of-the-art with respect to what is possible in the planarian system.

Audience

This will be of wide interest to developmental biologists, particularly those studying regeneration in planarians and other regenerative systems,and those who study comparative neurodevelopment.

Expertise

I have expertise in functional genomics in the context of stem cells and regeneration, particularly in the planarian model system

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

Review - Cathell, et al (RC-2025-03195)

Summary and Significance:

Understanding regenerative neurogenesis has been difficult due to the limited amount of neurogenesis that occurs after injury in most animal species. Planarians, with their adult neurogenesis and robust post-injury response, allow us to get a glimpse into regenerative neurogenesis. The Zayas laboratory previously revealed a key role for SoxB1-2 in maintenance and regeneration of a broad set of sensory and peripheral neurons in the planarian body. SoxB1-2 also has a role in many epidermal fates. Their previous work left open the tempting possibility that SoxB1-2 acts as a very upstream regulator of epidermal and neuronal fates, potentially acting as a pioneer transcription factor within these lineages. In the manuscript currently under review, Cathell and colleagues use ATAC-Seq and RNA-Seq to investigate chromatin changes after SoxB1-2(RNAi). With the experimental limitations in planarians, this is a strong first step toward testing their hypothesis that SoxB1-2acts as a pioneer within a set of planarian lineages. Beyond these cell types, this work is also important because planarian cell fates often rely on a suite of transcription factors, but the nature of transcription factor cooperation has been much less well understood. Indeed, the authors do show that loss of SoxB1-2 by RNAi causes changes in a number of accessible regions of the genome; many of these chromatin changes correspond to changes in gene expression of genes nearby these peaks. The authors also examine in more detail two genes that have genomic and transcriptomic changes after SoxB1-2(RNAi), mecom and castor. The authors completed RNA-Seq on mecom(RNAi) and castor(RNAi) animals, identifying genes downregulated after loss of either factor that are also seen in SoxB1-2(RNAi). The results in this paper are rigorous and very well presented. I will share two major limitations of the study and some suggestions for addressing them, but this work may also be acceptable without those changes at some journals.

Limitation 1:

The paper aims to test the hypothesis that SoxB1-2 is a pioneer transcription factor. Observation that SoxB1-2(RNAi) leads to loss of many accessible regions in the chromatin supports the hypothesis. However, an alternate possibility is that SoxB1-2 leads to transcription of another factor that is a pioneer factor or a chromatin remodeling enzyme; in either of these cases, the accessibility peak changes may not be due to SoxB1-2 directly but due to another protein that SoxB1-2 promotes. The authors describe how they can address this limitation in the future; in the meantime, is it known what the likely binding for SoxB1-2 would be (experimentally or based on homology)? If so, could the authors examine the relative abundance of SoxB1-2 binding sites in peaks that change after SoxB1-2(RNAi)? This could be compared to the abundance of the same binding sequence in non-changing peaks. Enrichment of SoxB1-2 binding sites in ATAC peaks that change after its RNAi would support the argument that chromatin changes are directly due to SoxB1-2.

We appreciate the feedback and agree that distinguishing between direct SoxB1-2 pioneer activity and indirect effects mediated through downstream regulators is an important consideration. While we did not perform a direct abundance analysis of potential chromatin-remodeling cofactors, we conducted a motif enrichment analysis following the approach of Neiro et al. (eLife, 2022), comparing control and soxB1-2(RNAi) peak sets. This analysis revealed that Sox-family motifs, particularly SoxB1-like motifs, were among the most enriched in regions that remain accessible in control animals relative to soxB1-2(RNAi) animals, consistent with a model in which SoxB1-2 directly contributes to establishing or maintaining accessibility at these loci. We have now included this analysis in the supplemental materials to further contextualize potential co-regulators and transcriptional partners within the SoxB1-2 regulatory network. We agree and acknowledge in the report that future studies assessing chromatin remodeling factor expression and abundance will be valuable to definitively separate direct and indirect pioneer activity.