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Reply to the reviewers

We thank the reviewers for their time and constructive comments on our manuscript.

Reviewer #1 recognizes the importance of the question we address (namely, the early consequences of Wilms' tumour inducing mutations on kidney development in two models for different Wilms' tumour initiating mutations) and provides useful suggestions for improvement of the manuscript.

Reviewer #2 raises the concern regarding the novelty of the study. We appreciate these comments and this implies the necessity of mainly textual changes we have to do to highlight the novel aspects of our study and findings and their significance in the revision of the manuscript.

Reviewer #3 offers a generally positive assessment of the data, while suggesting that the work may be interpreted primarily from a developmental perspective rather than a Wilms' tumour-focused one. In the revision there is need to better emphasize how these perspectives are closely interconnected in the context of Wilms' tumour biology.

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

This manuscript addresses an important gap in Wilms tumor (WT) biology: what are the earliest pathogenic events following WT driver mutation induction, and how do these early developmental trajectories differ across genotypes? The authors provide a carefully staged and comparative analysis of two WT-associated genetic contexts-conditional Wt1 loss (using lineage-specific Cre drivers targeting nephrogenic (Six2-Cre) versus stromal (Foxd1-Cre) compartments, as well as a temporally controlled Wt1CreERT2 model targeting both lineages upon tamoxifen induction) and inducible LIN28B overexpression, and relate the resulting developmental phenotypes to two CSC marker paradigms derived from patient-based studies. A major strength is the precise, time-resolved description of the earliest initiating phenotypes (E12.5 and E18.5, with additional postnatal analysis for LIN28B) and the direct side-by-side comparison of how each genotype perturbs nephrogenesis. The authors conclude that Wt1 loss (especially in the nephrogenic lineage) leads to a severe developmental block accompanied by a disturbance of lineage identity ("lineage confusion"), whereas LIN28B overexpression causes a disturbed transition between uninduced and induced nephron progenitor cell (NPC) states, producing blastemal-like regions that persist postnatally. Using immunostaining for NCAM1, SIX2, CITED1, and ALDH1A2, the authors map marker combinations during normal kidney development and across mutant contexts, and propose that tumor-initiating alterations, most clearly in the LIN28B model, and more suggestively in the Wt1CreERT2 (Wt1CE) context, promote the emergence of a CSC-like population inferred to co-express all four markers (NCAM1+SIX2+CITED1+ALDH1A2+), a state not observed in normal kidneys.

We thank Reviewer #1 for this correct and complete summary of our manuscript. This reviewer recognizes the current gap in our understanding of the origins of Wilms' tumors and appreciates the approach we have chosen to start filling this gap using two different mouse models.

Overall, this study provides a particularly clear direct comparison of the earliest tumor-initiating events triggered by distinct WT-relevant driver alterations. While the manuscript does not yet offer a detailed molecular mechanistic framework explaining why these two mutations produce such divergent developmental and marker-state outcomes (which would further strengthen the work), the careful comparison and the conclusions drawn from it are meaningful and make an important contribution to our understanding of the developmental processes that can lead to Wilms tumor initiation.

We thank this reviewer for recognizing the importance of a direct comparison of the early consequences of two different Wilms' tumour mutations. We agree we do not yet provide a mechanistic framework for these differences. Although these studies are on-going, they are outside the scope of this manuscript.

*Major comment: 1. A central and highly emphasized conclusion of this manuscript is that tumor-initiating alterations induce a CSC-like population co-expressing all four markers (NCAM1, SIX2, CITED1, and ALDH1A2), and that this state is not observed during normal kidney development. Because this "quadruple-positive" population is a key mechanistic take-home message and closely linked to the overall conceptual model, the manuscript would be substantially strengthened by a direct, same-cell demonstration of co-expression of all four markers, rather than inference from consecutive sections. The authors state that they were unable to do so due to a technical limitation, namely, antibody host-species constraints that prevent co-detection of CITED1 and ALDH1A2 within the same section. *

We agree that not being able to show co-expression of all 4 CSC markers is a serious limitation for the interpretation of our data. The reviewer suggests the following alternatives:

*Several feasible approaches could address this limitation for example: - Identify an alternative antibody reagent from a different host species. *

The 'problematic' antibodies are the ones staining for ALDH1A2 and CITED1, which are both Rabbit IgG. Alternative antibodies for ALDH1A2 are all raised in rabbit, so these will not solve this problem. For CITED1 we have now identified a biotin-conjugated antibody which could be used in additional co-staining. We propose to test this antibody for the revision of this manuscript.

*- RNAscope / smFISH for in situ single-cell co-detection. *

We are aware of these techniques as alternative for antibody staining. However, we have no experience with these techniques, nor do we have access to the required technologies. After discussions with collaborators with much experience in this technique, we realized the combination of the potential extensive optimization and costs does not make this a suitable alternative for the limited samples we have available.

*- Single-cell RNA-seq (scRNA-seq) to test whether a bona fide quadruple-positive transcriptional state exists. *

This could be an option but is itself a huge project and therefore outside the scope of this manuscript. We note that the known scarcity in single cell data might still complicate the detection of each marker in individual cells, especially for low-expressed TFs like Six2 and Cited1.

*Overall, resolving this technical limitation would markedly increase confidence in one of the manuscript's most important claims and strengthen the proposed genotype-phenotype/CSC-marker framework

*

_As discussed above, we propose the t_ry the biotin-conjugated CITED1 antibody__

• It is somewhat unexpected that the Six2-specific Wt1 deletion appears to produce a more severe phenotype than the tamoxifen-inducible Wt1CreERT2 approach, which is intended to target a broader Wt1-derived lineage (both nephrogenic and stromal). The Discussion offers several plausible, non-mutually exclusive explanations for this observation (e.g., timing, recombination efficiency/mosaicism, and the rescue contribution of "escaping" wild-type cells). It would be helpful to support at least one of these explanations experimentally. For example, the authors could quantify the extent of "escape" (percentage of non-recombined cells within the lineage) across embryos/timepoints to validate that mosaicism is indeed the cause of the milder phenotype. *

We can address this experimentally by making use of the tdTomato Cre reporter that was included in our model which allows us to follow the fate of mutated and non-mutated cells in the lineage. We propose to combine Six2 antibody staining with the tdTomato signal to quantify the percentage of cells that has maintained Six2 expression and is therefore likely an escaping cell/nephron.

Minor comments 1. Please clarify whether the difference shown in Fig. 2C is statistically significant, and report n, error bars/variation, the statistical test used, and p-values (if applicable).

These details will all be added.

• The authors note the presence of some SIX2+; tdTomato+ cells in Foxd1GC control kidneys. Given the expected stromal restriction of Foxd1 lineage labeling, please clarify the likely explanation and, if possible, indicate how frequent this is.

*

The reviewer here points to the important question regarding the origin and potential overlap between the stromal and nephrogenic lineages. This is not only an important but highly relevant question for origin and biology of Wilms' tumours, but also for normal kidney development. Kobayashi et al (2014) reported some contribution of the Foxd1 lineage in the Six2 lineage. Also Magella et al (2018) found some signs for this, as did a recent pre-print (Haghighitalab et al. 2026). There is even data suggesting that (part of) the renal stromal is derived from the paraxial instead of intermediate mesoderm in chicken (Guillaume et al. 2009) with some supportive data from mouse development as well (Levinson et al. 2005). The latter is especially interesting given the commonly found ectopic muscle differentiation in WT1-mutant Wilms' tumours (Miyagawa et al. 1998; Schumacher et al. 2003; Gadd et al. 2012). However, if a common, potentially Foxd1+/Six2+ double positive, progenitor exists, it will in the normal developing kidney be present before E11.5 and therefore the data in our current manuscript, or the unpublished scMultiome data, is not informative for this. We propose to discuss this in detail in the Discussion of the manuscript, and speculate on its relevance for Wilms' tumours.

It is somewhat unexpected that Six2-specific Wt1 deletion appears to produce a more severe phenotype than the tamoxifen-inducible Wt1CreERT2 approach, which is intended to target a broader Wt1-derived lineage. The Discussion offers several plausible, non-mutually exclusive explanations (e.g., timing and/or recombination efficiency/mosaicism and the contribution of "escaping" cells). it would be helpful to support at least one of these explanations experimentally, for example by quantifying the extent of "escape" across embryos/timepoints and tamoxifen dosing.

This was addressed above.

*4. A careful proofreading pass is needed to ensure text-figure consistency, particularly for arrow annotations. For example, the Results text refers to "Fig. 1F, arrows," but arrows are not apparent in that panel. Likewise, the Results text mentions a "white filled arrow" in Fig. 2H, whereas the figure appears to show only open arrows. Please align the wording with the annotations actually shown in the figures. *

We apologize for these errors and thank the reviewer for pointing them out. These, and all other textual and graphical errors, will be corrected in the new version of the manuscript.

__Reviewer #1 (Significance (Required)): __

Overall, this study provides a particularly clear direct comparison of the earliest tumor-initiating events triggered by distinct WT-relevant driver alterations. While the manuscript does not yet offer a detailed molecular mechanistic framework explaining why these two mutations produce such divergent developmental and marker-state outcomes (which would further strengthen the work), the careful comparison and the conclusions drawn from it are meaningful and make an important contribution to our understanding of the developmental processes that can lead to Wilms tumor initiation.

We thank the reviewer for this comment, and like to emphasize that this is precisely the scope we intended with the current manuscript.

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

*Wilm's Tumor, a pediatric kidney cancer, is associated with gain or loss of activity of a number of genes including the loss of activity of the nucleic acid binding protein WT1 and gain of activity (enhanced expression at the mRNA level) of the RNA binding protein Lin28 which negatively impacts the maturation of the miicroRNA let-7, elevating levels of let-7 targets. Previous mouse studies have examined the impact of loss of Wt1 throughout within the nephron progenitor and interstitial cell compartments in capping mesenchyme that is thought to be the source of the tumor and of broad elevated expression in all kidney progenitors. *

*In this manuscript, the authors have refined the loss of Wt1 to nephron or stromal progenitors and compared the phenotype to loss of Wt1 in both lineages examining cultured kidneys over a 72 hr period, in addition to uncultured kidneys examined at e18.5. A similar analysis was performed on Lin28 mutants. The analysis itself consisted of video imaging, limited immunostaining and histochemistry. *

Reviewer #2 provides, in our opinion, a very limited overview of the contents of our manuscript. Our work presented here shows:

• A detailed analysis of effects of Wt1 loss or activation of LIN28B in the following systems:
• 5 embryonic kidneys
• 5 embryo kidneys
• P19 postnatal kidneys (for the LIN28B model)
• In vitro cultured kidneys.

• Time-laps analysis of in vitro cultured kidneys

• In the case of the Wt1 knockout this was studied in nephrogenic, stromal, and the combination of nephrogenic and stromal lineages

• Whereas our previous work (Berry et al. 2015) focused on different stages of nephron development, we now focus on the different lineages.
• For the first time we study the different marker sets for Wilms' tumour cancer stem cells in their developmental context. Important take-home messages for this are:
• The two published maker sets behave different in the normal developing kidney, and no cell types or developmental stages exist in the normal developing kidney that expresses all four markers

• In contrast, after either of the two Wilms' tumour mutations are induced, we have strong, though not yet conclusive, evidence that this event induces cells that are positive for all four CSC markers, suggesting these quadruple-positive cells could be the functional CSCs. This mutation-dependent appearance of the CSCs would be a complete different mechanism for the origin of CSCs than believed for, for instance, leukemia and colorectal cancer, where an existing cell type with stem- or progenitor cell characteristics which already express the CSC markers picks up the tumour initiating mutations and thus starts behaving as CSC. The cascade our data suggests for the Wilms' tumour CSCs is much more complex.

• To our knowledge this is the first direct and side-by-side comparison of the early effects of different Wilms' tumour mutations. This analysis clearly shows the differences in underlying biology for these two situations, and this can have important consequences for interpretation of patients data (which was historically almost always generated without knowing the initiating mutation) and opens the possibility of mutation-specific therapeutic possibilities and requirements. This is funcamentally different from the current patient stratification based on clinical outcome (favorable vs non-favorable histology) or very general molecular markers with clear biological consequences (like chr 1p status).

• With respect to the mutation-dependent accumulation of CSC markers, although in both Wt1 and LIN28B models this seems to be happening, for the LIN28B model this seems to be the result of a simple developmental block, whereas for the Wt1 mutants this appears to be a lineage conversion phenotype. This is again something that has to our knowledge never been suggested for the origin of CSCs and even in the context of normal kidney development is almost unprecedented.
• We optimize the use of the Wt1CreERT2 driver to target different lineages in the developing kidney using different timepoints for tamoxifen treatment. Not only does this have technical use, it also illustrates the complex role of Wt1 in the earliest stages of kidney development.

Although the data presented are descriptive and do not yet provide a complete molecular mechanism, we believe they offer novel, unexpected and important insights that merit publication. We acknowledge that these aspects may not have been sufficiently clear in the original version of the manuscript, and therefore not being picked up by the reviewer. In response to Reviewer #2 comments, we propose a thorough rewrite of the Discussion of the manuscript to emphasize these aspects more.

*While wholly qualitative and largely observational and descriptive, the limited data are of good quality and the conclusions drawn are reasonable. *

We thank the reviewer for their compliments on the quality and conclusions of the data. While we acknowledge the reviewer's characterization of the study as quantitative and descriptive, we respectfully do not consider this to diminish its suitability for publication. We believe the dataset provides substantial and meaningful insights (definitely not limited), and we have clarified and expanded upon the novel aspects and significance of our findings as outlined above.

*For the Wt1 study, most interesting would be in the loss of Wt1 from the NPC lineage. Clearly, there is already a significant phenotype at the time of study (E12.5) hence there is no strong insight into the earliest effects of Wt1 loss and how this might contribute to tumor formation. Quite what happens to these cells phenotypically is unclear given the limited set of markers used to look at the cells. Specific removal of Wt1 from the stromal lineage generates a milder phenotype, indicating a role for Wt1 there, but without a mechanistic analysis of the resultant products, the underlying mechanisms remain unclear. *

As discussed in our response to reviewer #1, we agree on the lack of mechanism in the current study but emphasize here as well that although this is the topic of the on-going follow-up studies this is outside the scope of the current manuscript. We refer to the same response for our proposal for additional experiments for the revised version of the manuscript.

*Wt1 removal from both lineages generated a phenotype less severe than removal from nephron progenitors (and previous data on "double lineage removal" with a Nestin1 cre), an indication that the genetic approach was not up to the task. *

Respectfully, we would like to emphasize the practical challenges associated with the use of genetically modified mouse models for developmental (and other) studies. We doubt there are many Cre drivers that do exactly what they were intended to do, do only that, and at full 100% efficiency. Many Cre drivers are, when originally described, only described for the cell type they were intended for, and any other activities or limitations are missed or ignored. One could rightfully argue that is bad science, but unfortunately this is often the reality and the starting point for many in vivo analyses. And these are only the complications regarding the behaviour of the Cre driver, and does not even touch on issues like the biological processing of tamoxifen, and the stability of already existing mRNA and protein of the gene of interest in the context of, in this case, a rapidly developing organ. Simply dismissing technical complications as 'not up to the task' is in our opinion not the way forward for studying the origin of diseases.

What is important, and what we demonstrate, is the realization of the limitations of a system, test them and where possible take them into account in the interpretation of data. In this case, instead of hiding the incompleteness of the Cre activity, we actually demonstrate this using retained staining of Wt1 and discuss this in the context of the different phenotypes. We have carefully tried not to overinterpret our data, and note that this reviewer does not give any specifics where this could be affecting our manuscript.

We also like to stress that in the context of Wilms' tumour development the incomplete activity of this Cre driver could even increase the relevance of this model, since the early stages of Wilms' tumourigenesis in the (future) patient happen in a few mutant cells in the context of a further normal developing kidney. The effect of the normal cells in our model that we speculate about could also be important in the patient, we just don't have the technical possibilities to test this yet.

*In some sense, one could regard this work as a pilot study, looking to optimize expensive and time-consuming mouse experiments to maximize insight (ie choose optimum model, address most informative time points, decide on analytical approaches). As a stand-alone paper, the work may not significantly advance our understanding of the topic. *

As argued above, in our opinion this does not do justice to the work we describe in our manuscript.

For example, can simple loss of Wt1 tells us anything about Wt? Yes Wt1 is lost in a subset, but even in these there are additional genetic mutations.

Of course even in WT1-mutant tumours there will be additional mutations found in the tumour. In fact, it has been known for a long time that WT1-mutant Wilms' tumours select for oncogenic mutations in β-catenin with a surprising preference for specific mutations affecting Ser45. However, it is clear that in these tumours the loss of WT1 is the first, rate-limiting step (Fukuzawa et al. 2004; Li et al. 2004; Zirn et al. 2006; Uschkereit et al. 2007). These β-catenin mutations are selected for in an already WT1-mutant context. If we want to understand the full biology of the WT1 mutant tumours including the β-catenin mutation, we will first need to understand the effect of only losing WT1 because that is what provide the selective pressure for the next step (oncogenic mutation in β-catenin). The work described here is an essential first step in that.

• For Lin12, there is no significant advance beyond the studies of the Daly lab. *

As argued above, this is not correct. The following aspects were not covered in the original paper describing this model:

• The in vitro analysis of control and LIN28B embryonic kidneys, including the time-lapse analysis demonstrating how the phenotype develops over time
• The expression of the Wilms' tumour cancer stem cell markers and how these change as a result of the LIN28B activation
• The direct comparison to the Wt1 loss phenotypes, and the demonstration these different mutations lead to fundamentally different biological phenotypes despite both eventually being classified as Wilms' tumours.

  I have no useful suggestions for improvement which would require a completely different approach to the problem from the start.

We respect this reviewer's opinion, but based on the above we do not agree and maintain a different interpretation.

Reviewer #2 (Significance (Required)):

*The authors set out the goal in the introduction - to obtain a better understanding of the origins of Wilm's tumor. There doesn't appear to be an insight of cancer relevant significance beyond earlier studies. *

Our work studies the very first steps in the development of Wilms' tumours. It will never be possible to study this in the (future) patient as these happen around wk 8-10 of pregnancy. By instead analyzing this in mouse models we show fundamental biological differences between different Wilms' tumour inducing mutations which is for sure relevant for patients, the interpretation of patient data (or more the difficulties with interpreting patient data if the initiating mutation or tumour class is not known). Moreover, the data provides new insights in the Wilms' tumour cancer stem cells, a preferred target for any therapy, and suggests the combination of all four known markers might be required to identify and study the true WT CSC. In our opinion such findings provide extremely relevant insights for the field.

*To a readership now/too used to analysis at genome scales (genomic, transcription), this study might appear modest. *

While we agree that genome-wide approaches can provide valuable insights, this doesn't mean that work that doesn't use them cannot provide important insights nor does it mean that every piece of work that does use them provides any new insights. We respectfully emphasize that the merit of a study should be assessed based on the data presented and their interpretation, rather than on the techniques that were used to obtain them.

The target audience is unclear.

Our target audience for this manuscript is everybody who is interested, for whatever reason, in the biology of Wilms' tumours.

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

*Wilms tumor arises from disrupted kidney development. Progenitor-like populations and cancer stem cell (CSC) fractions have been described in patient tumors, but how specific mutations alter embryonic programs to generate these states remains unresolved. *

*Pop et al. model genotype-phenotype relationships during kidney embryogenesis. Using Six2- and Foxd1-driven Cre lines, they test the effects of Wt1 loss-of-function and Lin28b gain-of-function in nephron and stromal progenitors. Through explant imaging, histology, and immunofluorescence, they define mutation-specific effects on ureteric branching, cap mesenchyme organization, stromal composition, and nephron differentiation. *

*Lineage-restricted Wt1 deletion produces distinct outcomes depending on whether nephron progenitors, stromal progenitors, or both are targeted. Lin28b overexpression causes delayed nephrogenesis and lobular organization resembling human Wilms tumor morphology, with expansion of blastemal-like populations. *

This is a correct summary of this part of our data.

These genetic removals of Wt1 and overexpression of Lin28b are useful for the field in understanding where and how Wt1 functions and whether Lin28b could be a model for Wilms' tumor.

We agree that our data on Wt1 loss focusses on the role of Wt1 in normal kidney development, how its loss disrupts normal kidney development and how this could be important for Wilms' tumourigenesis. This includes but goes beyond being only relevant for the function of Wt1, it informs on the biology of WT1-mutant Wilms' tumours.

There is in our mind no doubt whether the LIN28B model is a model for Wilms' tumours. Activating mutations in LIN28B are found in human patient tumours, and already in the original publication of this model (Urbach et al. 2014) it was convincingly shown that the phenotype in the kidneys after less than 3 weeks (when the animals have to be culled animal welfare reasons) represents early stages of Wilms' tumours. Our data presented here confirms this, and extends it with respect to the behavior of the CSC markers and the comparison to the Wt1 loss phenotypes.

Whether the use of previously defined markers NCAM and Aldeflour serve the authors well or is a distraction is to be determine but it is unclear how useful these have been for understanding WT biology thus far. The authors describe these in the developing kidney in explants and in vivo.

*Overall, the data support the view that distinct mutations generate different forms of lineage derailment but it is unclear how this links to Wilms tumor. It is better suited to dsescribe the role of an interesting protein Wt1 in kidney development and lineages therein. Connecting it to tumor biology would require further scrutiny of tumors. *

Since CSCs are, according to the cancer stem cell model, the cells in a tumour that should preferentially be targeted, the exact identification of the CSC markers is directly important for the treatment of tumours. Our data analyzes two different sets of CSC markers, we show these cells label non-overlapping cell types in the normal kidney but that after mutation induction their expression changes and potentially become co-expressed in a single cell type (see our response to Reviewer #1 for more details on this). Identifying the developmental origins of CSCs in a tumour that is the direct result of disturbance of normal embryonic development (Hohenstein et al. 2015; Li et al. 2021) can be used as an entry point into understanding the biology of these tumours. Based on this we argue that although our analysis is on embryonic kidneys, their implications are highly relevant for the actual tumours and their treatment. We propose to further emphasize this in the Introduction and Discussion of our manuscript.

*The study shows that removal of Wt1 in the stromal compartment has distinct phenotypes, which could be important for Wilms tumor biology as this is an poorly understood part of this tumor. *

As already discussed in our response to Reviewer #1, we agree this is a potential important and poorly understood part of Wilms' tumours, directly for WT1 mutant tumours which are stromal-predominant, but potentially also for other tumours. We propose to further address this in the Discussion of the manuscript.

*Major comments: *

1. • This manuscripts uses elegant genetics to scrutinize the role of Wt1 and Lin28b. These stand out as difficult to conduct experiments and are of high value. *

We thank this Reviewer's appreciation for the design, challenges and value of our data.

In contrast, the section on ALDH1A2 and ALDEFLUOR activity is less integrated with the developmental framework.

We discussed our reasons for focusing on the normal developmental context of the cells expressing the CSC markers in the previous section. Since the originally described CSC marker was activity for the AldeFluor enzymatic assay (Pode-Shakked et al. 2013) which we could not use on sections or kidney rudiments, we had to conclusively identify which ALDH isozyme is responsible for this signal in this context. There is much inconsistency about this in the literature, and whichever isozyme is important in these tumours might not be the causative factor in other tumours where AldeFluor labels the CSCs. We therefore use previously published microarray data from the group that originally identified the NCAM1/ AldeFluor combination as Wilms' tumour CSCs to identify ALDH1A2 as the culprit in this cancer type. With this knowledge we could move our analyses to antibodies, allowing co-staining with the other markers. Note that if the signal in these CSCs would have been the result of ALDH1A1 or ALDH1A3 which we show are expressed in the developing ureteric bud, the implications of this for the biology of the tumours would be totally different. We propose to discuss this aspects and its importance in more detail in the revised manuscript.

*Much is unclear here e.g, antibody validation, rationale for performing these assays in explants rather than in vivo tissue, and the shift in Aldh1a2 staining pattern between E12.5 and E18.5, including reported nuclear localization.

*

We need to correct the reviewer on this remark, part of our data is using in vivo samples (E12.5 and E18.5) as well as cultured kidney rudiments. We will clarify which technique we use in the legends of the figures. We prefer to use this combination of techniques for several reasons: 1) the additional 3D information obtained from kidney rudiments can help with identifying specific developmental stages in the developing kidney; 2) due to the different fixation more antibodies work reliably in cultured rudiments than on paraffin frozen sections; 3) this is an important extra factor in the validation of antibodies; and 4) the possibility of culturing kidney rudiments on a time-lapse imaging system allows us to study phenotypes over time (this also greatly reduces the number of animals we need to study multiple timepoints in a developing system, an important aspect for the 3Rs). A good example of this in the timelapse data shown for the nephrogenic Wt1 knockout. The extreme outwards migration of the mutant cells (we show this using the tdTomato reporter) could only be identified in timelapse experiments, but is fully consistent with the sections of the corresponding E12.5 and E18.5 in vivo sections.

We have no explanation for the shift to nuclear localization for ALDH1A2. We are not aware of any other publications showing this. We cannot rule out this is a technical artifact but based on all other expression data obtained with this antibody and their consistency with other publication we don't think this is very likely.

*It is unclear how the manuscript is strengthened by this component. NCAM1 is referenced in the context of Wilms tumor CSCs, but unlike the rest of the manuscript which is mechanistic, it is unclear whether NCAM1 represents a mechanistic node in tumor initiation or merely a surface marker used for cell isolation? If NCAM1 functions just as a proxy for a progenitor-like state rather than a driver of tumor biology surely Wilms tumors will be full of progenitors or blastemal cells and many surface markers. It is unclear what strong evidence shows NCAM1 to be useful, this distinction should be stated. *

Cancer stem cells are defined based in functional characteristics, i.e. the capability of reconstituting a complete tumour with all of its complexity after transplantation in immune-compromised mice. The markers are usually, indeed, merely proxy markers for a specific cell type in the tumour with this functional capacity. The same can be said in this case for the AldeFluor activity, it is used as CSC marker for many cancer types but we are not aware of any data on a functional role for this pathway in any of them. It would be a really interesting experiment to combine our models with an additional conditional knockout for Ncam1 or Aldh1a2 to see if the phenotype we describe here changes. The genetics of such an experiment with so many alleles are however horrendous, would come with an enormous surplus of animals and would take too long for the average project.

The developmental framework presented argues that mutation-specific lineage derailment underlies tumor formation. Marker identity alone does not define pathogenesis. Perhaps reorganize this section to align it with the lineage-confusion model or removing it altogether would make the manuscript punchier?

• *

We propose to rewrite these parts to make this more clear.

• *

• The manuscript is highly focused on the nephrogenic compartment yet removes Wt1 from the stroma as part of one of the main lines of experiments. At several occasions, stromal changes are described qualitatively but using quantitative terms. As such, the manuscript currently comes across as having a bit of a black box where we cannot see the stroma beyond H&E stains. Could there additional antibody stains for stromal markers e.g., Pdgfra, Pdgfrb, or Meis1 to better visualize this compartment and perhaps enable quantification of changes?*

We agree this lack of additional stromal markers is a limitation of the current manuscript. Our reason for so far not including these was our doubts on the usefulness and relevance for the complete renal stroma of many commonly used markers. The scarceness of detailed studies on the developing stroma was a big part of this doubt. Some preliminary tests show that Meis1 is not exclusively found in the developing stroma of the mouse kidney but is also expressed in early stages of the nephrogenic lineage, and is therefore not a good marker for this purpose. Pdgfra and Pdgfrb however seem to be expressed throughout the complete stroma and not in the other lineages. __We propose to analyze these two additional markers for the revised manuscript. __

*Minor comments: *

*Page 4, Lines 89-95: Remove the repeated sentence beginning "Although best known as a transcription factor...". *

*Page 8, Line 164: Arrows referenced in Figure 1F are not visible. *

*Page 8, Lines 164-166: The sentence may refer to Figure 1G; this figure is not otherwise cited. *

*Page 18, Lines 413-414: (Pode-Shakked et al., 2013) is cited twice. *

*Figure 2C: Error bars are missing. Indicate number of biological replicates. *

*Gene nomenclature should be consistent throughout the manuscript. A mouse protein/gene is Six2/Six2. *

*Use precise language when referring to protein detection rather than "expression." *

*Standardize corticomedullary orientation across figures. *

*Page 7, Lines 160-161: Provide immunostaining supporting WT1+/Tdtomato− stromal identity. Co-staining with Foxd1 would clarify lineage assignment. *

*At E18.5 in the Six2-driven Wt1 mutant, WT1 signal is absent despite earlier stromal WT1+ cells. Clarify the fate of these cells. *

*Comment on the lower recombination efficiency observed in Wt1CE at E11.5. *

*Page 14, Lines 321-322: Determine how long CITED1 persists in WTCE mice. Co-staining with later differentiation markers would clarify whether progenitor retention coexists with nephron maturation. *

Page 15, Lines 352-353: Clarify whether the sentence describing blastemal-like regions should reference Figure 5D.

We thank the reviewer for these correction and other minor comments. We will address them in the revised manuscript. With respect to the remark regarding the gene nomenclature, until recently we were also under the assumption that mouse proteins only have the first character as capital. However, to our surprise we recently realized the official mouse nomenclature states that the protein (but not the gene) is in fact in all capitals. We refer for this to section 1.5.2 at https://www.informatics.jax.org/mgihome/nomen/gene.shtml.

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Fukuzawa R, Breslow NE, Morison IM, Dwyer P, Kusafuka T, Kobayashi Y, Becroft DM, Beckwith JB, Perlman EJ, Reeve AE. 2004. Epigenetic differences between Wilms' tumours in white and east-Asian children. Lancet 363: 446-451.

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Guillaume R, Bressan M, Herzlinger D. 2009. Paraxial mesoderm contributes stromal cells to the developing kidney. Dev Biol 329: 169-175.

Haghighitalab A, Nosrati F, Dehghani-Ghobadi Z, Sayed M, Ahn C, Hu Y-C, Chung E, Lim H-W, Park J-S. 2026. A knock-in Six2Cre line reveals transient interstitial potential in nephron progenitors. bioRxiv: 2026.2002.2004.703893.

Hohenstein P, Pritchard-Jones K, Charlton J. 2015. The yin and yang of kidney development and Wilms' tumors. Genes Dev 29: 467-482.

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Krishna A, Meynert A, Dolt KS, Kelder M, Mesropian A, Ewing A, Brouwers C, Claassens JW, Linssen MM, Sheraz S et al. 2026. Mutational scanning reveals oncogenic CTNNB1 mutations have diverse effects on signaling. Nat Genet 58: 366-375.

Levinson RS, Batourina E, Choi C, Vorontchikhina M, Kitajewski J, Mendelsohn CL. 2005. Foxd1-dependent signals control cellularity in the renal capsule, a structure required for normal renal development. Development 132: 529-539.

Li CM, Kim CE, Margolin AA, Guo M, Zhu J, Mason JM, Hensle TW, Murty VV, Grundy PE, Fearon ER et al. 2004. CTNNB1 mutations and overexpression of Wnt/beta-catenin target genes in WT1-mutant Wilms' tumors. Am J Pathol 165: 1943-1953.

Li H, Hohenstein P, Kuure S. 2021. Embryonic Kidney Development, Stem Cells and the Origin of Wilms Tumor. Genes (Basel) 12.

Magella B, Adam M, Potter AS, Venkatasubramanian M, Chetal K, Hay SB, Salomonis N, Potter SS. 2018. Cross-platform single cell analysis of kidney development shows stromal cells express Gdnf. Dev Biol 434: 36-47.

Miyagawa K, Kent J, Moore A, Charlieu JP, Little MH, Williamson KA, Kelsey A, Brown KW, Hassam S, Briner J et al. 1998. Loss of WT1 function leads to ectopic myogenesis in Wilms' tumour. Nat Genet 18: 15-17.

Pode-Shakked N, Shukrun R, Mark-Danieli M, Tsvetkov P, Bahar S, Pri-Chen S, Goldstein RS, Rom-Gross E, Mor Y, Fridman E et al. 2013. The isolation and characterization of renal cancer initiating cells from human Wilms' tumour xenografts unveils new therapeutic targets. EMBO Mol Med 5: 18-37.

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Urbach A, Yermalovich A, Zhang J, Spina CS, Zhu H, Perez-Atayde AR, Shukrun R, Charlton J, Sebire N, Mifsud W et al. 2014. Lin28 sustains early renal progenitors and induces Wilms tumor. Genes Dev 28: 971-982.

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Referee #3

Evidence, reproducibility and clarity

Wilms tumor arises from disrupted kidney development. Progenitor-like populations and cancer stem cell (CSC) fractions have been described in patient tumors, but how specific mutations alter embryonic programs to generate these states remains unresolved. Pop et al. model genotype-phenotype relationships during kidney embryogenesis. Using Six2- and Foxd1-driven Cre lines, they test the effects of Wt1 loss-of-function and Lin28b gain-of-function in nephron and stromal progenitors. Through explant imaging, histology, and immunofluorescence, they define mutation-specific effects on ureteric branching, cap mesenchyme organization, stromal composition, and nephron differentiation. Lineage-restricted Wt1 deletion produces distinct outcomes depending on whether nephron progenitors, stromal progenitors, or both are targeted. Lin28b overexpression causes delayed nephrogenesis and lobular organization resembling human Wilms tumor morphology, with expansion of blastemal-like populations. These genetic removals of Wt1 and overexpression of Lin28b are useful for the field in understanding where and how Wt1 functions and whether Lin28b could be a model for Wilms' tumor. Whether the use of previously defined markers NCAM and Aldeflour serve the authors well or is a distraction is to be determine but it is unclear how useful these have been for understanding WT biology thus far. The authors describe these in the developing kidney in explants and in vivo.

Overall, the data support the view that distinct mutations generate different forms of lineage derailment but it is unclear how this links to Wilms tumor. It is better suited to dsescribe the role of an interesting protein Wt1 in kidney development and lineages therein. Connecting it to tumor biology would require further scrutiny of tumors. The study shows that removal of Wt1 in the stromal compartment has distinct phenotypes, which could be important for Wilms tumor biology as this is an poorly understood part of this tumor. My recommendation is that the manuscript would be considered for a major revision where it is more focused on kidney biology.

Major comments:

1. This manuscripts uses elegant genetics to scrutinize the role of Wt1 and Lin28b. These stand out as difficult to conduct experiments and are of high value. In contrast, the section on ALDH1A2 and ALDEFLUOR activity is less integrated with the developmental framework. Much is unclear here e.g, antibody validation, rationale for performing these assays in explants rather than in vivo tissue, and the shift in Aldh1a2 staining pattern between E12.5 and E18.5, including reported nuclear localization. It is unclear how the manuscript is strengthened by this component. NCAM1 is referenced in the context of Wilms tumor CSCs, but unlike the rest of the manuscript which is mechanistic, it is unclear whether NCAM1 represents a mechanistic node in tumor initiation or merely a surface marker used for cell isolation? If NCAM1 functions just as a proxy for a progenitor-like state rather than a driver of tumor biology surely Wilms tumors will be full of progenitors or blastemal cells and many surface markers. It is unclear what strong evidence shows NCAM1 to be useful, this distinction should be stated. The developmental framework presented argues that mutation-specific lineage derailment underlies tumor formation. Marker identity alone does not define pathogenesis. Perhaps reorganize this section to align it with the lineage-confusion model or removing it altogether would make the manuscript punchier?
2. The manuscript is highly focused on the nephrogenic compartment yet removes Wt1 from the stroma as part of one of the main lines of experiments. At several occasions, stromal changes are described qualitatively but using quantitative terms. As such, the manuscript currently comes across as having a bit of a black box where we cannot see the stroma beyond H&E stains. Could there additional antibody stains for stromal markers e.g., Pdgfra, Pdgfrb, or Meis1 to better visualize this compartment and perhaps enable quantification of changes?

Minor comments:

Page 4, Lines 89-95: Remove the repeated sentence beginning "Although best known as a transcription factor...".

Page 8, Line 164: Arrows referenced in Figure 1F are not visible.

Page 8, Lines 164-166: The sentence may refer to Figure 1G; this figure is not otherwise cited.

Page 18, Lines 413-414: (Pode-Shakked et al., 2013) is cited twice.

Figure 2C: Error bars are missing. Indicate number of biological replicates.

Gene nomenclature should be consistent throughout the manuscript. A mouse protein/gene is Six2/Six2.

Use precise language when referring to protein detection rather than "expression."

Standardize corticomedullary orientation across figures.

Page 7, Lines 160-161: Provide immunostaining supporting WT1+/Tdtomato− stromal identity. Co-staining with Foxd1 would clarify lineage assignment.

At E18.5 in the Six2-driven Wt1 mutant, WT1 signal is absent despite earlier stromal WT1+ cells. Clarify the fate of these cells.

Comment on the lower recombination efficiency observed in Wt1CE at E11.5.

Page 14, Lines 321-322: Determine how long CITED1 persists in WTCE mice. Co-staining with later differentiation markers would clarify whether progenitor retention coexists with nephron maturation.

Page 15, Lines 352-353: Clarify whether the sentence describing blastemal-like regions should reference Figure 5D.

Significance

Overall, the data support the view that distinct mutations generate different forms of lineage derailment but it is unclear how this links to Wilms tumor. It is better suited to dsescribe the role of an interesting protein Wt1 in kidney development and lineages therein. Connecting it to tumor biology would require further scrutiny of tumors. The study shows that removal of Wt1 in the stromal compartment has distinct phenotypes, which could be important for Wilms tumor biology as this is an poorly understood part of this tumor.

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Referee #2

Evidence, reproducibility and clarity

Wilm's Tumor, a pediatric kidney cancer, is associated with gain or loss of activity of a number of gene including the loss of activity of the nucleic acid binding protein WT1 and gain of activity (enhanced expression at the mRNA level) of the RNA binding protein Lin28 which negatively impacts the maturation of the miicroRNA let-7, elevating levels of let-7 targets. Previous mouse studies have examined the impact of loss of Wt1 throughout within the nephron progenitor and interstitial cell compartments in capping mesenchyme that is thought to be the source of the tumor and of broad elevated expression in all kidney progenitors.

In this manuscript, the authors have refined the loss of Wt1 to nephron or stromal progenitors and compared the phenotype to loss of Wt1 in both lineages examining cultured kidneys over a 72 hr period, in addition to uncultured kidneys examined at e18.5. A similar analysis was performed on Lin28 mutants. The analysis itself consisted of video imaging, limited immunostaining and histochemistry.

While wholly qualitative and largely observational and descriptive, the limited data are of good quality and the conclusions drawn are reasonable. For the Wt1 study, most interesting would be in the loss of Wt1 from the NPC lineage. Clearly, there is already a significant phenotype at the time of study (E12.5) hence there is no strong insight into the earliest effects of Wt1 loss and how this might contribute to tumor formation. Quite what happens to these cells phenotypically is unclear given the limited set of markers used to look at the cells. Specific removal of Wt1 from the stromal lineage generates a milder phenotype, indicating a role for Wt1 there, but without a mechanistic analysis of the resultant products, the underlying mechanisms remain unclear. Wt1 removal from both lineages generated a phenotype less severe than removal from nephron progenitors (and previous data on "double lineage removal" with a Nestin1 cre), an indication that the genetic approach was not up to the task.

In some sense, one could regard this work as a pilot study, looking to optimize expensive and time-consuming mouse experiments to maximize insight (ie choose optimum model, address most informative time points, decide on analytical approaches). As a stand-alone paper, the work may not significantly advance our understanding of the topic. For example, can simple loss of Wt1 tells us anything about Wt? Yes Wt1 is lost in a subset, but even in these there are additional genetic mutations. For Lin12, there is no significant advance beyond the studies of the Daly lab.

I have no useful suggestions for improvement which would require a completely different approach to the problem from the start.

Significance

The authors set out the goal in the introduction - to obtain a better understanding of the origins of Wilm's tumor. There doesn't appear to be an insight of cancer relevant significance beyond earlier studies. To a readership now/too used to analysis at genome scales (genomic, transcription), this study might appear modest. The target audience is unclear.

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Referee #1

Evidence, reproducibility and clarity

This manuscript addresses an important gap in Wilms tumor (WT) biology: what are the earliest pathogenic events following WT driver mutation induction, and how do these early developmental trajectories differ across genotypes? The authors provide a carefully staged and comparative analysis of two WT-associated genetic contexts-conditional Wt1 loss (using lineage-specific Cre drivers targeting nephrogenic (Six2-Cre) versus stromal (Foxd1-Cre) compartments, as well as a temporally controlled Wt1CreERT2 model targeting both lineages upon tamoxifen induction) and inducible LIN28B overexpression, and relate the resulting developmental phenotypes to two CSC marker paradigms derived from patient-based studies.

A major strength is the precise, time-resolved description of the earliest initiating phenotypes (E12.5 and E18.5, with additional postnatal analysis for LIN28B) and the direct side-by-side comparison of how each genotype perturbs nephrogenesis. The authors conclude that Wt1 loss (especially in the nephrogenic lineage) leads to a severe developmental block accompanied by a disturbance of lineage identity ("lineage confusion"), whereas LIN28B overexpression causes a disturbed transition between uninduced and induced nephron progenitor cell (NPC) states, producing blastemal-like regions that persist postnatally. Using immunostaining for NCAM1, SIX2, CITED1, and ALDH1A2, the authors map marker combinations during normal kidney development and across mutant contexts, and propose that tumor-initiating alterations, most clearly in the LIN28B model, and more suggestively in the Wt1CreERT2 (Wt1CE) context, promote the emergence of a CSC-like population inferred to co-express all four markers (NCAM1+SIX2+CITED1+ALDH1A2+), a state not observed in normal kidneys.

Overall, this study provides a particularly clear direct comparison of the earliest tumor-initiating events triggered by distinct WT-relevant driver alterations. While the manuscript does not yet offer a detailed molecular mechanistic framework explaining why these two mutations produce such divergent developmental and marker-state outcomes (which would further strengthen the work), the careful comparison and the conclusions drawn from it are meaningful and make an important contribution to our understanding of the developmental processes that can lead to Wilms tumor initiation.

Major comment:

1. A central and highly emphasized conclusion of this manuscript is that tumor-initiating alterations induce a CSC-like population co-expressing all four markers (NCAM1, SIX2, CITED1, and ALDH1A2), and that this state is not observed during normal kidney development. Because this "quadruple-positive" population is a key mechanistic take-home message and closely linked to the overall conceptual model, the manuscript would be substantially strengthened by a direct, same-cell demonstration of co-expression of all four markers, rather than inference from consecutive sections. The authors state that they were unable to do so due to a technical limitation, namely, antibody host-species constraints that prevent co-detection of CITED1 and ALDH1A2 within the same section. Several feasible approaches could address this limitation for example:
   • Identify an alternative antibody reagent from a different host species.
   • RNAscope / smFISH for in situ single-cell co-detection.
   • Single-cell RNA-seq (scRNA-seq) to test whether a bona fide quadruple-positive transcriptional state exists.

Overall, resolving this technical limitation would markedly increase confidence in one of the manuscript's most important claims and strengthen the proposed genotype-phenotype/CSC-marker framework 2. It is somewhat unexpected that the Six2-specific Wt1 deletion appears to produce a more severe phenotype than the tamoxifen-inducible Wt1CreERT2 approach, which is intended to target a broader Wt1-derived lineage (both nephrogenic and stromal). The Discussion offers several plausible, non-mutually exclusive explanations for this observation (e.g., timing, recombination efficiency/mosaicism, and the rescue contribution of "escaping" wild-type cells). It would be helpful to support at least one of these explanations experimentally. For example, the authors could quantify the extent of "escape" (percentage of non-recombined cells within the lineage) across embryos/timepoints to validate that mosaicism is indeed the cause of the milder phenotype.

Minor comments

1. Please clarify whether the difference shown in Fig. 2C is statistically significant, and report n, error bars/variation, the statistical test used, and p-values (if applicable).
2. The authors note the presence of some SIX2+; tdTomato+ cells in Foxd1GC control kidneys. Given the expected stromal restriction of Foxd1 lineage labeling, please clarify the likely explanation and, if possible, indicate how frequent this is.
3. It is somewhat unexpected that Six2-specific Wt1 deletion appears to produce a more severe phenotype than the tamoxifen-inducible Wt1CreERT2 approach, which is intended to target a broader Wt1-derived lineage. The Discussion offers several plausible, non-mutually exclusive explanations (e.g., timing and/or recombination efficiency/mosaicism and the contribution of "escaping" cells). it would be helpful to support at least one of these explanations experimentally, for example by quantifying the extent of "escape" across embryos/timepoints and tamoxifen dosing.
4. A careful proofreading pass is needed to ensure text-figure consistency, particularly for arrow annotations. For example, the Results text refers to "Fig. 1F, arrows," but arrows are not apparent in that panel. Likewise, the Results text mentions a "white filled arrow" in Fig. 2H, whereas the figure appears to show only open arrows. Please align the wording with the annotations actually shown in the figures.

Significance

Overall, this study provides a particularly clear direct comparison of the earliest tumor-initiating events triggered by distinct WT-relevant driver alterations. While the manuscript does not yet offer a detailed molecular mechanistic framework explaining why these two mutations produce such divergent developmental and marker-state outcomes (which would further strengthen the work), the careful comparison and the conclusions drawn from it are meaningful and make an important contribution to our understanding of the developmental processes that can lead to Wilms tumor initiation.

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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:

Building a functional nervous system with the correct number of correctly specified and wired pre- and post-synaptic neurons requires a tight control of proliferation and cell survival during development. Focusing on the latter, Naser Alshami and colleagues in the laboratory of Alicia Hidalgo investigated the role of three neurotrophins and their respective Toll receptors in regulating neuronal survival in the visual system of Drosophila. A combination of expression and genetic loss-of-function and gain-of-function analyses revealed a novel role for the neurotrophin DNT2 (spaetzle-5) in controlling survival, dendritic spine formation, columnar axonal innervation of lamina neuron L1 expressing the receptor Toll-2.

Major comments:

• DNT-2 (spz-5) is described to be expressed in non-neuronal cells in the retina. However, the clustered arrangement of cells in cross-sections of the retina during pupal development (72h DNT-2 bottom panel) suggests that photoreceptors could be labeled by the reporter as well. This should be assessed by co-labeling experiments with Elav and/or mAb24B10. This is important, as photoreceptors may represent a presynaptic additional source of this neurotrophin to lamina neurons L1 (see below).
• The most right hand panel of Figure 2A, first row, Toll-2, does not resemble a 24h APF optic lobe, and would need to be replaced by a correctly staged younger sample. This is relevant, as the image at 48 h APF shows extensive staining in a cluster at the medulla edge, suggesting that expression in medulla neurons may be more abundant at younger stages. The expression of Toll-2 in L3 neurons is not unambiguously demonstrated at the angle shown in Figure 1E first panel. Normally, MCFO clones should be able to reveal single cells instead of L1 and L3 together.
• Related to this part of the study, the authors describe that Toll-2 is expressed by connecting neurons (L1, Mi1, Tm3...). This is solely based on RNAseq data. In the next paragraph, the authors describe that Toll-2 is expressed in L1 and DNT-2 in Mi1 (or related) medulla neurons. However, this is rather vague, as it is not clear what "related" medulla neurons refers to. As expression in Mi1 neurons is at the heart of this study, it would be essential to verify that Mi1 is included in the Toll-2-Gal4 and DNT-2 expression pattern. Indeed, in Figure 1A (right panel, row 2, 48 h APF) expression of DNT-2 in this neuron subtype may be visible. This should be verified by markers and single cell labeling such as MCFO. Finally, the authors mention that the DNT-2 ligand could "reach" the Toll-2 receptor. Here some more precision would be helpful, as it is not clear, how far neurotrophins would need to travel, and synaptic contacts may form too late for mediating survival. Furthermore, there seems to be also the possibility that there is a substantial contribution of autocrine signaling, if L1 neurons indeed express both the ligand and the receptor, which would need to be presented more clearly.
• The next set of experiments uses over-expression of DNT-2 and DNT-3 in Toll-8 expressing neurons and assessment of survival rates in lamina neurons. Survival is determined by evaluating Dcp-1 signals rather than cell numbers. During normal larval development, 7 future lamina neurons per column are formed, two of which are eliminated by apoptosis. Thus, it would be important to verify whether it is these neurons that are surviving, using for instance Elav labeling; moreover lamina neuron specific markers (see Xu et al., 2024) may enable assessment whether the surviving neurons adopt specific lamina neuron identities in excess to the normal 5. It may also need to be considered that both neurotrophins could affect proliferation, if the numbers do not add up (as drivers may be active already during the third instar larval stage, this is possible).
• Gain-of-function experiments are followed by loss-of-function experiments, assessing the impact of loss of DNTs in entire animal mutants on lamina neuron survival. As for the gain-of-function studies, it would be important to know, which lamina neuron subtypes are dying in the absence of DNT-2 and DNT-3. Indeed, Figure 4C reveals a substantial loss of L1 and L3 neurons. The over-expression experiments of the ligands using the Toll-2 driver are complicating matters, considering that the driver line is described to be a mutant in Toll-2, and the ligand is expressed in the same neuron, creating an autocrine signaling situation. Moreover, since Toll-2-Gal4 is used to drive expression in all lamina neurons L1 and L3, and entire optic lobes are assessed, the numbers should be around 1600 in wild type, but are not, suggesting that there might have been some cell death in controls. If there are more lamina neurons in the over-expression situation, it would mean that additional neurons are adopting L1 and L3 identity and thus reveal an additional direct role in cell fate determination by DNT-2 and Toll-2 or an indirect role considering the intricate interactions of lamina neurons to adopt specific identities via N signaling (see Xu et al. 2024). This would need to be assessed more in detail using for instance independent drivers or markers for lamina neuron subtypes.
• The statement, that the remaining signal is coming from macrophages would need to supported by additional markers or described more carefully (as it could be glia).
• Page. 9. The study reports a new interaction between DNT-2 and Toll-2 as its possible receptor. This is in part based on whole animal lethality, without providing quantification. This should be added.
• Interestingly, knock-down of Toll-2 in all neurons led to increased cell death of lamina neurons, which cannot be overcome by over-expression of DNT-2 [FL]. It would be interesting to assess whether cell death is even higher by providing a statistical test comparing the knock-down of Toll-2 with the knock-down of Toll-2 and the simultanous over-expression of DNT-2 in Figure 4B.
• Page 11 (also page 4). The authors describe that "connectivity of lamina neurons to medulla neurons takes place at 30-48 h APF and between medulla and lobula complex at 60-70h APF, and that expression of synaptic markers starts at 24h APF". It is not clear how the authors define connectivity (here and throughout the manuscript). While axonal and dendritic projections are established during the first half of pupal development, functional synapses are thought to be solely established from mid-pupal development onwards (early expression of synaptic markers may not be indicative of synapse formation as early as 24h APF). Moreover, there is no solid evidence yet that connections form sequentially between the lamina and medulla, and medulla and lobula and lobula plate neurons. This description would need to be adjusted. A reference for the occurrence of spontaneous activity (prior to synapse formation) should be provided: Akin et al. 2019. This is important for the subsequent interpretation that cell death overlaps with "connectivity": if this term is used to refer to synapse formation, this may not hold, and need adjustment.
• Next, the study assesses the impact of loss of Toll-2 in surviving lamina neurons L1 on columnar axonal branching. The authors observed that loss of Toll-2 or over-expression of DNT-2 leads to extension of axonal branches into neighboring columns in the medulla neuropil layer M1. Here, it would be important to assess, whether this phenotype is really due to the loss of Toll-2 or the fact that neighboring L1 neurons are missing (even just one neighbor missing may be enough to create this defect as contact-dependent repulsion may no longer work, Millard et al. 2007). Toll-2 MARCM clones would be able to address this point. Without further experiments conclusions need adjustments. Finally, the authors conclude that this is an indication for a role in connectivity, but indeed, it is not clear whether these projections lead to abnormal connections, as the thin projections may not form synapses. This statement would need to be adjusted or supported by including synaptic markers, such as Brp/or TransTango experiments.
• The study concludes with the statement that over-expression of DNT-2 FL and knock-down of Toll-2 alters dendritic spine formation of lamina neurons L1 in the lamina, it increases by over-expression and decreases in Toll-2 knock-down. This is in contrast to the axonal projections, where additional extensions are observed in both genotypes. This should be discussed, as the opposite effects may be in line with an indirect effect through loss of neighbors in medulla columns (in contrast to the lamina).
• The authors conclude in the discussion (page 15 and 17) that DNT-2 by medulla neurons Mi1 or related medulla neurons is key to promoting survival of lamina neurons L1, expressing the Toll-2 receptor. However, the manuscript does not provide any direct evidence that it is indeed Mi1 (or other medulla neurons) playing this role. Considering that DNT-2 may also be provided by photoreceptors (see above), this statement may need support by additional experiments, such as a Mi1 specific or photoreceptor-specific over-expression of DNT-2 in a DNT-2 whole animal mutant background and assessment of survival of labeled L1 neurons (e.g. using the markers Svp/Zfh1 (Xu et al. 2024). Moreover, it would be crucial to indeed determine the time point of when cells are undergoing apoptosis and to assess whether this would coincide with synaptogenesis. Such experiments would allow to comment on a potential retrograde signaling process between connecting neurons.
• The data and molecular and genetic methods are presented in detail in the Material and Method sections, as well as through pertinent supplementary tables. Similarly, the statistical analyses and sample numbers are indicated in the Material and Methods section and related supplementary tables. Table S4 does not indicate genotypes, but short versions of crosses, which should be corrected. Moreover, the list of fly lines seems to miss one line (UAS-mCherry). Concerning the antibody list, sources are not provided (unlike stated in the main text). In the Result section, differences are described simply as statistically significant decreases and increases, however, at times it would be useful to add some indication about the level of differences (percentage or fold times).

Minor comments:

• The figures are informative, however, their orientations are not as indicated horizontal or lateral, but often oblique and not consistent (e.g. Fig 1a, last four panels). This makes comparisons more difficult. The authors could possibly find more suitable optical sections and present images more consistently.
• Please provide the correct reference describing the occurrence of spontaneous activity (Akin et al. 2019).
• The manuscript would be more easily accessible to non-experts, if schematic drawings would be provided (neuron subtypes, model).
• The final paragraph of the discussion about DNT-2 keeping connecting neurons together is not easily understandable, as the term "keeping together" remains undefined.

Significance

As in the vertebrate nervous system, insect nervous systems rely on neurotrophins to control the survival and correct wiring of neurons. This study proposes a model, that advances our understanding as to how a specific neurotrophin, delivered by a post-synaptic neuron, acting via a specific receptor, controls several developmental steps of one of its pre-synaptic partners. The study assessed the expression patterns of three neurotrophins and the Toll receptor family, using the T2A-Gal4 expression system, revealing their dynamic expression in photoreceptors, specific lamina and medulla neurons, as well as tracheae and glia during pupal development. A strength of the study represents the identification of DNT-2 and Toll-2 as interacting partners, which could be assessed by the extensive set of specifically generated reagents for this study (Gal4 drivers and mutants). However, a number of statements may require additional experiments to conclusively support the proposed model, in particular the action of DNT-2 and Toll-2 in Mi1 and L1, respectively. Moreover, it would be important to critically assess the timing of events of cell death, setting up of projection patterns and synapse formation.

Audience: The outlined findings, if strengthened further, will be of interest for scientists studying nervous system development in vertebrates and invertebrates in general, and the action of neurotrophins in particular.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors investigate the role of neurotrophins in development of the Drosophila visual system, where multiple waves of cell death eliminate populations of neurons. Using transgenic reporter lines, the authors examine expression of four spz genes, which encode ligands and four Toll receptor genes in the optic lobe. The authors argue that two of these ligands, spz-3/DNT-3 and spz-5/DNT-2, are expressed in the optic lobe concurrently with a wave of cell death. Through gain- and loss of function studies they argue that DNT-3 promotes survival through Toll-8 whilst DNT-2 promotes survival through novel interactions with Toll-2 (with a focus on the lamina neurons). Finally, the authors argue that DNT-2 and Toll-2 regulate L1 neuron targeting and size.

The involvement of neurotrophins in neuronal apoptosis has not been explored in detail in the visual system, making this a potentially interesting topic. However, there are several issues with the manuscript: The primary concern is that most of the authors' conclusions are not supported by the data presented. Many of the figures are difficult to interpret without the addition of appropriate markers. In addition, there are several inconsistencies both within the manuscript and within the context of existing literature that are not addressed. For example, the authors have not demonstrated that lamina neurons undergo apoptosis. This point is critical, as apoptosis, particularly that likely to be affected by neurotrophic factors, fine-tunes multicolumnar neuron numbers after they establish connections with their partners. On the other hand, unicolumnar neurons such as those in the lamina are not thought to need much fine-tuning because of their unicolumnar status. This distinction is not addressed in the manuscript. At present, the evidence presented does not convincingly support the authors' conclusions, and substantial further work is needed before the claims can be firmly established. Overall, these limit the credibility and significance of this study.

Major comments:

In general, the conclusions drawn about neuropil regions and specific cell identities are not supported by sufficient evidence. Across the figures, the identity of neurons and neuropils remains unclear due to the absence of subtype-specific markers or neuropil labelling that would place the data in the anatomical context of the optic lobe.

(1) The authors claim that spz and Toll genes are differentially expressed in the optic lobe throughout pupal development. However, the data presented do not convincingly support this conclusion. The primary concern is that the Gal4 reporter insertions used to infer gene expression do not match published single-cell transcriptomic datasets (as noted by the authors). This discrepancy calls into question the accuracy of these reporters (or the transcriptomics) and raises uncertainty about which dataset can be trusted. Given that these data are inconsistent, gene expression should be assessed directly by HCR to draw reliable conclusions.

Related comments: The authors claim that spz and Toll genes are expressed differentially in the optic lobe throughout pupal development. However, the characterisation of these expression patterns is lacking in the following aspects: - Time courses are inconsistent and incomplete across the different genes. - The conclusion that DNT-2/3 are expressed concurrently with cell death lacks evidence is not supported: DNT2/3 expression does not appear restricted to a clear time window and without co-staining for apoptotic markers this conclusion cannot be substantiated. - There is insufficient evidence to support the claim that spz-2 is specifically expressed in Mi1 neurons or that Toll-8 is specific to L4/L2. These claims are largely based on the transcriptomics data, which were inconsistent with the reporters in many other contexts. There are no neuron type markers costained to validate this claim. - Sample sizes are too low for some reporter lines (~2-4).

(2) The authors quantified cell death using Dcp-1 signal volume and concluded that overexpression of DNT-2 or DNT-3 reduces cell death, while loss of either increases cell death in the lamina. However, the lamina is not labelled with an appropriate marker, nor are neuropils labelled to make the structure recognisable making it unclear whether this wave of cell death is truly occurring in the lamina. This is a recurring issue throughout the manuscript. Related comments: the reported values for Dcp-1 signal volume differ dramatically between the Gal4 (~40,000) and mutant (~2,000) controls, without an explanation for this discrepancy.

(3) The claim that DNT-2 and DNT-3 promote survival via Toll-2 and Toll-8, respectively, is not sufficiently supported. The authors do not show that manipulation of each ligand specifically affects neurons expressing the relevant receptor. To substantiate this conclusion, the specificity of ligand manipulation should be tested. For example, through compensation experiments or by demonstrating that DNT-2 loss of function specifically induces cell death in Toll-2+ neurons.

(4) The authors further investigate a potential interaction between DNT-2 and Toll-2, concluding that DNT-2 promotes survival in the lamina, medulla, and lobula complex through Toll-2. However, no evidence is presented showing altered levels of apoptosis in the medulla or lobula/lobula plate following DNT-2 manipulation. The conclusion that DNT-2 promotes survival via Toll-2 is based on a Toll-2RNAi;DNT-2FL epistasis experiment, but this interpretation does not account for the reduced expression of each construct due to Gal4 titration. This issue also applies to subsequent experiments (Figs. 5 and 6). A Gal4 titration control is required for each of these experiments to exclude this confound.

(5) The authors conclude that DNT-2 production in Mi1 medulla neurons is required for L1 connectivity, survival, and morphology. However, these conclusions are based on manipulating DNT-2 and Toll-2 expression in L1 neurons, which does not directly test the requirement for DNT-2 in Mi1 neurons. In addition, the image quality in Figure 5 is problematic: brightness and contrast differ visibly between panels, making them challenging to interpret. Finally, the discussion states that "loss of function for DNT-3 (spz-3) causes lamina cell death that is not naturally compensated for by DNT-2," but no evidence is presented in this manuscript to support that conclusion.

Other general comments:

• Lack of labels for each individual image makes figures and text difficult to interpret/reference.
• Gene names not italicised in figures
• Inconsistent aspect ratio for graph axes (Obvious in figure 5C,D)
• Image borders often not completely vertical/horizontal making them appear jagged in some figures e.g. Figure1A.
• General typos e.g. (n=10 10 brains), inhibitor pf apoptosis p35
• Lobula complex should not be used to refer to lobula plate and lobula plug at this stage as they are distinct neuropils

Figure 1:

• Arrows not explained
• N-Cadherin absent from some images without explanation
• First two images of 1B are identical.
• Images in panel B at different timepoints and spz-4 is missing without explanation.

Figure 3:

• Dark spot in DNT-3FL 3A image.
• Descriptions in text often lack specific details "Dcp1+ apoptosis in the lamina and outside the lamina too." Supplementary:
• Figures S2-S6 lack labels denoting the timepoint of each figure
• Figure S7 is illegible
• Supplementary figure 8 is referred to as S9 in text and is missing genotype information as well as neuropil labels on images

Significance

Significance: This is an interesting topic of investigation, and the findings-if substantiated-would be of interest to the field of Drosophila visual system development and programmed cell death. In particular, it would be valuable to place these results in the broader context of programmed cell death as a mechanism for eliminating excess multicolumnar neurons during visual system development. However, at present the evidence presented does not convincingly support the authors' conclusions, and substantial further work is needed before the claims can be firmly established.

Expertise:

Drosophila neurogenesis, neuron specification, cell signalling

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

Alshamsi et al. investigate the role of Drosophila neurotrophins (DNTs) and their Toll receptors in regulating neuronal apoptosis during optic lobe development.

The authors provide compelling evidence that different DNTs and their Toll receptors are expressed in optic lobe neurons, and their activity regulates neuronal survival during optic lobe development. They further show that disruption of DNT/Toll signaling impacts neuronal morphologies.

Comments

ABSTRACT

"Over-expression of DNT-3 (spz-3) and DNT-2 (spz-5) could rescue natural occurring cell death, whereas their loss of function caused cell death, showing that DNT-3 and DNT-2 can, and are required to, promote cell survival during optic lobe development."

I find it more appropriate to say that OE prevents naturally occurring cell death because it inhibits a normal physiological process."rescue" would only be correct if there were an experimental or genetic loss (e.g., deletion of a survival factor) and you are restoring normal survival levels

"Importantly, DNT-2 is expressed in Mi1 neurons and Toll-2 in connecting L1 neurons. We show that DNT-2 functions in concert with Toll-2, as Toll-2 RNAi knock-down prevented the rescue of apoptosis by DNT-2 over-expression and all Toll-2+ neurons were lost in DNT-2 mutants."

I find this sentence very difficult to follow

i suggest moving "Importantly, DNT-2 is expressed in Mi1 neurons and Toll-2 in connecting L1 neurons."

to the next sentence. "by specifically investigating the Mi1 (DNT-2+) and L1 (Toll-2) synaptic partners", alterations in DNT-2 or Toll-2 expression levels impaired connectivity of L1 neurons at the M1 medulla layer and altered dendritic morphology of L1 neurons

"As DNT-3 (spz-3) and DNT-2 (spz-5) are expressed in the medulla and they could influence both lamina and medulla neurons, this suggests that their function maintaining cell survival could enable the stabilisation or alignment of connected neurons across medulla columns."

influence what? this is very vague and needs a temporal understanding of when neurons die, synapses are formed, and consider the phenotypes of the mutants and RNAi experiments.

INTRODUCTION

"Neuronal survival is maintained by neurotrophic factors secreted in limited amounts by target cells, leading to the survival of only those neurons that receive trophic support (Levi-Montalcini, 1987, Davies, 2003)."

Perhaps the authors can be more precise, e.g. One mechanism by which Neuronal survival is regulated is through neurotrophic factors secreted in limited amounts by to be synaptic partners and adjacent cells

"In this context, if neurotrophism is fundamental for nervous system development, it could have been enabled by evolutionarily conserved molecular mechanisms."

I think the authors want to suggest that given the fundamental and widespread role of neurotrophism in nervous system development, it remains unknown if it relies on evolutionarily conserved molecular players.

"Neurotrophins - NGF, BDNF, NT3, NT4 - are the main growth factors maintaining neuronal survival in the vertebrate nervous system (Levi-Montalcini, 1987, Lu et al., 2005). Importantly, they can also promote cell death, depending on context (Lu et al., 2005). They can promote cell survival via their Trk receptors and ERK and AKT downstream and via p75NTR and NFB downstream, or cell death via p75NTR, Sortilin, and JNK signalling instead (Lu et al., 2005). mechanisms."

The authors should avoid the repeated use of "they"

"There are six spz and nine Toll paralogous genes in Drosophila, which could play distinct functions. In fact, at least full-length DNT-1 and Toll-1 can promote cell death instead, and at least Toll-6 can promote either cell survival or cell death, depending on context (Foldi et al., 2017, Singh et al., 2025, Zhu et al., 2008) . Importantly, mature DNT-1 and DNT-2 with Toll-6 and Toll-7 are required for and can promote neuronal survival during circuit formation in the embryonic ventral nerve cord (McIlroy et al., 2013, Zhu et al., 2008)."

I find this paragraph difficult to follow. I suggest the following editing, which the authors might want to consider:

"There are six spz and nine Toll paralogous genes in Drosophila, which could play distinct functions. In fact, at least full-length DNT-1 and Toll-1 can promote cell death instead, while and at least Toll-6 can promote either cell survival or cell death, depending on context (Foldi et al., 2017, Singh et al., 2025, Zhu et al., 2008) . Importantly, mature DNT-1 and DNT-2 with Toll-6 and Toll-7 are required necessary and sufficient to promote for and can promote neuronal survival during circuit formation in the embryonic ventral nerve cord (McIlroy et al., 2013, Zhu et al., 2008).

"During this time (24-50h APF), connectivity between photoreceptors, lamina and medulla neurons is established; this is followed by medulla neurons connecting to lobula neurons;"

I find this sentence misleading, if not incorrect. If by connectivity the authors mean synaptogenesis, for all that is known, synaptogenesis has been shown to occur from from mid-pupal development (P50) onwards If by connectivity, the authors mean the targeting of specific neuropiles and layer organization, it is also incorrect that lamina and medulla organization precedes the connectivity between medulla and lobula neurons. These processes are all concurrent. Can the authors please clarify?

"and by 72h APF cell death has greatly diminished and synaptogenesis completes connectivity patterns, in preparation for adult eclosion at 96h APF (Millard and Pecot, 2018, Melnattur and Lee, 2011, Hadjieconomou et al., 2011, Kurmangaliyev et al., 2020) "

Kurmangaliyev et al., 2020 is probably not an appropriate citation here as it mostly deals with transcriptional programs of circuit assembly in the developing optic lobe

"Thus, 24-48h APF is a critical period to maintain necessary lamina and medulla neurons alive in the optic lobe."

Perhaps the authors want to revisit this sentence and explicitly say that 24-48h APF is a period where apoptosis defines cell numbers

"The development of the Drosophila visual system has been well described (Holguera and Desplan, 2018, Melnattur and Lee, 2011, Millard and Pecot, 2018, Hadjieconomou et al., 2011, Behnia and Desplan, 2015)."

I find that Behnia and Desplan, 2015 is not appropriate, as it is a review that describes the characterization of neuronal circuits underlying visual modalities in the fly brain, and not their development. The following reviews dealing with different aspects of neurogenesis, neuropile development and circuit formation are likely more relevant: Bakshi et al Current Opinion in Neurobiology 2025 Malin et al PNAS 2021 Ngo Dev Bio 2017

"R7 and R8, together with lamina neurons target to medulla layers M6 and M3, respectively, organizing into medullar columns that respond to the same point in visual space and maintain retinotopy."

I find this sentence misleading because lamina neurons do not target M6 and only L3 targets M3.

"Medullar interneurons also form connections across multiple layers, where each layer represents different visual features (Fischbach and Hiesinger, 2008, Millard and Pecot, 2018)."

Here, Behnia and Desplan, 2015, Matsliah et al Nature 2024, Borst and Groschner , Annu. Rev. Neurosci. 2023, and even Schnaitmann et al J Comp Physiol A Neuroethol Sens Neural Behav Physiol 2020 are better references that review feature detection and circuit organization in the optic lobe.

"Neurons within the lobula complex integrate signals from the medulla and project to the optic glomeruli in the central brain and motor outputs to enable appropriate behavior (Behnia and Desplan, 2015, Borst et al., 2020, Courgeon and Desplan, 2019b)."

I find Courgeon and Desplan, 2019b is not very appropriate here, as it reviews the coordination of neural patterning in the Drosophila visual system. More adequate and relevant manuscripts and reviews are Wu et al. elife 2016, Tanaka and Clark, 2022, Lapoetke et al. Neuron 2022 , even Zhao et al. elife 2024

"Spz-5 is well known as Drosophila neurotrophin-2 (DNT-2), and as Spz-3 has been proposed to have neurotrophin functions which we expand on and demonstrate here, we refer to Spz-3 as DNT-3 (Zhu et al., 2008, Coutinho-Budd et al., 2017, Sun et al., 2024, Ballard et al., 2014, Ulian-Benitez et al., 2017)."

This last paragraph of the introduction seems out of place, and partly redundant with page 3. Perhaps the authors would like to finish the introduction with a paragraph highlighting the major findings and conceptual advance of the manuscript? This seems to be a good and natural way of following their previous sentence "Here, we asked whether neurotrophin family ligands encoded by DNTs (spzs) and their Toll receptors could regulate cell survival during neural circuit formation, in the Drosophila pupal optic lobe."

RESULTS

I suggest the following edit: To ask whether DNTs (spzs) are expressed in the pupal optic lobe, we generated T2A-Gal4 driver lines for spz-1,3,4,5 fly lines , crossed them to 10xUASmyrGFP or 20UAS6xmCherry reporter flies, and analysed resulting progeny optic lobes during development and in the adult with anti-GFP antibodies, as required (Figure 1A).

Also, If the lines were also crossed with mcherry, mentioning anti-GFP antibodies is incomplete.

"spz-1MIO2318-T2A>myrGFP and spz-1MIO2318-T2A>6xmCherry revealed expression in a few centrifugal neurons in the lobula complex that projected to the lamina,"

At which stage?

"subsequently medulla neurons and abundant arborisations into the lobula complex and medulla."

Subsequent to what? I am sorry, but I don't understand this description.

"Expression from spz4MI5678 -T2A->myrGFP was not detected until 72h APF" Data before 72h APF is missing Where was it expressed? Which cell types? Which neuropiles?

"And then was found in the medulla and lobula complex and followed by the trachea." At which stage? What was followed by the trachea? I think the authors mean that at later staged (in the adult) expression was restricted to the trachea in both medulla and lobula

"spz-3-T2A>6xmCherry (hereby named DNT-3) was highly expressed in non-neuronal retinal cells and medulla neurons;"

At what stage?

"And subsequently in the trachea and possibly glia."

The authors could and should explain how they reach this conclusion. Given that no cell type specific markers were used, this identification was likely based on morphological features.

"Finally, DNT-2-T2A>6xmCherry (spz-5) was found in medulla neurons, which could be tentatively identified as Mi1 medulla neurons (Nern et al., 2025) by 48h APF, and this pattern was maintained."

The authors suggest these neurons are Mi1 based on what? Also, Fischbach's Cell Tissue Res (1989) seminal paper is probably worth mentioning.

"Abundant cells expressed spz-1 in the lobula complex (Figure 1B, left) and medulla (Figure 1B, right), and DNT-3 (spz-3) and DNT-2 (spz-5) in the medulla (Figure 1B) during optic lobe development. DNT-3 (spz-3) and DNT-2 (spz-5) were expressed in distinct non-neuronal cells in the retina, seen in Multi Colour Flip Out (MCFO) clones (Figure 1C)."

This sentence is misleading. These experiments allow the authors to conclude that spz+ neurons innervate these neuropiles. It does not allow the authors to conclude that spz molecules localize to the neuropiles. The authors should revise these claims in the main text and relevant figure legends

"To visualize the distribution of Tolls in the optic lobes during pupal development, we used the GAL4 lines previously described (Li et al., 2020), driving expression of the reporter myrGFP (Figure 2A)."

Same comment as above

"Using MCFO clones as well as myrGFP, we could identify some of the Toll-8+ neurons as Lawf1, feedback neurons projecting from the medulla to the lamina (Figure 2B), and L2 and L4 lamina neurons (Figure 2B, C); Toll-6+ cells to include L3 and L4 lamina neurons (Figure 2B,D); and Toll-2+ neurons as L1 lamina neurons which target to M1 and M5 medulla layers and L3 lamina neurons that project to M3 (Figure 3B,E) (Hakeda-Suzuki and Suzuki, 2014, Behnia et al., 2014)."

Hakeda-Suzuki and Suzuki, 2014, Behnia et al., 2014 are not the most appropriate references. Instead, I suggest the authors should cite Fischbach's Cell Tissue Res (1989).

"Overall, the expression in the scRNAseq dataset (Kurmangaliyev et al., 2020) of the spz ligands and Toll-8 (also known as Tollo) data were less consistent with the cell biology data, whereas the expression of Toll-1, -2 and -6 confirmed cells seen with the cell-biology based reporters"

It is perhaps more accurate to refer to the cell-biology based reporters as translation reporters, which is what T2a based Gal4 drivers are.

"Most particularly, Toll-2 mRNA (synonym 18w) was found in L1 and L3 lamina neurons over time, plus also in L5 at 24h APF, and Toll-6 mRNA was found in L2, L3, L4 over time, plus also in L1 at 24h (Supplementary Figure 1-6)."

This sentence is difficult to read and could be considered poorly written for several reasons including: - "plus also" is repetitive. "Plus" and "also" serve the same function. - Inconsistent punctuation. The lack of commas before "and Toll-6 mRNA..." makes the sentence feel unbalanced. -Vague time reference. "Over time" is imprecise. It's unclear whether it means during development, at multiple timepoints, or something else. Also regarding scRNAseq analysis: - the authors mention "We compared our reporter-based profiles with published scRNAseq datasets of the optic lobe through development (Kurmangaliyev et al., 2020, Ozel et al., 2021)" however the Ozel dataset doesn't seem to be used.

Also, from the Material and Methods section:

"The data were imported as a Seurat object, and cells corresponding to specific timepoints (e.g., 24 h, 36 h) were subsetted based on the provided metadata. Dimensionality reduction was carried out using principal component analysis (PCA), followed by Uniform Manifold Approximation and Projection (UMAP) embedding computed on the first 30 principal components. Cluster annotations provided by the original authors were used for all cluster-level analyses and visualisations."

The Kurmangaliyev dataset is already processed. I am probably missing something here, but is not obvious to me why the authors performed PCA again

"To conclude, at the time of naturally occurring cell death (0-48h APF), Toll-1 is highly expressed throughout the optic lobe; Toll-2, -6 and -8 are expressed in the medulla; Toll-8 and Toll-6 are prominently expressed in the lobula complex, and Toll-6 and Toll-2 are prominent in the lamina."

This is misleading. These experiments allow the authors to conclude that toll+ neurons innervate these neuropiles. It does not allow us to conclude that toll molecules localize to the neuropiles. The authors should revise these claims in the main text and relevant figure legends

"To ask whether DNTs can promote cell survival in developing optic lobes, we over-expressed DNT-2 (spz-5) and DNT-3 (spz-3) and visualized dying cells with the apoptotic marker anti-Dcp1 at the peak of naturally occurring cell death (24h APF)."

These experiments were done using Toll8-Gal4 and nsyb-Gal4 drivers. What's nsyb-Gal4 expression during development? Is the expression of this driver consistent with the conclusions drawn from these experiments?

"To test whether DNT-2 could promote cell survival during optic lobe development, we over-expressed full-length DNT-2FL or cleaved DNT-2CK in all neurons with nsybGAL4. This reduced the incidence of Dcp1+ apoptosis in the lamina and outside the lamina too (Figure 3C-D and Supplementary Figure S9C,D)."

How do the authors explain that DNT-2CK reduced the number of Dcp1+ cells?

"We generated DNT-3 (spz-3) loss of function mutants by P-element mobilization. DNT-2 and DNT-3 loss of function mutants caused considerable cell debris in the medulla and lobula complex, which compromised the analysis in this region, so we focused on the lamina."

Perhaps, rather than stating that the mutants caused considerable cell debris, the authors could say that the mutants displayed considerable cell debris

More importantly, I have concerns with the data from these experiments (Figure 3). Dcp1 signal volume intensity using Imaris. In all panels (A,C,E) the segmented images do not match the raw DCP1 staining, raising concerns on how much can one rely on this quantification. Could this be because the Dcp1 staining shown is a single z plane and the segmentation is a 3d rendering? The authors should carefully and robustly explain this discrepancy which is present in all images where Dcp1 signal volume intensity was quantified.

Also, could the authors explain why the quantifications in Figure 3B and 3C differ by an order of magnitude (10×) from those in panel 3D? Please look at the WT control, there is a 10X difference in signal volume intensity.

"Toll-2pTVGAL4 flies are heterozygous mutant for Toll-2, and, remarkably, in combination with DNT-2 homozygous mutants resulted in semi-lethality, revealing a functional interaction between these two genes.

I cannot entirely follow this conclusion. I understand the authors propose that the combination of partial loss of Toll-2 and full loss of DNT-2 affects viability, more than either mutation alone. Is this what they mean? Can the authors comment on the viability of DNT-2 mutants?

"Macrophages loaded with HisYFP and distributed mostly between the retina and lamina could be observed across these samples (Figure 4C), suggesting they had engulfed dead cells" How do the authors identify these YFP+ cells as macrophages?

"Together, these data show that DNT-2 functions as a ligand for Toll-2 to maintain the survival of neurons in the lamina, medulla and lobula complex during optic lobe development." While the results from Figure 4 showing that DNT-2 acts as a ligand for Toll-2 to support neuron survival are solid ( in particular panels C-F), it doesn't necessarily mean all neurons die directly due to loss of Toll-2 signaling. It is plausible that Neurons that express Toll-2 die because they lose critical survival signals. The death of these Toll-2-expressing neurons could then cause a cascade effect, where neighboring or connected neurons die indirectly due to loss of trophic support, disrupted circuits, or secondary damage. So, the observed cell death in multiple regions may be a combination of direct effects on Toll-2-positive neurons and indirect effects on other neurons. "In the Drosophila pupa, connectivity of lamina to medulla neurons takes place at 30-48h APF, and between medulla and lobula complex at 60-70h APF (Kurmangaliyev et al., 2020, Millard and Pecot, 2018, Pecot et al., 2014, Hadjieconomou et al., 2011)." I have the same comment as mentioned above regarding the timing of connectivity. If by connectivity, the authors mean the targeting of specific neuropiles and layer organization, it is incorrect that lamina and medulla organization precedes the connectivity between medulla and lobula neurons. These processes happen concurrently. Can the authors please clarify?

"Importantly, the expression of synaptic markers starts at 24h, peaks at 60h APF and spontaneous neuronal activity takes place at 48h APF, meaning that at least some neural circuits are already connected by this point (Kurmangaliyev et al., 2020)."

The correct placement of the reference to Kurmangaliyev et al. is after "peaks at 60h APF " A reference to Akin et al and Bajar et al when referring to PSINA is missing.

"Thus, the period of naturally occurring cell death overlaps with connectivity" I think the authors mean that the period of cell death is concurrent with the development of synaptic connectivity.

"L1 neurons normally project along columns that can be labelled with mAb24B10, and target to layers M1 and M5 of the medulla." The authors should mention that 24b10 labels the photoreceptors, providing a spatial reference to identify medulla columns

"Interestingly, Toll-2RNAi knock-down did not alter the phenotype caused by DNT- 112FL overexpression, and impaired targeting to the same extent as each genetic manipulation alone (Figures 5B,D)."

How do the authors interpret these results? And perhaps the authors would like to explain the rationale of overexpressing DNT-2fl in L1 neurons, that do endogenously express it.

"To conclude, these data show that DNT-2 and Toll-2 are required for appropriate connectivity of L1 neurons to target Mi1 medulla neurons at M1 medulla layer."

The authors characterize neuronal morphologies but do not directly assess connectivity using synaptic markers. While defective morphologies are likely to impact connectivity, the conclusion that DNT-2 and Toll-2 are required for appropriate connectivity should be tempered. The authors should revise their wording to reflect that their data support morphological defects rather than direct evidence of altered synaptic connectivity.

DISCUSSION

"In fact, throughout animal development, between 50% (e.g. in Drosophila) and 80% (e.g. in vertebrates) are lost to naturally occurring cell death"

"of neurons" is missing before "are lost"

"Consistently with these findings, we have shown that the survival of L1 neurons depends on DNT-2 functioning together with Toll-2."

The authors state that "the survival of L1 neurons depends on DNT-2 functioning together with Toll-2." It seems that what they intend to convey is that DNT-2 acts as a ligand for Toll-2. The text should be clarified to explicitly indicate this ligand-receptor relationship rather than implying a cooperative function.

"These data demonstrate that DNT-2 and Toll-2 function together in visual system development."

Since the authors did not use tub-GAL80 or another temporal control to restrict gene expression specifically to development, the observed phenotypes could reflect combined developmental and adult effects. Throughout the text, the authors should revise their wording to acknowledge this limitation.

"Finally, interference with the normal levels of DNT-2 and Toll-2 also impaired axon targeting and dendritic morphology, consistently with the coupling between cell survival with connectivity."

The authors state that interference with normal levels of DNT-2 and Toll-2 "impaired axon targeting and dendritic morphology, consistently with the coupling between cell survival and connectivity." This statement seems tautological, as neurons that die cannot form connections. The authors should clarify whether they are referring to a specific mechanistic link beyond this obvious consequence.

"Our findings are consistent with prior reports that had shown the maintenance of cell survival to be required during neural circuit formation."

This statement seems tautological. It is generally expected that neurons must survive in order to contribute or be part of neural circuits. The authors should clarify if they are highlighting a specific mechanistic insight beyond this obvious requirement.

"In the medulla, Dm8 medulla neurons are produced in excess and are eliminated during connectivity to their R7 inputs (Courgeon and Desplan, 2019a). This is enabled by the cell surface molecular tags DIP in yDm8 binding Dpr11 in yR7, during synaptic matching (Courgeon and Desplan, 2019a)."

The statement that "Dm8 medulla neurons are produced in excess and are eliminated during connectivity to their R7 inputs" is both unclear and inaccurate. It is not evident what is meant by "during connectivity." Moreover, Courgeon and Desplan (2019a) show that Dm8 neurons undergo cell death before or by P40, prior to synaptogenesis. The authors should correct this statement and clarify the timing and mechanism of Dm8 neuron elimination.

"Importantly, the maintenance of cell survival takes place during connectivity, and enables synaptic matching between connecting neurons."

It is unclear what is meant by "during connectivity." Moreover, both Courgeon et al. (2019a) and Xu et al. (2018, 2022) show that these neurons (e.g., Dm8, Dm12, Dm14) undergo cell death before or by P40, prior to synaptogenesis. The authors should clarify the timing and mechanism of cell survival and revise this statement accordingly.

"By contrast, it has also been proposed that apoptosis plays a minor role in cell number control during visual system development, depending instead on cell proliferation and spatial patterning through Dpp/BMP signalling (Malin et al., 2024). However, those findings were based on events taking place at the larval third instar wandering stage, when proliferation and spatial patterning are prevalent, whereas apoptosis peaks in pupa."

It seems that the authors are trying to suggest that different mechanisms control cell numbers at different developmental stages: during larval neurogenesis (L3), cell numbers are regulated primarily by proliferation and spatial patterning, whereas in the pupal stage, neuronal survival via apoptosis plays a key role. If this is the intended point, it should be stated more clearly, as the current comparison to Malin et al. (2024) is confusing and does not make this distinction explicit.

"However, Toll-2 mutant MARCM clones generated in the pupa result in a dramatic loss of lamina neuron dendrites and aberrant axonal navigation in the medulla, as well as widespread neuronal loss (Li et al., 2020)." This statement is puzzling. Neurogenesis occurs during the larval stage until P15, and MARCM requires progenitor cell division. The authors should clarify how MARCM clones were generated during pupation and provide the relevant experimental details in the Materials and Methods. "Importantly, connectivity between L1 and medulla neurons takes place between 20-48h APF, during the period of naturally occurring cell death, and spontaneous activity in the optic lobe takes place at 48h, meaning at least some circuits are connected by then (Kurmangaliyev et al., 2020)."

The authors state that "connectivity between L1 and medulla neurons takes place between 20-48h APF," but no reference is provided for this timing. To my knowledge, no study has directly demonstrated this, so the authors should either provide supporting evidence or revise this statement. Additionally, citing Kurmangaliyev et al. (2020) for spontaneous activity in the optic lobe is not appropriate for this point, as PSINA was originally described by Orkun Akin.

"When altering DNT-2 or Toll-2 levels, L1 axonal terminals in the medulla were misrouted, rather than being confined to a single column. This is reminiscent of the phenotypes caused by alterations in Dscam and Fez levels (Millard et al., 2007, Peng et al., 2018)."

The authors note that altering DNT-2 or Toll-2 levels causes L1 axonal terminal phenotypes reminiscent of phenotypes caused by changes in Dscam and Fez levels (Millard et al., 2007; Peng et al., 2018). However, they only reference these previous studies without discussing whether there could be a shared mechanism. While these comparisons are interesting, the manuscript would benefit from either a deeper discussion of potential mechanistic links or a clear statement that the comparison is purely phenotypic.

"As DNT-2 is secreted in medulla neurons and Toll-2 is expressed along neurons that connect in the medulla (e.g. L1, Mi1, Tm3, Dm9, T4), DNT-2 could help keep connecting neurons together during dynamic cellular events in development."

This sentence is poorly written and vague. It is unclear what "keep connecting neurons together" means mechanistically. Likely, DNT-2 is secreted by postsynaptic medulla neurons (e.g., Mi1), whereas Toll-2 is expressed in neurons innervating the medulla (e.g., L1, Mi1, Tm3, Dm9, T4). The authors should rephrase this sentence to clearly convey their mechanistic and cellular interpretation.

FIGURES

Figure 1 Arrowheads point to what? OL orientations should be described in the figure captions

Figure 5 The title of Figure 5 ("Altering the levels of DNT-2 and Toll-2 modifies L1 axon targeting at medulla M1 layer") is misleading. The correct layer targeting is preserved; what changes is the pattern of unicolumnar innervation. When DNT-2 or Toll-2 levels are altered, L1 neurons innervate multiple columns rather than maintaining their normal single-column specificity. The title should be revised to reflect that the defect is in columnar specificity rather than layer targeting.

Supplementary Figures S1 to S6 Combined UMAPs showing the expression of spz-1, -3 (DNT-3),-4 and -5 (DNT-2) and Toll-1, -2 (18w), -6 and -8 (Tollo) in distinct cells over time.

Information about which UMAP corresponds to which time point is missing

MATERIALS AND METHODS Genetics. Please see S1 Table for the list of the stocks used and Table S3 for full genotypes for each experiment. Table S3 is not the full genotypes for each experiment. This information is partly available in the Source Data excel file

Significance

During development, neurons are initially produced in excess. One mechanism by which the final neuronal numbers are refined relies on trophic support, which maintains the survival of necessary neurons, while excess neurons are eliminated.

In the Drosophila optic lobe, a wave of apoptosis occurs during pupation, peaking at a critical period thought to be essential for establishing final neuronal numbers and supporting proper neural circuit formation. However, the mechanisms underlying this developmental process remain poorly understood. In this manuscript, Alshamsi et al. investigate this wave of apoptosis by examining the role of Drosophila neurotrophins (DNTs), which are encoded by spätzle (spz) paralogous genes and signal through Toll receptors to regulate neuronal survival during brain development.

The authors use translation reporters to demonstrate that DNTs and Toll receptors are differentially expressed across various neuronal types innervating all optic lobe neuropils during development. They then focus on DNT-3 and DNT-2, which they show to be necessary for controlling neuronal numbers, likely by maintaining neuronal survival during pupal stages.

Notably, the results reveal a previously uncharacterized interaction between DNT-2 and Toll-2. The findings suggest that DNT-2 acts as a neurotrophic factor produced by medulla intrinsic neurons, binding to the Toll-2 receptor expressed in other neurons innervating the medulla. By examining Toll-2+ L1 neurons, which are postsynaptic in the lamina and presynaptic in the medulla, the authors provide compelling evidence that DNT-2/Toll-2 signaling regulates L1 neuronal numbers.

Interestingly, the authors also show that disruption of DNT-2/Toll-2 signaling affects L1 axonal and dendritic morphologies. However, the extent to which changes in neuronal survival and neuronal morphology are mechanistically or cellularly linked is not addressed. These findings are consistent with previous reports showing that DNTs and Toll receptors regulate neuronal survival in embryonic, larval, and pupal ventral nerve cords, as well as in the adult. Importantly, DNTs and Tolls can also promote cell death, highlighting their dual role in controlling neuronal number and circuit formation.

While the data is for the most part solid, I have concerns regarding the execution, interpretation of certain results and the conclusions drawn. Additionally, references to previous work are often incorrect or incomplete; I provide several examples below along with non-exhaustive suggestions for improvement. Finally, the manuscript would benefit from careful text revision and improvements to figure presentation, for which I also offer non-exhaustive guidelines.

Overall, I would recommend this manuscript undergo revision before its publication and I would be happy to reassess a revised version that addresses the comments above.

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

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Reply to the reviewers

Manuscript number: RC-2023-01861

Corresponding author(s): Manuela, Baccarini

1. General Statements

We were happy to learn that all three reviewers found the paper novel and of interest for a cell biology audience. They especially highlighted the carefully conducted screen, whose results will be integrally published with this paper and will be of use for scientists interested in lysosome biology. The revised manuscript contains key validation experiments (antibody/KO controls, lysosome positioning quantification, live-cell actin dynamics) to strengthen our central conclusions.

2. Point-by-point description of the revisions

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

Reviewer 1

• The colocalization of endogenous PLEKHG3 and LAMP1 as depicted in figures 3B and 3C (data from fixed cells) is not convincing. PLEKHG3 appears to be present on cortical actin structures as opposed to being colocalized with LAMP1 on lysosomes. And related to this point:

• There is no apparent colocalization of PLEKHG3 and lysotracker in the movie S5.

Answer:

We do not claim that the two structures always colocalize, but that PLEKHG3 is a LAMTOR3 vicinal protein that co-enriches with a subset of peripheral lysosomes at focal adhesions (FAs)/protrusions. The images in Figure 3C are schematic for how PLEKHG3-high/low and LAMP1-high/low regions were defined for quantification. We agree with the Reviewer and with the previous literature that PLEKHG3 main localization is to cortical actin structures, as reaffirmed by the strong cortical actin localization shown in Figure 3F of the original version and in Figure S2C (HEK293T cells) and in Figure S3A in HeLa cells in the revised version. We have clarified the text referring to Figure 3F on page 26, line 11-14 as follows:

“Immunofluorescence experiments showed the reported colocalization of endogenous PLEKHG3 (Figure S2C in HEK293T cells, Figure S3A in HeLa cells) and GFP-PLEKHG3 with cortical actin structures and the partial localization of LAMP1-positive vesicles to these structures in correspondence with vinculin-positive focal adhesions.”

Live imaging in GFP-PLEKHG3-expressing cells (including movie S5, and particularly the stills of the leading edge in Figure 4F) further supports this spatial association without implying obligate colocalization. We added explicit language (p. 27, lines 19-21): “Following a single cell over time, we could observe that __a subset of __lysosomes appears to travel to PLEKHG3 accumulation sites and specifically move into developing protrusions.”

• The authors should also confirm the specificity of the PLEKHG3 antibody in immunofluorescence using control and PLEKHG3 siRNA in untransfected cells that have not been transfected with GFP-PLEKHG3 (as is shown in Fig. S2C). Numerous antibodies recognize the overexpressed protein but do not recognize the same protein at endogenous expression levels.

Answer: To assess the specificity of the antibody for endogenous PLEKHG3 we have used HEK293T cells, which based on the fact that PLEKHG3 is most highly expressed in neuronal cells (https://www.proteinatlas.org/ENSG00000126822-PLEKHG3/tissue#expression_summary) should yield a clearer endogenous signal. The pattern of PLEKHG3-positive bands is similar to that observed in HeLa cells, and only the band around 250 kD is clearly reduced by the siPLEKHG3. The IF images show a selective loss of the PLEKHG3 signal in correspondence of actin filaments close to the plasma membrane, whereas the nuclear signal is preserved, and therefore to be considered non-specific (revised Figure S2B-C).

Extract from revised Figure S2B-C: ____PLEKHG3 KD test in HEK293T cells: B) Western blot of HEK293T cells showing downregulation of PLEKHG3 expression upon siPLEKHG3 treatment compared to siScr. Bar plot shows quantification of PLEKHG3 bands from immunoblot above. Error bars = SEM, n=3. * = p values according to student's t-test. C) Immunofluorescence images of HEK293T cells. siPLEKHG3 shows drop in PLEKHG3 intensity in the periphery of the cell and less colocalization with Phalloidin. Scale bar = 50 µm. Line plots show intensity profiles of Phalloidin (green) and PLEKHG3 (red) along the white lines in the merged inset images. Scale bar = 10 µm.

In addition, we have now generated a PLEKHG3 CRISPR-Cas KO in HeLa cells. The results, shown in revised Figure S2G-I, confirm the specificity of our reagents and the localization of PLEKHG3 seen in HEK293T cells.

Extract from revised Figure S2G-I: G) Immunoblot and quantification of HeLa PLEKHG3 KO cells represents the degree of PLEKHG3 depletion achieved using different guides compared to WT cells transfected with empty vector (EV). The most potent guides (8-9) are boxed in red. H) Immunofluorescence images of WT and PLEKHG3 KO8 cells reveal an overall drop in PLEKHG3 intensity and the specific loss of PLEKHG3 signal at the periphery of the cells. I) Quantification of PLEKHG3 intensity as displayed in H for two KO cell lines compared to WT cells. Dots represent individual data points of each of the three-color coded replicates; diamonds represent the mean of each replicate; black bars represent the mean ± the SEM of three biological replicates; * = p values according to 2-way-ANOVA. Error bars = SEM.

These results establish that the peripheral cortical signal is specific for endogenous PLEKHG3; the nuclear signal is non-specific. Loss of PLEKHG3, however, had no effect on lysosomal distribution, morphometric parameters (see revised Figure S4A-C) or protrusive activity (see revised Figure S6E-F) compared to WT cells.

Extract from revised Figure S4A-C: ____PLEKHG3 KO does not influence lysosomal distribution or cell morphometry: A) __Quantification of lysosomal distribution in WT compared to two KO cell lines. N ≥ 50 cells in three biological replicates. __B) Schematic representation of analysis of cell shape descriptors as referred to in C). Left picture shows the calculated outline in yellow based on which the cell area and circularity are calculated. Right picture shows the minor and major cell axis which, calculated as fraction, result in the aspect ratio of the cell. Scale bar = 50 µm. C) Quantification of cell morphometric parameters Area, Circularity and Aspect ratio. N ≥ 50 cells in three biological replicates. Black dots represent mean of each biological replicate. Statistical analysis according to student’s t-test. Error bars = SEM.

• The claim that "peripheral accumulation of lysosomes inhibits protrusion formation and limits cell motility" should be tested more rigorously using the RAMP method, preferably in living cells. Other approaches, such as overexpression/siRNA of Arl8b and other motor adaptors, such as SKIP/PLEKHM2, can be used to alter lysosome positioning and confirm this central finding of the manuscript. The authors could also consider including additional mechanistic data in order to comprehend how lysosome positioning controls cell motility. For instance, the RAMP approach could be employed to investigate cortical actin dynamics upon repositioning of lysosomes to the peripheral/perinuclear region.

Answer: We have purchased the RAMP system from Addgene and adapted the reporters to express fluorophores compatible with our color setup in the different respective cell lines (HeLa GFP/GFP-PLEKHG3 as well as in HeLa PLEKHG3 KO cells. Unfortunately, we’ve experienced difficulties with imaging due to suboptimal efficiency of the double transfection necessary to introduce the RAMP system into the cell lines. The LAMP1 and the KIF plasmids were co-expressed at very different levels in the cells, leading to the need for high laser power in both channels, which too often resulted in cell death. Additionally, the redistribution of the lysosomes after biotin addition was incomplete and slower than initially expected, which made it impossible to investigate cortical actin dynamics.

To gain some mechanistic insight, we have performed further live cell imaging analyses comparing PLEKHG3 WT vs KO cells and GFP vs GFP-PLEKHG3 cells expressing a combination of BFP-LifeAct (to visualize F-actin) with either control mCherry or mCherry-KIF1A to move lysosomes to the periphery.

• In all experiments, locking lysosomes in the periphery drastically reduces membrane dynamics (protrusion formation and retractions).
• PLEKHG3 remains colocalized with LifeAct under KIF1A (Fig. S6C–D), indicating that the reduced protrusiveness is upstream or independent of PLEKHG3’s cortical localization
• Live-cell BFP-LifeAct imaging revealed that KIF1A-driven peripheral lysosomes reduce protrusion formation/retraction and dampen cortical actin dynamics in both WT and PLEKHG3 KO cells (Fig. S6A–B, E–G; Movies S12–15; S18–21), indicating that these phenomena are independent of PLEKHG3. We believe these data, together with the quantitative lysosome repositioning and FA analyses, substantiate the central finding that forced peripheral lysosome clustering correlates with more adhesive FA states and suppressed protrusive activity. We have clarified scope and limitations accordingly.

Extract from Figure S____1____A-C,E,G: PLEKHG3 localizes to F-actin independently of lysosomal transport but is dispensable for protrusive activity. A) __Stills from live cell imaging (Movies S12-15). Cells stably expressing GFP or GFP-PLEKHG3 were transfected with the indicated mCherry constructs. Yellow arrows = forming protrusions; blue arrows = retracting protrusions. Stills were generated over a period of 2 hrs. Scale bar = 50 µm. __B) __Quantification of protrusions formed and retracted over time in cells from A. Values indicate average number of protrusions formed in a timespan of three hours from a total of ≥ 15 cells per condition. Error bars = SEM. C) Quantification of colocalization by Fijis Coloc2 Plugin (see materials and methods) over a timespan of three hours. Lines represent mean of all cells per condition, and light-color shading represents the SEM. __E) Stills from live cell imaging (Movies S18-21). PLEKHG3 WT and PLEKHG3 KO cells were transfected with the indicated mCherry constructs and incubated with LysoTracker. Yellow arrows = forming protrusions; blue arrows = retracting protrusions. Stills were generated over a period of 2 hrs. Scale bar = 50 µm. G) Quantification of protrusions formed and retracted over time in cells from E. Values indicate average number of protrusions formed in a timespan of one hour from a total of ≥ 15 cells per condition. Error bars = SEM. In B,G, black asterisks denote p values according to Kruskal-Wallis and Bonferroni post-hoc testing, comparing the effect of KIF1A against mCherry or PLEKHG3 WT against KO.__ __

• It is not clear how the authors conclude that Figure 4E graph shows "the LAMP1 signal was stronger in paxillin-labeled FA compared to control regions". The 4E graph shows LAMP1 signal in GFP versus GFP-PLEKHG3 and shows a modest enrichment of LAMP1 in FAs in GFP-PLEKHG3 overexpression. LAMP1 enrichment in FAs is also not obvious in the image shown in Figure 4B.

Answer: We stand corrected – the Figure we referred to was not in the manuscript. It has been inserted now, as a plot next to Figure. Figure 4B (schematic representation of colocalization analysis) was designed to explain how we define focal adhesions (paxillin positive) and adjacent control regions (same size and shape, but paxillin-negative). The actual analysis was missing and has now been inserted. We apologize for this mistake.

We do not claim that PLEKHG3 brings lysosomes to FAs. The enrichment of lysosomes in FA regions of cells expressing GFP-PLEKHG3 compared to GFP-expressing cells shown in 4E, as the Reviewer correctly notes, is marginal and is not highlighted anywhere in the text exactly for this reason.

• In Fig. 2B, there appears to be a labeling error. The lanes 2,4 and 7 appear to be transfected with L3-T-V5 but labeled as GFP-V5-cyto. Here the PLEKHG3 band should be indicated.

• AND -Fig. 2C is an IP experiment as per the manuscript text but it is labeled as pulldown.

Answer: We stand corrected, and the necessary changes have been made in the revised version in Figure 2B.

Reviewer 2

1 - Specificity of PLEKHG3 antibody: In Fig. S2, authors show that PLEKHG3 antibody recognizes 3 bands (above 100 kDa, above 130 kDa and 250 kDa) and all of them are reduced by the silencing of PLEKHG3. Then, in Fig. 2A and C, authors only show the band above 130 kDa, despite implying that the specific band should be "much higher than the 134 kDa calculated from the aminoacid sequence of the protein".

In Fig. 2 B, they show all the bands shown in Fig. S2 and presumably favor that the specific band is the 250 kDa one. Finally, in Fig. 2D, they show all bands and note that the band above 130 kDa is not specific. Therefore, authors need to conclude what is the specific band and always analyze the same one, and, possibly, use a different antibody or purify this one to remove non-specific binding. Without this, the main result of the paper, cannot be substantiated.

Answer: We apologize for this misunderstanding. The antibody recognizes three bands, all reduced by siRNA treatment. These three bands are only resolved in the gels in Figure S2A and B, and in Figure 2B. The reason for this is the high molecular weight of the isoforms, that are resolved in these 8% gels, but collapse into one band in the 15% gels shown in Figure 2A and C. Therefore, the high molecular weight bands are not resolved under these conditions. 8% gels such as the ones in Figure 2B are needed to resolve the high molecular weight bands.

Figure 2D shows an 8% gel, and therefore all bands are visible. The band marked by an arrow is only present in the streptavidin pulldowns but not in the input or in the supernatant and is therefore considered unspecific. This has been clarified in the revised figure legend on page 41. In addition, to assess the specificity of the antibody for endogenous PLEKHG3 we have used HEK293T cells, which based on the fact that PLEKHG3 is most highly expressed in neuronal cells (https://www.proteinatlas.org/ENSG00000126822-PLEKHG3/tissue#expression_summary) should yield a clearer endogenous signal. The results of this experiment are shown in Figure S2B-C of the revised manuscript. The pattern of PLEKHG3-positive bands is similar to that observed in HeLa cells, and only the band around 250 kD is clearly reduced by the siPLEKHG3. The IF images show a selective loss of the PLEKHG3 signal in correspondence of actin filaments close to the plasma membrane, whereas the nuclear signal is preserved, and therefore to be considered non-specific. More importantly, we have now generated a PLEKHG3 CRISPR-Cas KO in HeLa cells. The results, shown in Figure S2G-I confirm the specificity of our reagents and the localization of PLEKHG3 seen in HEK293T cells. Loss of PLEKHG3 however, had no effect on lysosomal distribution or morphometric parameters compared to WT cells (Figure S4A-C).

2 - In page 12, authors state that "These results indicated that PLEKHG3 is a transient interactor, or a proximal, not directly binding protein, of L3" and in page 14 that "... PLEKHG3 is a proximal L3 protein rather than a transient physical interactor". It is not clear at all how did the authors reach such conclusions, nor they have data to conclude this. Indeed, they would have to express the proteins in vitro and test their interaction to conclude about a direct binding. They also do not know what is the stability of the interaction.

Answer: This is also a misunderstanding. We mislabeled Figure 2C as “pulldown”, rather than “IP”, as it is characterized in the text. We revised terminology to “vicinal (proximity-labeled) protein” throughout, avoiding claims on directness. Our basis is: robust L3 TurboID labeling of PLEKHG3; failure to co-immunoprecipitate PLEKHG3 with V5-tagged L3 (Fig. 2C); lack of PLEKHG3 labeling by TMEM192; and unchanged PLEKHG3 FA localization in L3 KO (Fig. S3H–J). Together, these support spatial proximity rather than a stable L3–PLEKHG3 complex. We explicitly state that we did not perform in vitro binding due to the negative co-IP.

Based on these negative data, we did not proceed to test the possibility of complex formation in vitro.

3 - Still in page 12, authors state that "... two different membrane structures, protrusions and ruffles". What do the authors mean exactly by "protrusions", as there are several different ones (e.g., lamellipodia, filopodia, pseudopods)? And how can they distinguish between ruffles and, for example, lamellipodia? They need to use markers and more carefully analyze their morphology to be able to distinguish these. Like this, it is too preliminary.

Answer: It was our intention to indicate with the arrows the trajectories in the figure along which we measured the MFI of LAMP1 and PLEKHG3. Although this is indicated in the figure legend, it had apparently given the impression that the arrows indicated specific membrane structures. Since we are focusing on different types of membrane protrusions rather than ruffles, we replaced the ambiguous terms "ruffles" and "protrusions" with the terms "elongated protrusions" (Figure 3D upper panel) and then compared these with "non" elongated protrusions” (Figure 3D lower panel). Indeed, we note that PLEKHG3 accumulation is possible below and along the plasma membrane, but colocalization with lysosomes occurs preferentially in elongated protrusions. We therefore amended the text on page 26, line 4-9 as follows:

„More specifically, we found that PLEKHG3 colocalized more strongly with LAMP1-positive vesicles in elongated membrane structures (Figure 3D-E). Focal adhesion sites, which anchor the intracellular cortical actin network to the extracellular matrix and are remodeled with the help of late endosomes/lysosomes during protrusion formation and cell motility, can also be found in such elongated membrane protrusions (reviewed in [58,59]).”

5 - It is not clear if in cells KO for PLEKHG3, the overexpression of KIF1A leads to more lysosomes localizing close to the PM, as well as more protrusions and more cell motility, as the authors only compare cell overexpressing GFP or GFP-PLEKHGL3.

Answer: We have now generated a PLEKHG3 KO cell line. In these cells, KIF1A still drives peripheral lysosome clustering and suppresses protrusive activity and actin dynamic (see revised Figure S4A-C displayed below). Baseline lysosome distribution and morphometric parameters are unchanged in KO cells (see revised Figure S6E-F displayed below).

Extract from revised Figure S4A-C: ____PLEKHG3 KO does not influence lysosomal distribution or cell morphometry: A) __Quantification of lysosomal distribution in WT compared to two KO cell lines. N ≥ 50 cells in three biological replicates. __B) Schematic representation of analysis of cell shape descriptors as referred to in C). Left picture shows the calculated outline in yellow based on which the cell area and circularity are calculated. Right picture shows the minor and major cell axis which, calculated as fraction, result in the aspect ratio of the cell. Scale bar = 50 µm. C) Quantification of cell morphometric parameters Area, Circularity and Aspect ratio. N ≥ 50 cells in three biological replicates. Black dots represent mean of each biological replicate. Statistical analysis according to student’s t-test. Error bars = SEM.

Extract from revised Figure S6E,G: ____PLEKHG3 localizes to F-actin independent of lysosomal transport but is neglectable for lysosomal effect on protrusive activity. E) Stills from live cell imaging (Movies S18-21). PLEKHG3 WT and PLEKHG3 KO cells were transfected with the indicated mCherry constructs and incubated with LysoTracker. Yellow arrows = forming protrusions; blue arrows = retracting protrusions. Stills were generated over a period of 2 hrs. Scale bar = 50 µm. G) Quantification of protrusions formed and retracted over time in cells from E. Values indicate average number of protrusions formed in a timespan of one hour from a total of ≥ 15 cells per condition. Error bars = SEM. In F,G, black asterisks denote p values according to Kruskal-Wallis and Bonferroni post-hoc testing, comparing the effect of KIF1A against mCherry or PLEKHG3 WT against KO.

6 - Regarding the statistical analysis, authors assert that it was done using Student's t tests, unless otherwise stated. However, they never refer in figure legends other statistical analysis methods. If so, they cannot use such test, for example, in cases where more than two groups are compared.

Answer: We clarified in Methods that we performed two-group comparisons unless otherwise stated. Where >2 groups are compared, we used appropriate tests with correction (e.g., Kruskal–Wallis with Bonferroni in Fig. S6B, S6G). Figure legends now explicitly state the test used.

__Minor comments: __

1 - In the abstract, authors refer that cytosolic proteins are recruited to platforms on the limiting membrane of lysosomes. What do they mean by "platforms"? Is it microdomains?

Answer: We apologize for this lack of clarity and have now changed the first sentence in the abstract on page 1 to “Lysosomes are key organelles involved in metabolic signaling pathways through their ability to recruit cytosolic molecules to protein platforms bound to the lysosomal membrane”. We refer to protein platforms as multifunctional protein complexes that can recruit and assemble signaling components (e.g., the recruitment of mTORC1 activating proteins by the LAMTOR complex).

2 - In the Introduction, there is a period before the reference at the end of the first paragraph.

Answer: We stand corrected. See changes on page 18, line 9.

3 - In the results, Fig. 1E is mentioned before Fig. 1D and Figure S1F before Fig S1E, which can be confusing.

Answer: Figure S1E on page 6 was mislabeled as Figure 1E and Figure S1K on page 9 was mislabeled as Figure 1K. We stand corrected. See changes on page 21, line 21+23 and page 23, line 5.

4 - All the immunofluorescence images need to be bigger, in general, and have zoom-ins, except Fig. 3A, 4B, 4F, and S2C. Also, in Fig. S1F, the green channel has different intensities and the V5-lyso signal is clearly saturated. Finally, Fig. S1D, S1I and S3F must be enlarged, too.

Answer: We appreciate the Reviewer's suggestion, but enlarging all the immunofluorescence images and including zoom-ins would make the manuscript very crowded and could distract from the main findings. Regarding the expression levels of the baits, as mentioned in the manuscript, we aimed to express them at near-endogenous levels. However, TMEM192 is expressed at higher levels than LAMTOR3 in these cells, which may have resulted in the observed discrepancy. We hope the Reviewer will understand our decision and find the current presentation of the data clear and informative.

5 - In page 9, where it reads "Figure 1K", should read "Figure S1K".

Answer: See answer to minor point 3.

6 - The observation that PLEKHG3 silencing leads to loss of the perinuclear clustering of LAMP1-positive vesicles, and increase in their accumulation at the cell tips, is not referred in the text.

Answer: While this might seem the case in part of the cells shown in the representative image in Figure S2C, population-level analysis (n > 30 cells) did not support a shift in lysosome distribution with PLEKHG3 silencing.

__Figure 1 for Reviewer 2: __Lysosomal distribution in HeLa cells transfected with either siScr or siPLEKHG3. X-axis is relative distance from the nucleus and Y-axis the normalized intensity of the LAMP1 channel. Results are averages of >30 cells from one experiment (only displayed in “final revision” document).

Similar results were obtained using two independent PLEKHG3 KO cell lines, and are shown in Figure S4A

__Extract from revised Figure S4A-C: PLEKHG3 KO does not influence lysosomal distribution or cell morphometry: A) __Quantification of lysosomal distribution in WT compared to two KO cell lines. N ≥ 50 cells in three biological replicates.

7 - Fig. 2C is not referred in the legend.

Answer: We stand corrected and have changed the legend of Figure 2 accordingly on page 41.

8 - Figure S3A and B: authors should show the colocalization of endogenous PLEKHG3 with phalloidin and not only the GFP-tagged protein.

Answer: We thank the Reviewer for this comment and have performed this experiment showing the colocalization of endogenous PLEKHG3 with F-actin structures stained by Phalloidin. Even though the endogenous PLEKHG3 staining in HeLa cells is rather weak, sites where membrane protrusions are formed are clearly marked with PLEKHG3 staining below the plasma membrane. These data confirm the specific colocalization of PLEKHG3 with Phalloidin shown in the revised Figure S3A. See also the extract from Figure S3A below.

Extract from revised Figure S3A: Immunofluorescence images of HeLa cells. A) HeLa cells stained with PLEKHG3 (red) and Phalloidin (green). The nucleus is indicated by DAPI staining (blue). Scale bar = 50 µm. Insets on the right as indicated by white box in image on the left. Scale bar = 10 µm. Line plot corresponds to white line in merged inset.

9 - In page 14, authors refer to Fig. 3G, which does not exist.

Answer: We stand corrected, the sentence on page 14, line 9 (now page 26 line 24 in revised document) refers to Figure S3G.

10 - In page 30 and page 32, different antibodies for LAMP1 and PLEKHG3 are mentioned, but in the figure legends authors do not refer which one they used.

Answer: We tried different PLEKHG3 antibodies but ended up using only one. The other antibody has been excluded from the list on page 32, line 18 (now page 9, lines 4-5 in revised manuscript). We have specified which LAMP1 antibodies were used in which Figure in the Material and Methods on page 6, line 23 and page 7, line 4-5.

11 - In page 33, where it reads "300 µm protein", it should probably read "300 µg protein".

Answer: We stand corrected. See changes on page 10, line 2.

Reviewer 3

A key issue … is that the authors focus solely on peripheral lysosomes as target compartments for PLEKHG3. This is not self-evident, particularly in light of images presented in Figures 2 and 3, where colocalization of PLEKHG3 with perinulcear lysosomes appears very likely. The authors should make differences/similarities they observe between effects on perinuclear versus peripheral lysosomes explicit both with data and in the text, if such differences exist.

Answer: The Reviewer is likely addressing the images in Figure 3, which were obtained by staining endogenous PLEKHG3 and do diffuse staining around the nucleus. This perinuclear haze is resistant to siPLEHG3 (revised Figure S2C) or to PLEKHG3 CRISPR-Cas9-mediated ablation (revised Figure S2H) and is not observed with the GFP-PLEKHG3 fusion protein (revised Figure S2E-F), which gives a less diffuse signal. This is why we are confident about the colocalization of PLEKHG3 with peripheral lysosomes.

Data presented in Figure 6 showing cell motility analysis is interesting and has potential to make the manuscript impactful. Similarly, data in Figure 4F (live cell imaging) looks attractive but is not informative in the absence of relevant genetic perturbations as comparisons. These types of experiments would benefit greatly from PLEKHG3 loss of function analysis, as well as mutational analysis in the over-expression setting.

Answer: We have now generated a PLEKHG3 KO cell line. Loss of PLEKHG3, however, had no effect on lysosomal distribution or morphometric parameters compared to WT cells, and it does not impact the suppression of protrusions/actin dynamics by KIF1A is preserved in KO, indicating PLEKHG3 is not required for this phenotype.

Mutational analysis of PLEKHG3–LAMTOR binding is not feasible in the absence of co-IP or other direct binding evidence (see revised Figure S6E,G displayed in the answer above).

Minor point: 1. Multicolor overlays with one of the channels in white is in my view not reader-friendly. Appreciating colocalization between endosomes/lysosomes, actin and G is very important for this study, and while is typically reserved to show overlay between green and magenta or green (standard for 2 channels), red and blue (standard for 3-channels). I therefore advise the authors to choose a different color combination throughout the figures when presenting microscopy images.

Answer: White as a channel color has been substituted for with red (in the 2- and 3-color images) or with blue (in the 4-color images) throughout the images of the revised manuscript, except for the stills from the videos that have not been changed because no colocalization analysis has been performed in this case.

1. Description of analyses that authors decided not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Reviewer 2

4 - At least Fig. 2F and 3A need quantification. Regarding cell motility, there is no quantification and the authors must perform a quantitative assay (despite stating that "As another measure of cell motility, analysis of the number of forming protrusions and retracting membranes..."). Not only this is not a measure of cell motility, but there the issue of what are "protrusions" referred above. Therefore, authors need to quantify the distance that the cells move and/or perform quantitative motility/migration assays.

Answer: We appreciate the Reviewer’s attention to detail and agree that the quantification of these figures is essential to understand the results. We believe that the Reviewer refers to Figure 3F and Figure 4A, as there is no Figure 2F, and Figure 3A only confirms the localization of endogenous PLEKHG3, as previously reported in (Nguyen et al., PNAS 2016). If our assumption is correct, then the salient aspects of Figure 3F, which is a representative image, are quantified

• in Figure 3C-E (endogenous PLEKHG3 colocalization with LAMP1/lysosomes)
• In Figure 4E and 5F-G (FA with LAMP1/lysosomes).
• Figure 4A is quantified in Figure 4C-E (GFP-PLEKHG3 colocalization with FAs, labeled with paxillin in this experiment, and LAMP1 colocalization with FAs). In response to the Reviewer's comment regarding the absence of quantification for cell movement/migration in our study, we apologize for any confusion that may have arisen from our use of the term "cell motility." We have clarified usage to mean membrane remodeling dynamics integral to migration rather than net displacement. To avoid overclaiming, we removed statements that could imply directed migration and focused on protrusion/retraction metrics and shape changes. In this context, our statement that lysosomal subcellular localization plays a role in cell motility remains valid. The relationship between membrane protrusive activity and motility is evident from our observations in cells overexpressing KIF1A-mCherry, where both membrane remodeling/protrusive activity and movement are significantly impaired compared to control cells (refer to Movie S7 vs. S6 and S10 vs. S9).

To address the Reviewer's concern, we have clarified our definition of motility in the introduction by stating on page 19, line 23 – page 20, line 2: "We demonstrate that PLEKHG3 colocalizes with lysosomes at focal adhesion and protrusion sites, and that the localization and function of this protein – and consequently, overall cell motility – are fundamentally dependent on lysosomal dynamics." This revision ensures that our results are accurately described and minimizes any potential confusion. Additionally, we have removed the statement on page 23, line 1 of the original manuscript. We apologize for any confusion our original wording may have caused and appreciate the opportunity to clarify our intentions.

Reviewer 3

1. The mechanism of PLEKHG3 action on lysosomes/late endosomes is underdeveloped in my view. In the absence of for instance mutational analyses to examine what drives the interaction of PLEKHG3 with LAMTOR3, as well as delineation of at least some molecular consequences of this binding, the study remains incomplete.

Answer: We are grateful for the Reviewer's feedback and concur that gaining insight into the mechanistic details of PLEKHG3's interaction with LAMTOR3 would be beneficial. We now consistently refer to PLEKHG3 as a L3 vicinal protein based on TurboID and lack of co-IP. Because L3 KO does not alter PLEKHG3 FA localization and we find no evidence for a stable complex, mutational binding analyses lack a clear readout and are beyond the scope of this revision. We emphasize the conceptual advance—lysosome positioning gates PLEKHG3 cortical enrichment at FAs while peripheral lysosome clustering correlates with more adhesive, less protrusive behavior—and explicitly flag mechanistic questions (e.g., integrin turnover, IQGAP, Rac1 pools) as future work.

We hope that the Reviewer will bear with us on this point, considering the novelty of our findings, which illuminate the interplay between lysosomes and actin dynamics as well as the role of PLEKHG3 in regulating cell protrusions—findings not previously reported in the literature.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Ettelt et al describes the identification of PLEKHG3 as a collaborator of the LAMTOR complex on lysosomes using proximity-based biotinylation. The biotinylation screen is well executed and controlled. The authors choose to follow up on PLEKHG3, a protein involved in actin dynamics, which they refer to as understudied (I let the validity of the latter statement to be evaluated by the editor). Generally speaking, the data are of good quality, and the manuscript is clear and well written. However, much of the evidence on the role of PLEKHG3 on lysosomes is suggestive at best and further investigation into its mechanisms of action is warranted. Some important points to address prior to publication are detailed below.

Major Points:

1. The mechanism of PLEKHG3 action on lysosomes/late endosomes is underdeveloped in my view. In the absence of for instance mutational analyses to examine what drives the interaction of PLEKHG3 with LAMTOR3, as well as delineation of at least some molecular consequences of this binding, the study remains incomplete.
2. A key issue possibly (but not necessarily) related to the point above is that the authors focus solely on peripheral lysosomes as target compartments for PLEKHG3. This is not self-evident, particularly in light of images presented in Figures 2 and 3, where colocalization of PLEKHG3 with perinulcear lysosomes appears very likely. The authors should make differences/similarities they observe between effects on perinuclear versus peripheral lysosomes explicit both with data and in the text, if such differences exist.
3. Data presented in Figure 6 showing cell motility analysis is interesting and has potential to make the manuscript impactful. Similarly, data in Figure 4F (live cell imaging) looks attractive but is not informative in the absence of relevant genetic perturbations as comparisons. These types of experiments would benefit greatly from PLEKHG3 loss of function analysis, as well as mutational analysis in the over-expression setting.

Minor point

1. Multicolor overlays with one of the channels in white is in my view not reader-friendly. Appreciating colocalization between endosomes/lysosomes, actin and G is very important for this study, and while is typically reserved to show overlay between green and magenta or green (standard for 2 channels), red and blue (standard for 3-channels). I therefore advise the authors to choose a different color combination throughout the figures when presenting microscopy images.

Significance

In principle, I consider this study to be of interest to the community of cell biologists working on the endolysosomal system and/or the actin cytoskeleton and its relationship to intracellular membranes. However, the authors find themselves in a rather crowded field. I feel that developing the mechanism of action of PLEKHG3 on lysosomes beyond this first submission could help with boosting the impact of the study. There is clearly something interesting going on, but what that is exactly, remains unclear in my view.

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Referee #2

Evidence, reproducibility and clarity

Summary: The authors use proximity-dependent labelling and mass spectrometry to identify cytoplasmic proteins that interact with lysosomes. They show that PLEKHG3 interacts with the LAMTOR complex; that PLEKH3 accumulates in focal adhesion sites, where it colocalizes with peripheral lysosomes; and that the increased translocation of lysosomes to the periphery leads to less "protrusions", as well as rounder cells and less motile cells.

Major comments: While the study is generally carefully performed and thorough, there are major shortcomings that affect the conclusions taken, namely the specificity of the PLEKHG3 antibody, the identification of "protrusions" and ruffles, several quantifications missing, and the data used to conclude about cell motility. There are also conclusions for which there is no concrete or solid evidence.

Specific issues:

1. Specificity of PLEKHG3 antibody: In Fig. S2, authors show that PLEKHG3 antibody recognizes 3 bands (above 100 kDa, above 130 kDa and 250 kDa) and all of them are reduced by the silencing of PLEKH3. Then, in Fig. 2A and C, authors only show the band above 130 kDa, despite implying that the specific band should be "much higher than the 134 kDa calculated from the aminoacid sequence of the protein". In Fig. 2 B, they show all the bands shown in Fig. S2 and presumably favor that the specific and is the 250 kDa one. Finally, in Fig. 2D, they show all bands and note that the band above 130 kDa is not specific. Therefore, authors need to conclude what is the specific band and always analyze the same one, and, possibly, use a different antibody or purify this one to remove non-specific binding. Without this, the main result of the paper, cannot be substantiated.
2. In page 12, authors state that "These results indicated that PLEKHG3 is a transient interactor, or a proximal, not directly binding protein, of L3" and in page 14 that "... PLEKHG3 is a proximal L3 protein rather than a transient physical interactor". It is not clear at all how did the authors reach such conclusions, nor they have data to conclude this. Indeed, they would have to express the proteins in vitro and test their interaction to conclude about a direct binding. They also do not know what is the stability of the interaction.
3. Still in page 12, authors state that "... two different membrane structures, protrusions and ruffles". What do the authors mean exactly by "protrusions", as there are several different ones (e.g., lamellipodia, filopodia, pseudopods)? And how can they distinguish between ruffles and, for example, lamellipodia? They need to use markers and more carefully analyze their morphology to be able to distinguish these. Like this, it is too preliminary.
4. At least Fig. 2F and 3A need quantification. Regarding cell motility, there is no quantification and the authors must perform a quantitative assay (despite stating that "As another measure of cell motility, analysis of the number of forming protrusions and retracting membranes..."). Not only this is not a measure of cell motility, but there the issue of what are "protrusions" referred above. Therefore, authors need to quantify the distance that the cells move and/or perform quantitative motility/migration assays.
5. It is not clear if in cells KO for PLEKHG3, the overexpression of KIF1A leads to more lysosomes localizing close to the PM, as well as more protrusions and more cell motility, as the authors only compare cell overexpressing GFP or GFP-PLEKHGL3.
6. Regarding the statistical analysis, authors assert that it was done using Student's t tests, unless otherwise stated. However, they never refer in figure legends other statistical analysis methods. If so, they cannot use such test, for example, in cases where more than two groups are compared.

Minor comments:

1. In the abstract, authors refer that cytosolic proteins are recruited to platforms on the limiting membrane of lysosomes. What do they mean by "platforms"? Is it microdomains?
2. In the Introduction, there is a period before the reference at the end of the first paragraph.
3. In the results, Fig. 1E is mentioned before Fig. 1D and Figure S1F before Fig S1E, which can be confusing.
4. All the immunofluorescence images need to be bigger, in general, and have zoom-ins, except Fig. 3A, 4B, 4F, and S2C. Also, in Fig. S1F, the green channel has different intensities and the V5-lyso signal is clearly saturated. Finally, Fig. S1D, S1I and S3F must be enlarged, too.
5. In page 9, where it reads "Figure 1K", should read "Figure S1K".
6. The observation that PLEKHG3 silencing leads to loss of the perinuclear clustering of LAMP1-positive vesicles, and increase in their accumulation at the cell tips, is not referred in the text.
7. Fig. 2C is not referred in the legend.
8. Figure S3A and B: authors should show the colocalization of endogenous PLEKHG3 with phalloidin and not only the GFP-tagged protein.
9. In page 14, authors refer to Fig. 3G, which does not exist.
10. In page 30 and page 32, different antibodies for LAMP1 and PLEKHG3 are mentioned, but in the figure legends authors do not refer which one they used.
11. In page 33, where it reads "300 µm protein", it should probably read "300 µg protein".

Significance

The study provides evidence that lysosome positioning can affect cortical actin cytoskeleton dynamics, as well as cell shape and motility. Experiments are in general thorough and data subjected to quantification. However, there are fundamental conclusions that are preliminary at this stage, as some of the data is not yet solid enough. Therefore, it needs to be further strengthened to be considered for publication. In general, it reads well but the amount of abbreviations (e.g. in the case of the constructs) makes it somehow difficult to follow. The study will be interesting for the cell biology, membrane trafficking and cytoskeleton dynamics communities.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Ettelt et al., describes identification of Rho guanine nucleotide exchange factor- PLEKHG3 as one of the positive hits from a TurboID proximity-dependent labeling screen using LAMTOR3 (one of the subunits of the pentameric LAMTOR complex/Ragulator) as a bait protein. The authors find that PLEKHG3 colocalizes with lysosomes at focal adhesions and that peripheral clustering of lysosomes promotes PLEKHG3 localization near the plasma membrane, and also inhibits protrusion formation and cell motility. The experiments, particularly the Turbo ID proximity-dependent labeling screen, are well-executed, and the imaging data is aptly quantified. The manuscript explores an exciting question of how lysosome positioning regulates cortical actin dynamics and thereby cell motility.

Major comments:

• The colocalization of endogenous PLEKHG3 and LAMP1 as depicted in figures 3B and 3C (data from fixed cells) is not convincing. PLEKHG3 appears to be present on cortical actin structures as opposed to being colocalized with LAMP1 on lysosomes. The authors should also confirm the specificity of the PLEKHG3 antibody in immunofluorescence using control and PLEKHG3 siRNA in untransfected cells that have not been transfected with GFP-PLEKHG3 (as is shown in Fig. S2C). Numerous antibodies recognize the overexpressed protein but do not recognize the same protein at endogenous expression levels.

Moreover, do the authors observe colocalization between GFP-PLEKHG3 and lysotracker in living cells? There is no apparent colocalization of PLEKHG3 and lysotracker in the movie S5. - The authors observe that GFP-PLEKHG3 is concentrated at the cell's periphery when KIF1A is overexpressed, whereas RUFY3 overexpression results in more cytosolic staining. To bolster their conclusion that a change in lysosomal positioning alters the subcellular localization of PLEKHG3, it is preferable to employ inducible techniques, such as the recently described "reversible association with motor proteins" (RAMP) (PMID: 31100061). The method is a rapid and reversible method for altering organelle positioning. It is still unknown whether PLEKHG3 is associated with lysosomes and mechanism of how positioning of lysosomes affects PLEKHG3 localization. - Similarly to the preceding point, the claim that "peripheral accumulation of lysosomes inhibits protrusion formation and limits cell motility" should be tested more rigorously using the RAMP method, preferably in living cells. Other approaches, such as overexpression/siRNA of Arl8b and other motor adaptors, such as SKIP/PLEKHM2, can be used to alter lysosome positioning and confirm this central findings of the manuscript. The authors could also consider including additional mechanistic data in order to comprehend how lysosome positioning controls cell motility. For instance, the RAMP approach could be employed to investigate cortical actin dynamics upon repositioning of lysosomes to the peripheral/perinuclear region. - It is not clear how the authors conclude that Figure 4E graph shows "the LAMP1 signal was stronger in paxillin-labeled FA compared to control regions". The 4E graph shows LAMP1 signal in GFP versus GFP-PLEKHG3 and shows a modest enrichment of LAMP1 in FAs in GFP-PLEKHG3 overexpression. LAMP1 enrichment in FAs is also not obvious in the image shown in Figure 4B. - In Fig. 2B, there appears to be a labeling error. The lanes 2,4 and 7 appear to be transfected with L3-T-V5 but labeled as GFP-V5-cyto. Here the PLEKHG3 band should be indicated. - Fig. 2C is an IP experiment as per the manuscript text but it is labeled as pulldown.

Significance

Using a TurboID proximity-dependent labelling screen, the authors identified an interesting subset of actin-remodeling proteins that interact with the lysosomal protein LAMTOR3. The authors further characterized one of these proteins, PLEKGH3, and found that lysosome positioning regulates PLEKGH3 localization, as well as plasma membrane protrusion formation and cell motility. This study suggests that lysosome peripheral accumulation could regulate cortical actin remodelling and consequently cell migration by regulating PLEKGH3 localization (although this is not tested in the manuscript). This study adds to the previous findings that microtubule-based transport of late endosomes regulate delivery of late endosomal LAMTOR proteins to the vicinity of focal adhesions, which in turn, regulate focal adhesion dynamics. The mechanism of how lysosomes can influence actin remodeling will be important in the context of cancer cell migration. My area of expertise is lysosome fusion and motility and I have limited expertise in regulation of actin dynamics and how Rho family members regulate actin remodeling.

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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 #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors investigate the role of Transcription Termination Factor 2 (TTF2) in the regulation of mitotic transcription. Using siRNA-mediated knockdown in two distinct human cell types combined with nascent RNA labeling (EU pulse), the authors identify an unexpected role for TTF2 in the timing of RNA Polymerase I (Pol I) reactivation following mitosis. The study suggests that this temporal misregulation may have downstream consequences for nucleolar morphology and function in interphase. The manuscript is well-written, and the figures are of high quality and clearly presented.

Major comments:

1. A primary limitation of the current study is that it does not deeply explore the underlying mechanism of the observed phenomenon. To strengthen the claims, the following points should be addressed:

1a. Directionality of Phenotype: In Page 9, the authors conclude that TTF2 depletion is linked to abnormal nucleolar organization during interphase. It remains unclear if this is a direct result of mitotic misregulation or an independent interphase effect. To distinguish between these possibilities, I suggest the following experiment: perform a mitotic shake-off early in the siRNA treatment (~24h), collect mitotic cells, and allow them to re-enter G1 to image for nascent RNAs and nucleolin. This would clarify if the mitotic defect precedes and causes the interphase morphology changes. Alternatively, the authors should state that their current study cannot distinguish between these two possibilities.

1b. Secondary Effects: The long duration of siRNA treatment (48h) raises the possibility that TTF2 knockdown misregulates the expression of other Pol I regulatory factors, leading to secondary effects. This limitation should be explicitly acknowledged in the Discussion. 2. The term "significant" is used throughout the manuscript without accompanying statistical testing.

2a. Please provide statistical analyses (e.g., p-values) for the average plots in Figures 1-3 to substantiate the findings.

2b. Where statistics are not performed, the language should be softened to "notable" or "observed increase" rather than "significant." 3. siRNA knockdowns are generally supported by quantification. Please provide the percentage reduction of the target protein by quantifying the blots provided in the supplemental figures. 4. To rule out the possibility that the increased nucleolin signal observed after TTF2 KD is simply due to higher protein abundance, the authors should perform a western blot to confirm that total nucleolin protein levels remain unchanged upon TTF2 depletion.

Minor comments:

1. The abstract and discussion refer to the role of TTF2 as a "conserved" process. As the study only tested human cell lines, "conserved" is technically inaccurate (as it implies evolutionary comparison). I recommend using "general" or "cell-type independent."
2. While the Methods section is detailed, the Results section would benefit from brief descriptions of the treatments to improve flow.

Example revision (Page 4): "...we treated two distinct cell lines with control and TTF2-specific siRNAs for 48 hours, followed by a 30-minute EU pulse to label nascent RNAs. Click chemistry and Hoechst labeling enabled 2-color imaging of mitotic chromosomes and nascent RNA..." 3. The data generally agree across both cell types; however, the presence of clustered signals in HeLa metaphase chromosomes is a notable divergence. It would be beneficial to include speculation in the Discussion on whether this represents a failure to silence Pol I transcription or an even earlier reactivation, and what this implies about a cancer cell line.

Significance

General assessment:

The study is strong in its use of two different cell systems, providing confidence that the observed effects are not cell-line-specific. The figures are beautifully presented and the writing is clear. The primary limitation is the lack of mechanistic depth regarding how TTF2 specifically interfaces with the Pol I machinery compared to its known roles with Pol II.

Advance:

This work reports a previously unrecognized role for TTF2 in the temporal control of Pol I reactivation. While TTF2 is well-known for its role in terminating transcription and facilitating Pol II release during mitosis, its specific influence on the nucleolar transcription cycle provides a new perspective on how cells transition out of the mitotic state.

Audience:

This research will be of interest to researchers in the fields of gene regulation, the cell cycle, and nucleolar biology. Because it touches on the fundamental process of how transcriptional machinery is reset after cell division, it has implications for the broader basic research community interested in epigenetic memory and cellular identity.

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Referee #1

Evidence, reproducibility and clarity

In this paper by the Oliveira lab a new perspective on TTF2 function during mitosis is proposed. Known for its role to terminate transcription at mitotic onset, this paper further shows an exciting involvement of TTF2 to schedule timely rDNA transcription at mitotic exit. Moreover, this role is shown to have a clear importance in the structuration of nucleoli, since TTF2 depletion is associated with premature partial assembly of nucleoli on the mitotic chromosomes and, subsequently, to fragmented nucleoli in interphase. These conclusions, which are well supported by imaging data, are original, interesting and, in fact, largely unexpected.

The paper is very simple in its execution, based on siRNA depletion of TTF2 and monitoring of transcription by imaging using EU incorporation and rRNA-FISH, as well as nucleoli morphology and dynamics using immunostainings. Yet, it is well executed and has no major caveats. However, the authors should consider the following:

1. The Teves lab has shown that TBP is a key factor maintaining its binding at rDNA loci during mitosis, enabling a prompt reactivation of rRNA production in interphase (Kwan et al. RNA 2024). This paper should be discussed on the light of current findings.
2. In relation to the previous comment, I would strongly recommend the authors to analyse TBP-depleted cells, ideally using the line generated in the Teves lab, to address whether delayed rDNA transcription after mitosis leads to delayed nucleoli structuration. This assay would allow them to further confirm their model.
3. In addition, it would be important to test if in the absence of mitotic TBP, the depletion of TTF2 does also lead to mitotic transcription.

Significance

Strengths: originality of the observation and simplicity of the experimental setup

Limitations: exclusively based on imaging data

Advance: completely unanticipated observation

Audience: general readers interested in gene regulation

My expertise: gene regulation through mitosis

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Reply to the reviewers

Manuscript number: RC-2026-03407

Corresponding author(s): Laura Cantini, Julio Saez-Rodriguez

[The "revision plan" should delineate the revisions that authors intend to carry out in response to the points raised by the referees. It also provides the authors with the opportunity to explain their view of the paper and of the referee reports.

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If you wish to submit a full revision, please use our "Full Revision" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

We thank both reviewers for their thorough and constructive evaluation of our manuscript.

Reviewer 1 highlighted that the manuscript would benefit from 1) a stronger positioning of ReCoN within the existing literature on multicellular modelling and network exploration, 2) a justification of our methodological choices, including the use of Random Walk with Restart (RWR), 3) the choice of input datasets for GRN inference and an assessment of the robustness of ReCoN's predictions to noise in these networks, 4) a more systematic exploration of ReCoN's parameter space (restart probability, layer transition probabilities, filtering thresholds).

Reviewer 2 raised concerns about 1) the generalisability of the α parameter value (by default, 0.8) across independent datasets, 2) the expected contribution of the indirect effect in prediction performances, 3) the robustness of GRN across datasets and systems, and 4) the need for more quantitative validation in the spatial/microenvironment showcase. They also pointed out an unsupported claim regarding gene knockout prediction in the abstract.

Several clarifications on figures, methods, and writing were also requested by both reviewers.

As the main addition to the manuscript, we propose a new showcase based on the recently published Human Cytokine Dictionary (Oesinghaus et al., 2025). This showcase will simultaneously address several reviewer concerns by allowing us to 1) test the robustness and performance of α = 0.8 in an independent dataset, 2) evaluate the impact of different GRN inference methods (HuMMuS, SCENIC+, CellOracle, GRNBoost2) and noise on ReCoN's predictions..

We will conduct a systematic parameter exploration on the Heart Atlas showcase, covering restart probability and inter-layer transition probabilities. We will additionally strengthen the validation of the microenvironment showcase by providing additional comparison to matched single-cell fibroblast data.

Regarding the manuscript, we will substantially expand the discussion to better contextualise ReCoN within existing multicellular modelling approaches and the methods to justify our methodological choices (RWR/MultiXrank, dataset selection). We will remove the unsupported gene knockout claim from the abstract and reframe it as a future direction. In addition, we will clarify the distinction between ReCoN variants and rename them for clarity in the results section 1.2., improve figure legends. Finally, we will also work on the tool's documentation, including new tutorials on using spatial data and on running ReCoN with scRNA-seq-only GRN inference.

We believe these revisions will substantially strengthen the manuscript and address the reviewers' concerns regarding method's robustness, generalisation, and contextualisation.

2. Description of the planned revisions

Reviewers' comments are in blue

Authors' answers are in black

Proposed text modifications are in green

Reviewer #1

R1.1. This is a very well-written paper; the methods used are adequate, and the use cases are relevant and broad, exploiting state-of-the-art datasets and tools.

The author's claims are mostly justified. The authors could make an effort to more explicitly cite other efforts in similar directions. The claim 'We envision ReCoN as an extension to prior multicellular modelling, offering an interesting compromise between prediction of cell type responses and understanding of their molecular coordination.' is very general and could be better substantiated. In fact, the authors do not really give examples of alternative approaches to study systems of interacting cells, other than mechanistic agent-based models, which are clearly very different.

Response:

We thank the reviewer for pointing out the lack of contextualisation for ReCoN in this closing discussion.

We wanted to remind that ReCoN builds notably on multicellular factor decomposition methods. We also want to emphasise the interest in completing cell communication methods that describe the big picture in multicellular interactions.

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We proposed to *explicitly state these two points with such rephrasing: *

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Network-based representations of multicellular systems have been an active field for many years, from early conceptual cytokine networks (Frankenstein, Alon, and Cohen 2006) to curated ligand-receptor cascades of hematopoietic tissue (Kirouac et al. 2010, Qiao et al. 2014). In parallel, and from bulk RNA-seq, the consideration of tissue specificities in GRN inference has been another way to consider the importance of the context in molecular mechanisms reconstruction (Sonawane et al. 2017). Single-cell analysis allowed decomposing tissue composition and quantifying gene expression, opening the possibility of scaling the inference of these networks and the inference of multicellular mechanisms in general, to large sets of molecules. Several methods have been developed to recover multicellularity. A first direction extends ligand-receptor interaction inference into the receiver cell response through curated signalling cascades, yielding ligand to target cascades (Browaeys, Saelens, and Saeys 2020, Jin et al. 2021, Zhang et al. 2021, Yan et al. 2025). A second direction leverages spatial context through explainable multi-view models that decompose marker variation in both intra- and intercellular contributions (Arnol et al. 2019, Tanevski et al. 2022), without considering the mediating cascades. Finally, the more recent family of multicellular factor decomposition methods focuses on the coordinated aspect of cellular programs rather than on the mechanisms. ReCoN's methodology proposes a network-based approach based on single-cell data and the philosophy of this last group of methods. Indeed, ReCoN aims to retrieve links between molecular drivers and such coordinated multicellular programs by bridging and exploring CCC inference and GRN modelling (Badia-i-Mompel et al. 2023) within large and coherent heterogeneous multilayer network.

Arnol D, Schapiro D, Bodenmiller B et al. Modeling Cell-Cell Interactions from Spatial Molecular Data with Spatial Variance Component Analysis. Cell Rep 2019;29(1):202-211.e6. https://doi.org/10.1016/j.celrep.2019.08.077.

Badia-i-Mompel P, Casals-Franch R, Wessels L et al. Comparison and evaluation of methods to infer gene regulatory networks from multimodal single-cell data. Preprint, bioRxiv, 21 Dec. 2024, 2024.12.20.629764. https://doi.org/10.1101/2024.12.20.629764.

Badia-i-Mompel P, Wessels L, Müller-Dott S et al. Gene regulatory network inference in the era of single-cell multi-omics. Nat Rev Genet 2023;24(11):739-54. https://doi.org/10.1038/s41576-023-00618-5.

Browaeys R, Saelens W, Saeys Y. NicheNet: modeling intercellular communication by linking ligands to target genes. Nat Methods 2020;17(2):159-62. https://doi.org/10.1038/s41592-019-0667-5.

Frankenstein Z, Alon U, Cohen IR. The immune-body cytokine network defines a social architecture of cell interactions. Biol Direct 2006;1(1):32. https://doi.org/10.1186/1745-6150-1-32.

Jin S, Guerrero-Juarez CF, Zhang L et al. Inference and analysis of cell-cell communication using CellChat. Nat Commun 2021;12(1):1088. https://doi.org/10.1038/s41467-021-21246-9.

Kirouac DC, Ito C, Csaszar E et al. Dynamic interaction networks in a hierarchically organized tissue. Mol Syst Biol 2010;6(1):MSB201071. https://doi.org/10.1038/msb.2010.71.

Oesinghaus L, Becker S, Vornholz L et al. A single-cell cytokine dictionary of human peripheral blood. Preprint, bioRxiv, 15 Dec. 2025, 2025.12.12.693897. https://doi.org/10.64898/2025.12.12.693897.

Qiao W, Wang W, Laurenti E et al. Intercellular network structure and regulatory motifs in the human hematopoietic system. Mol Syst Biol 2014;10(7):MSB145141. https://doi.org/10.15252/msb.20145141.

Radig J, Droit R, Doncevic D et al. Tracking biological hallucinations in single-cell perturbation predictions using scArchon, a comprehensive benchmarking platform. Preprint, bioRxiv, 27 June 2025, 2025.06.23.661046. https://doi.org/10.1101/2025.06.23.661046.

Sonawane AR, Platig J, Fagny M et al. Understanding Tissue-Specific Gene Regulation. Cell Rep 2017;21(4):1077-88. https://doi.org/10.1016/j.celrep.2017.10.001.

Tanevski J, Flores ROR, Gabor A et al. Explainable multiview framework for dissecting spatial relationships from highly multiplexed data. Genome Biol 2022;23(1):97. https://doi.org/10.1186/s13059-022-02663-5.

Yan L, Cheng J, Nie Q et al. Dissecting multilayer cell-cell communications with signaling feedback loops from spatial transcriptomics data. Genome Res published online 12 May 2025. https://doi.org/10.1101/gr.279857.124.

Zhang Y, Liu T, Hu X et al. CellCall: integrating paired ligand-receptor and transcription factor activities for cell-cell communication. Nucleic Acids Res 2021;49(15):8520-34. https://doi.org/10.1093/nar/gkab638.

R1.2. Moreover, the exploration of the multilayer networks with RWR is a very reasonable choice but could there be other approaches? I think the authors could discuss this issue to briefly support their choice of this method.

Response:

It is a very relevant comment, as this choice has not been discussed in the paper; we propose extending the method section about ReCoN's networks exploration with a justification about this choice.

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There is currently a limited set of network exploration methods that have been implemented for multilayer networks. It includes notably pymnet (Nurmi et al., 2024), natively adapted to heterogenous multilayer networks, and multinet (Bagavathi et al., 2019) and muxviz (De Domenico et al., 2015), initially developed for multiplexed networks (e.g. social network where the same set of nodes is present in each layer) but adaptable to more complex multilayer networks. However, to our knowledge, only MultiXrank proposes a robust measurement of proximity between each pair of nodes.

Indeed, pymnet does not propose implementation for pairwise distance, similarly for muxViz, which focuses on community and motif detection. Multi-net does propose pairwise distance based on shortest paths, but implements it only for nodes of the same multiplex (e.g. in our network, it would only be two genes, or two receptors, respectively). https://www.rdocumentation.org/packages/multinet/versions/4.3.2/topics/multinet.distance

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We provide the additional justification for choosing RWR and MultiXrank over a reimplementation of another method or an extension of another method.

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• The total complexity of the RWR is O(δm) - when the number of nodes is negligible compared to the number of edges, with m the number of edges and δ the number of iterations in the walk (Baptista et al., 2022 - Supp Notes 2.A; Jin W. et al, 2019). This linear increase with the number of edges is particularly interesting for large networks, such as ReCoN ones that can contain several million* edges. The number of iteration δ and the computational time increases inversely to the restart probability, which is an important factor to keep this probability high. *

• *

• *MultiXrank is particularly interesting for its flexibility as it allows to easily attribute different weights to the different layers and to precise the direction of the exploration easily. *

• *

• It also produces deterministic results by prolonging exploration until convergence.

• *

• Additionally, in the context of ReCoN, the indirect effect of each cell is run independently. We previously extended the implementation of multiXrank for running RWR in parallel in a previous work (Trimbour et al., 2024), making it already adapted for optimising ReCoN's explorations.

• *

For all these reasons MultiXRank implementation seemed to be the best choice for robust and efficient exploration of ReCoN's HMLN.

• *

Bagavathi, A., Krishnan, S. (2019). Multi-Net: A Scalable Multiplex Network Embedding Framework. In: Aiello, L., Cherifi, C., Cherifi, H., Lambiotte, R., Lió, P., Rocha, L. (eds) Complex Networks and Their Applications VII. COMPLEX NETWORKS 2018. Studies in Computational Intelligence, vol 813. Springer, Cham. https://doi.org/10.1007/978-3-030-05414-4_10

Manlio De Domenico, Mason A. Porter, Alex Arenas, MuxViz: a tool for multilayer analysis and visualization of networks, Journal of Complex Networks, Volume 3, Issue 2, June 2015, Pages 159-176, https://doi.org/10.1093/comnet/cnu038

Nurmi et al., (2024). pymnet: A Python Library for Multilayer Networks. Journal of Open Source Software, 9(99), 6930, https://doi.org/10.21105/joss.06930

Jin, Woojeong, Jinhong Jung, and U. Kang. "Supervised and extended restart in random walks for ranking and link prediction in networks." PloS one 14.3 (2019): e0213857

R1.3. Generally the discussion should provide the reader the context in the existing literature in which the work can be set, detailing its impact. I think this could be improved.

Response:

• *

We hope that the correction on the context proposed for comment R1.1 offers a first clarification on the context in the literature.

• *

We also propose to extend the description of ReCoN's impact with the following sentences in the discussion: "Unlike purely data-driven approaches, ReCoN contextualizes prior knowledge balancing both robustness through literature data, and specificity through new measurements. This mechanistic approach opens new possibilities for understanding how cellular coordination shapes tissue-level responses and for designing targeted molecular interventions."

• *

R1.4. Regarding the choice of datasets, it is clear that the method is quite demanding, requiring single cell and different omics to build the model, in addition to the expression dataset that is used as a use case. This inevitably leads to using a mix of datasets.

For example in the mouse experiments the gene regulatory network was inferred from both a lymph node scRNA-seq dataset and a splenic scATAC-seq dataset, presumably due to the lack of multiome data in this setting. However the cell-cell communication network was inferred from the control case of the Immune Dictionary. Why can't the authors use the control data also for inferring GRNs?

Is atac-seq really necessary in the inference of the GRN? What is the impact of the fact that lymph node and spleen samples might be different?

:

• *

Is it a very *interesting comment, and we propose to add both 1) an explanation about our dataset choice to generate the GRN as a Supplementary text, and 2) a new experiment about the effect of GRNs built from multi-omics and scRNA-seq alone. *

• *

• Dataset choice

• *

We decided to infer a GRN using multiomics data, as these methods seem to perform better and are becoming the state of the art (Badia-i-Mompel et al. 2023, Trimbour, Deutschmann, and Cantini 2024, Yuan and Duren 2025).

As scATAC-seq data was not produced for the Mouse Immune dictionary, we tried to find an external dataset, used HuMMuS, the method we previously developed, as it is also based on RWR and performs well on unpaired data.

• *

scATAC-seq

Our first criteria was to match the mouse model used in the immune dictionary dataset, which reduced importantly the number of multicellular immune cell datasets available. We extended our research to a splenic dataset, as spleen is itself classified as a high specialised lymphatic structure, (check) and contains notably the same cell types than classical lymph nodes.

• *

scRNA-seq

While we could technically use the control mice of the Immune Dictionary single-cel RNA-seq data with the spleen scATAC-seq data, the Immune Dictionary only provides 100 or less cells for each cell types per stimulation, which would results in a low number of cells. As GRN quality seems to depend a lot on the number of cell used, we favoured choosing a larger dataset.

• *

Our choice to use single-cell multiomics methods was driven by the novelty of these methods over scRNA-seq based ones, the performance improvement that they seemed to offer in several benchmarkings, and the will of developing a pipeline integrating the most complete data available for contextualization (Badia-i-Mompel et al. 2024).

• *

• GRN impact over the Human Immune Dictionary

• *

While it does not relate directly to this showcase, we will also add a new dataset analysis, detailed in the the comment R1.12. In the Human Cytokine Dictionary showcase,, we propose exploring the effect of choosing different GRNs, built from external multi-omics data or from the control scRNA-seq data of the dataset itself. We hope it can partially help users to decide in general wether to use external datasets of higher quality or sample-specific datasets.

• *

Finally, we propose to add in the documentation of the tool, a section showing how to use ReCoN with only scRNA-seq for the GRN inference, and the performance of different GRNs for the Human Cytokine Dictionary dataset directly in the paper.

• *

R1.5. The code is very clear, we were able to install and run it and it is quite well-documented. However, a few more details should be given in the text regarding how the evaluation of the performance is carried out.

For example: If I understand correctly, when predicting the impact of cytokine perturbations the ReCoN predictions of genes impacted are compared to differentially expressed genes identified through traditional DEG analysis. What is compared is the ranking of these genes from ReCoN with the ranking provided by DEseq2. There is no description of how this comparison of ranking gives rise to AUROC values. Also, is it just the ranking that is predicted or can they also estimate how well they can predict the effect size?

Response:

• *

We are thankful for pointing out the unclear technical details. DEG results were binarised, to obtain the list of differentially genes using the thresholds indicated in the section 4.4.4. We considered a gene as perturbed in each cytokine treatment if the comparison of control and treated cells had a t-test p-value below 0.1 and if the log-fold change was above 1.

• *

The second, and more general point of the reviewers, ReCoN scores should be considered to provide ranking on the possible regulations, but cannot be considered proportional to the effect size. As they are represent a likelihood more than a score, the binarisation should be the most appropriate transformation for the validation

• *

*Moreover, as the scores can be seen as the probability to end up the exploration on each node, they are always summing to one. This also prevents interpreting the scores as the amplitude of change. As an illustration example: if a receptor regulates three genes identically, they would (hopefully) all be having a score of (1 - R)/3, R being the restart probability in ReCoN, whether their expression doubles or is multiplied by 10. *

• *

While it can legitimately be seen as a downside, we believe it is similar in practice to most methods inferring GRN methods in practice, where trying to predict the true amplitude of gene perturbations usually results in very low performances (Badia-i-Mompel et al. 2024).

• *

We propose changes related to this comment.

• *

• We would modify the section 4.4.4. of the method with the following paragraph to explicit that it consists in a binary selection: "For each cytokine-cell type pair, differentially expressed genes were binarised: genes passing the significance thresholds (FDR P-val 1) were labelled as positives, and all remaining genes as negatives. ReCoN scores were then used to rank all genes, and AUROC values were computed from this ranking against the binary labels."

• *

• We will also include a section "ReCoN scores interpretation" on the documentation website, as score interpretation precisions will be particularly useful for users.

  R1.6. When describing the use cases, I think a bit more detail would help.

For example 'To identify the cell-type-specific genes associated with HF, we used the MOFAcell scores of the multicellular factor 1 (MCP1) reported in ReHeat236' I supposed the explanation is on the dataset but for the sake of clarity it would be good to expand this sentence to give at least an idea of the approach.

Response:

• *

We completely agree that more explanations should be provided, to avoid for the reader having to switching between articles to understand the concepts behind this showcase. As suggested by the reviewer, we propose a general description of the approach with the short paragraph, and to remove the term "loading":

• *

"In the ReHeat2 study, the first multicellular factor (MCP1) was associated with heart failure. We used the gene loadings of MCP1 as a proxy for the cell-type-specific transcriptomic changes associated with heart failure, ranking genes by their absolute loading values."

• *

We also propose to complete the method section: "MOFAcell is a multicellular factor analysis method that decomposes multi-sample single-cell data into latent factors representing coordinated gene expression patterns across cell types. Each factor is characterised by cell-type-specific gene scores, reflecting their individual contribution to the coordinated program. In this showcase, we use the first multicellular program (MCP1), as it was associated with heart failure"

R1.7. Regarding the calculation of the R matrix from the NichNet matrices L and G, I gather that the R matrix is calculated once and is thus fully data-independent and available just like the L and G matrices from NichNet. This was not very clear in the tutorials.

Response:

• *

We are very thankful for the reviewers' involvement in testing the tools itself and its documentation. First, we propose a new website page explaining the pre-computed resources available for receptor - gene links, and added a descriptive paragraph in the tutorial themselves.

*Second, we notice a typo in the equation, where it should actually be L = R * G with the current definition. We corrected it in the next version, and precised that R is fully data independent and solely inferred from prior knowledge. *

R1.8. Also, this might just be a typo in the tutorial: 'The default α = 0.8 gives more weight to direct effects, which has been empirically validated. You can adjust this based on your biological question." I believe the manuscript says alpha>0.5 refers to indirect effects dominating.

Response:

• *

We corrected the saying in the tutorials. Indeed, a high alpha represents a stronger indirect effect. Additionally, a similar typo was in the first equation of the paper, we are correcting it too.

R1.9. Same for the pre-processing of the spatial data for the third use case, a little more details on how this was done would help the users and readers.

Response:

• *

We propose adding a specific section about the spatial pre-processing and analysis in the methods.

We are also adding a tutorial on spatial data. Since spatial data processing is computationally intensive without GPUs, we will also provide the data already processed, in order to allow anyone to test this tutorial too.

• *

R1.10. I don't see issues with the statistical power of the analysis.

Rather, I think the authors should provide some examination of the parameter space for their model. Whereas ana analysis of the impact of the Alpha parameter is provided, I believe there are several more parameters that have a crucial impact and choices for their values should be discussed.

For example 'In the GRN reconstruction only the links with a score above 1.5e-7 were retained in ReCoN's gene regulatory layer. How was this chosen?

We have identified the following parameters that are somehow justified but could be explored to have a better feel for how they impact the results

Restart probability: How often the walker goes back to the starting seed/molecule

Layer transition probability: How often the walker stays in the same layer - different cell? - different layers? Gamma

Node transition within a layer: How often one jumps to a different layer

Response:

This is a very valid point raised by the reviewer about parameters explorations.

• *

We focused on exploring the alpha (direct/indirect effect) parameter, as its value was the incertitude when designing the model.

• *

We would like to address this comment by adding new explorations for the restart probability and the transition probability between layers. The probability to transition between specific nodes inside a layer directly depends itself on 1) the restart probability, 2) the transition probabilities, and 3) the weights of the edges, that are determined before and independently to ReCoN's exploration.

• *

The Heart Atlas showcase allows to evaluate each set of parameters in around 10 min instead of 10h for the Immune Dictionary. We thus propose to evaluate restart probability and layer transition probabilities on the data of this showcase.

• *

• We would explore the restart probability of 0.1 * N, with N between 1 and 9.

• *

• For transitions probabilities we propose varying GRN, receptor, and cell communication importance with the following configurations: - Staying in CCC probabilities (- not jumping to receptor layer) among (0.1, 0.3, 0.5, 0.7, 0.9), staying in receptor layer (- not jumping to GRN) of (0.25, 0.5, 0.75), staying in GRN layer (- not jumping to CCC) of (0.25, 0.5, 0.75). It would result in 9 intracellular variations combined with 5 intercellular variations.

• *

We envision an evaluation by measuring the correlation between the results of the different configurations, and the time before convergence of the results, as it could potentially increase drastically when decreasing the restart probability. If correlations below 0.9 are observed between some results, we will compare their absolute performances.

• *

We would include the figures related to these explorations in the supplementary data. We would highlight the main findings in the method section dedicated to the random walk with restart. Finally, we would briefly describe the parameter exploration design in the first section of the results, for curious readers who would like to verify parameter choice before reading the showcases.

• *

R1.11. Weighting parameters: How much weight for direct or indirect effect to account for the combined effect - alpha - this is the only one that is explicitly explored.

Response:

We are very thankful for this comment, and we decided to modify our tutorial guidelines to make this choice more intuitive and general.

• *

Indeed, 1.5e-7 would hardly make sense for most methods, which would not produce such low scores. We now propose to select the first 2 million connections of GRNs, in order to keep a complete or a large portion of the network if other methods than HuMMuS are applied.

• *

In our case, 1.5e-7 was empirically determined from the distribution of HuMMuS scores, to keep the 2 million top connections as HuMMuS networks are generally almost fully connected, which is a particularity for classical GRN inference methods, and keeping it entirely would make exploration time much longer.

• *

R1.12. Finally, this might be considered OPTIONAL but would greatly improve the work in our opinion:

The method crucially depends on the networks that are used in the different layers and to connect layers and cell types. As we know, biological data is noisy and incomplete (FP and FN) at each level and in each datatype. It would be really useful to estimate what is the robustness of the results to this noise. Particularly, from personal experience, we think the GRNs reconstructed from data are often almost fully connected and it is exceedingly difficult to validate them in specific contexts. This means that some 'errors' are likely to be present.

Since several methods exist for inferring GRNs one could simply compare the results using different methods for this part of the network.

A related point involves the characteristics of the RWR algorithm, that will be quite impacted by the presence of hubs in these networks (either in single layers or across several) that is likely to impact the exploration. If proteins that are hub are effectively important, that is not a problem, but in some layers, for example, the receptor-receptor layer that presumably will contain PPIs, there might be biases in hubs being just better studied proteins, and these hubs might have an 'unjustified' weight in the walks.

One potential approach to assess the robustness of the method to these issues could be an empirical one that just randomly perturbs the networks in ReCoN to see to what extent similar predictions are achieved.

*Response: *

• *

We are thankful for this relevant comment on GRN and prediction stability, and would like to take it as an opportunity to support the hypothesis that different GRN methods can be used in ReCoN.

• *

When developing our previous HMLN-based tool, HuMMuS (Trimbour et al. 2024 - Supp Figure 6), we observed that its multilayer structure provided more robust results than individual layers. We would like to reproduce such an analysis, verifying that ReCoN results have less variability than the GRN layers individually.

We propose to integrate a new showcase on the Human Cytokine Dictionary (Oesinghaus et al. 2025), trying to predict cytokine downstream effects similarly to the Mouse Immune Dictionary showcase.

This showcase would be useful to confirm the contribution of the indirect effect and test the impact of different GRN on the results.

We would generate different GRN with several other GRNs methods: SCENIC+, CellOracle, and GRNBoost2 - the latest using only the scRNA-seq of the control samples in the Human Cytokine Dictionary.

• *

The GRN methods produce generally output with very low overlap (Badia-i-Mompel et al. 2024)*. *

*If we observe high correlations between the ReCoN predictions associated with the different GRNS, it would provide already a validation of ReCoN's robustness to GRN noise. *

If lower correlations between ReCoN's predictions are obtained, we will add a specific permutation experience over the HuMMuS GRN, creating different level of artificial noise and assessing more precisely the robustness of ReCoN to GRN stochasticity.

• *

Regarding PPI hub justification, our *applications did not use receptor PPI and are not affected by bias at this level in the showcases. This bias could specifically be present in the receptor-gene links, as we derive it from the ligand-gene connections of Nichenet which was itself partially based on prior knowledge. It is thus possible that some receptor are reached more often due to this bias and not a stronger effect. It seems however, hard to control in this context, as ReCoN currently relies on this prior knowledge. Currently, we hope that the combination of personalised, literature-agnostic GRN with literature-based receptor - gene can provide an interesting trade-off. In future development, we could imagine a receptor-gene network based solely on perturbations, but it would require controlling also the bias of ligand - receptor binding couples, which limits even the use of ligand-based experience. *

We propose adding a short point in the discussion about hub effects from RWR-based methods.

• *

R1.13. Please add page numbers.

*Response: *

• *

We will add the page numbers.

• *

R1.14. Figures are nice and clear.

Some specific minor points are listed here below.

Define hMLN on first appearance fig1 caption (no page numbers..

2nd appearance heterogeneous multilayer structure (HMLN) ...

Response:

• *

We updated the legend of the figure to include the definition of the acronym, as it arrives before first text occurrence. (Or define at both positions ?)

R1.15. Bi_j not so clear to what it refers when first mentioned

Response:

• *

*Bi_j represents a weight that can be attributed to favour some cell-to-cell transitions. It is usually not necessary to use them.

*

*It is of interest notably to model 1) known spatial patterns in situ and hypothesis/design where cell types favour some connections. *

• *

E.g.: for modelling the skin, a user might notably want to increase connections between epidermic and dermic cells, and between dermic and hypodermic cells.

• *

We propose a new explanation of Bi_j to both explain it's meaning in the modelling, and illustrates situations for using it: "The coefficient B_{i,j} modulates the influence of cell type i on cell type j in the indirect effect computation. By default, all B_{i,j} are set to one, weighting each cell type's contribution equally per cell. However, it can be adjusted to encode additional biological knowledge, such as spatial proximity between cell types or known cooperation patterns. For instance, when modelling the skin, a user might increase B_{i,j} between epidermal and dermal cells, and between dermal and hypodermal cells, to reflect their spatial organisation."

R1.16. personalized interaction specificity. - maybe better word than personalised (contextualised?)

Response:

• *

We agree that contextualised explicits better the meaning behind this model. Personalised might notably lead to expect patient-specific data, which is not the case here.

• *

We propose to rephrase all the model names to : Receptor-matrix, ReCoN-no-CCC, ReCoN-no-context, ReCoN-complete.

R1.17. ReCoN-genetic and ReCoN, ( generic?)

Response:

• *

We will correct this typo.

R1.18. responses. It is expected to observe common behaviors in-between cell-type, that the GRN

and the generic CCC network already contribute captures.

• not very clear

Response:

• *

We aimed here to provide an explanation to the already good performance of the "ReCoN-no-context" (or its name updated according to comment R1.16), which could be surprising as no cell-type specific information is used. The explanation proposed is the good prediction of several properties shared by all immune cell types, such as similar metabolic pathways, despite their specific roles. If we adopt a quantitative view on their transcriptome like in this showcase, it can be expected that the cell type responses are relatively well predicted through the common properties only.

• *

As this is a very relevant comment, and that several comments pre-submission we received were also related to this result, we would like to keep an explanatory sentence.

• *

R1.19. Figure 2b the icon of cells with double arrows might suggest phenotype shift when instead this is just communication

Response:

(left side) We are very thankful for paying attention to the details of the paper and fully agree with this analysis. We propose to represent ligand emission instead of arrows, reusing the convention of the Figure 1.

R1.20. eTACs explain acronym and what they are

Response:

• *

We update the first occurrence of eTACS to extrathymic Aire-expressing cells (eTACS).

R1.21. Due to very few genes being differentially

expressed, only cDC1 was conserved and evaluated for IL22,

Not so clear

Response:

• *

As we are commenting on IL22 stimulation results, we reorganised the sentence to make it less convoluted: "For IL22 stimulation, only cDC1 presented enough genes being differentially expressed."

R1.22. In this showcase (not very clear, use case?)

Response:

• *

We perceive "use case" as describing a type of use for the method, while a show case is a specific example of a use case. We thus find showcase more appropriate here. We will however go over all use of the word, to be sure it is only used for the precise examples we provided, and not to describe "use cases".

R1.23. different fibroblast specializations - maybe phenotypes?

Response:

• *

• • It is a very good suggestion, as specialisation would involve functional aspects (that we can't really be sure of), and a chronological evolution*
• Phenotype generally includes numerous properties, such as morphology, that we cannot validate here. We think the use of phenotype might be stronger than specialisation here. To simplify, phenotype can work, to be more precise: transcriptomic specialisation? I am honestly not sure of the best change here.

R1.24. Figure 4b

1. b) Schematic view of the deconvolution process and cell type-specific count inference from the spatial niches.

Not so clear what the heatmap shows, rows and columns

Spots heatmap : label niche on rectangles in cols

And each col is a spot

Rows are cell types or cells?

In the cell types x spot

Response:

This figure can indeed benefit strongly from legend modifications. On both matrix, lines represent the genes, while columns represent the spot / individual cells deconvoluted per spots

• *

• We would annotate the niche legend (here the colour surroundings) by a symbolic drawing instead of writing it on the matrix

• *

Legend "genes" on the first matrix

• *

Write deconvolution ON the figure directly

R1.25. Cell2location. Add reference, maybe explain basic functionality?

Response:

• *

Cell2location was not referenced in the results section, and was only referenced in the section 4.6.2 of the methods, as the 72th citation. We corrected this oversight, and propose 1) a brief explanation of deconvolution right before, 2) a brief explanation of Cell2location particularity in inferring individual cell profiles - which is not common in spatial deconvolution.

R1.26. reconstructing different patients, tissues, and microenvironments to predict

context-specific molecular treatments.

Unclear

fibrosis in different - at

molecular levels

Response:

• *

We will modify this section title according to the reviewer's citation and the different reformulation.

R1.27. Figure 5d myeloid and endothelial colour code inversed from 5 BC

Response:

• *

The legends are individually correct, but there is no reason to not make them coherent across panels. We will update the legend of the panel 5.d..

• *

R1.28. 5d indicate important pathways in organe should not change the colour of the nodes (purple=common, blue or green specific). Use border colour maybe?

Response:

• *

We had forgotten to precise the colour code of this panel, where the choice of orange highlighted here the gene set related to molecular pathways instead of functional annotations. As the name already explicits pathway, we now think that the orange background is redundant informations and may create some confusion. We thus would like to update Wnt and TNFA pathways backgrounds to ___ (more enriched in cell type), and purple (significantly enriched in all cell types).

R1.29. 5e is not a venn diagram

1. e) Venn diagram showing the overlap between transcription factors (TFs) predicted by ReCoN (green) and those previously

implicated in fibrosis (orange) or cardiac diseases (violet). Only the top 10 TFs were annotated from literature

sources; full sizes of fibrosis- and cardiac disease-related receptor sets can therefore not be represented.

1. f) also not a venn diagram e/f now in supp

the "NABA ECM collagens" gene set. Nodes are

grouped by molecular type (e.g., transcription factors, receptors, ligands), and links represent the weighted,

direct regulatory interactions present in the ReCoN-constructed

Response:

• *

As the diagrams do not indicate the total number of receptor/TF that are in the literature, it cannot be Venn diagrams. We updated the legend to :Venn diagram showing the Overlapp between [...]

• *

As we reorganised the paper, these plots are now only in supplementary; we removed the duplicate occurrence in the figure 5 legend.

R1.30. Why Sankey plot? Normally sankey plot represents flow (of regions changing from 1 state to another) but here this is just a weighted network?

No communication from firbos back to other cell types? No communication between ventricular/myeloid/lymphoid?

Response:

• *

We are thankful for this useful feedback which helped us realising interesting details were missing from the paragraph.

• *

*This is only intended for visualising regulatory cascade, so users have to decide on one receiving cell, a set of target genes, and sending cells. It includes a specific subset of regulatory cells, and only their interactions with the target cells. Here, we illustrated the regulation of some ECM genes produced by fibroblast. *

• *

Sankey Diagram might indeed not be the clearest representation, as we are not modelling the all diffusion, and not a flow per se. We propose to replace by another representation that we hope will be more intuitive for biologists (and more aesthetic), such as illustrated below:

R1.31. as a extension to - an

underrepresented in the current. - current framework?

Response:

• *

framework works perfectly to fill the missing word in the sentence

• *

R1.32. However, it can't represent more - cannot

Borrowing representation from hypergraphs, which introduces

The network exploration implementation of ReCoN also present some limitations.

limitations. While random walks

with restarts offer a stable and fast exploration workflow for multilayer networks, it

currently only considers positive weights to predict regulation strengths. It involves that the

nature of the regulation, as activation or inhibition, has to be identified a posteriori.

• check concordance/grammar

Response:

• *

We will update the raised grammatical errors

• *

R1.33. Only the nodes that are included in one of the layers are present in the

final results, ignoring the ones present only in bipartites.

Unclear

Response:

• *

Layers and bipartites are treated differently by the algorithm, and layer presence is necessary to appear in the results.

• *

In practice, it just means that receptors/ligands not paired in the CCC, or genes not regulated by any TF in the GRN, won't appear.

• *

We propose clarifying with this second explanation

• *

"In practice, a node must have at least one connection in its layer to appear in the final results. It thus means that receptors or ligands absent from the CCC network and genes not targeted by any transcription factor in the GRN will not receive a score from the random walk exploration."

• *

R1.34. a scATAC - an

• *

Barsi et al is published https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1013188

Response:

• *

We updated the reference with the published article.

R1.35. effects, allowing for modulating in a second

time their contribution. - word order

Response:

• *

We propose to formulate "allowing in a second time to modulate their contribution"

R1.36. others. However, it is possible to adjust the Beta coefficient to

represent it based on the available information for each dataset.

Represent- adjust?

Response:

• *

We agree with the reviewer's suggestion to use adjust.

R1.37. We use the latter to compare the different models. - what is the latter?

Response:

• *

The latter referred to the 25 cytokines of the Immune Dictionary which had at least one connection in the inferred cell communication network with CellPhoneDB. We propose clarifying this formulation to "..."

R1.38. It resulted in the scRNA-seq in 1,789 cells with 13,167

genes, and for the scATAC-seq in 3,759 cells with 254,545 regions.

Check english

Response:

• *

We propose replacing this sentence by the following: "It resulted in a scRNAseq dataset of 1,789 cells with 13,167 genes, and a scATACseq dataset of 3,759 cells with 254,545 regions."

R1.39. GRETA pipeline.- reference

Response:

• *

We added the citation to the paper of the GRETA pipeline in the section 4.5 of the methods: "Badia-i-Mompel et al., 2026"

R1.40. We kept all the cells whose annotations through unsupervised clustering,

followed by marker gene annotations, through scANVI were coherent.

Word order

Response:

• *

We propose the following reformulation to correct the sentence: "We kept all cells whose annotations were coherent between unsupervised clustering with marker-gene labelling and scANVI-based label transfer"

R1.41. In parallel, pairs of ligands and receptors with both associated with scores above

an absolute gene loading of 0.1 were considered potential driver interactions in HF.

Unclear

Response:

• *

In the MOFAcell results, factors correspond to linear combination of genes that explain a large part of the data variance; the contribution of each gene is called loading. We chose the factor that classified the best patient with and without fibrosis, and kept all the top genes, all of those with a score above 0.1.

• *

We propose reformulating this sentence as the word "loading" could overcomplicate here for most readers: "To identify the ligand and receptors driving heart failure, we considered all of those with an absolute contribution to the multicellular factor of 0.1."

R1.42. gseapy Python - reference?

Response:

• *

The gseapy package was indeed not cited, we now include the citation : "Zhuoqing Fang, Xinyuan Liu, Gary Peltz, GSEApy: a comprehensive package for performing gene set enrichment analysis in Python, Bioinformatics, 2022;, btac757, https://doi.org/10.1093/bioinformatics/btac757"

R1.43. and to calculate average for each spatial context the average cell type expression.

Unclear

Response:

• *

we propose to reformulate the sentence to: "These cell-type-spot profiles were used later for each spatial context to create a specific cell-cell communication networks and to calculate cell type average expressions."

R1.44. We only used the loadings of all cell

types but the fibroblasts to consider the effect of the sole environment.

Unclear

Response:

• *

we propose to use "APART from the fibroblast" to clarify the sentence and "to ONLY consider the environment effect".

R1.45. We realised a downstream - performed

Response:

• *

We fully agree with the reviewer's suggestion.

R1.46. The profiles inferred by ReCoN were first very correlated in all three contexts. - unclear

Response:

• *

The sentence was missing clarity and deserved being rephrased. We propose: "When looking at the absolute scores of ReCoN in all three contexts, results were initially highly correlated. To focus on context-specific differences, enrichments were performed using the log-ratio of each context profile over the mean of the other profiles."

• *

R1.47. Potentially the closest results are models that can predict the effect of perturbations on cell line cultures. Several approaches in the literature employ either transformers or optimal transport to predict the effect of perturbations in single cell datasets. One of the main issues is an underlying necessary assumption that the perturbation effect will be larger than the heterogeneity (in cell lines for example), which becomes increasingly difficult when considering in-vivo experiments. ReCoN obviously goes beyond this by considering explicitly the presence of different cell types but distinctions of cell types are sometimes quite arbitrary and potentially application of ReCoN to some of the in-vitro culture datasets, even on cell lines, could be a way to test its performance and benchmark it against other methods.

The main bottleneck in the application of this framework to 'personalisation' of therapies, mentioned even in the abstract as a potential future goal for such an approach, will be the lack of data. This approach requires single cell level descriptions of the system at hand, plus additional datasets to build the model structure. To a certain extent, public data of related tissues/contexts can be used, but it will be necessary to test the dependence of performance on coherence of the input data to develop sufficient trust to use it for new predictions, especially in a medical field.

• *

We thank the reviewer for these reflections, which raise several distinct points that we would like to add in the discussion.

Cell line perturbation is indeed a close and active field of research, with notably numerous models based on optimal transport and VAE and relevant benchmarks(Radig et al. 2025)*. In our view, ReCoN tries to take a complementary angle, by both focusing on the environment effect and using a network-driven approach providing explainability. *

These perturbation methods are typically benchmarked on single cell line screenings, where cell-cell communication is highly limited or absent by design, while ReCoN is specifically designed to exploit multiple cell types interactions. Furthermore, ReCoN relies on a network that aims to provide only explainable hypotheses and molecular cascades. They also typically learn from different data, as ReCoN only uses single-cell data and best perturbation prediction methods learn from a subset of perturbation experiments.

Exploring the performance of ReCoN in perturbation predictions would require designing extensive comparisons with the state-of-the-art taking into account all these nuances which we believe goes outside of the scope of the present study. It however still raises a fundamental question for the development of the next methods and the need to assess whether the perturbation effect is actually larger than the heterogeneity, and we propose to extend the discussion to cover these aspects.

Secondly, this comment raised a point about cell type definition, which can be a hard task and sometimes a wrong description of cells heterogeneity. We note that even if ReCoN relies on grouping cells in some way, it does not impose any particular cell type ontology: users can define their own cell types or cell states, since the CCC layer is typically inferred from single-cell RNA-seq alone and does not require canonical cell-type annotations. This flexibility allows ReCoN to accommodate finer or coarser groupings depending on the biological question. We do not propose a framework to take into account diversity in other ways than homogeneous clusters of cells, but we think that it constitutes an interesting future development of ReCoN or new multicellular modelling methods.

Lastly, we fully agree that an important limitation for ReCoN's use is data availability and generation, which was also a limitation when identifying datasets for the manuscript's applications. We hope that the development of open source atlases will make it easier to leverage tissue-specific prior knowledge and increase potential application, prediction performances, and trust in ReCoN results.

In conclusion, we propose to state in the discussion two new points:

*1) extending multicellular perturbations (including gene knock-out) to conditions where cell types cannot be defined prior to the analysis, or are more to consider across a spectrum, will be an interesting future direction. *

2) there is new a need for broad benchmarks covering both multicellular and single-cell line tasks to evaluate the trade-off between accounting for cell heterogeneity and overall prediction accuracy.

Radig, J., Droit, R., Doncevic, D. et al. scArchon: a scalable benchmarking framework for assessing single-cell perturbation models. Genome Biol 27, 162 (2026). https://doi.org/10.1186/s13059-026-04104-z

R1.48. The authors could comment on how their method compares to others that do not require single cell level information. Despite clear differences, it might be important to show the advantage of using this more complex approach that requires data that is less available. Given the ease with which bulk profiles can be constructed from single cell data, it might be possible to compare the approaches directly. For example, see

1. Wang, S. Patkar, J.S. Lee, E.M. Gertz, W. Robinson, F. Schischlik, D.R. Crawford, A.A. Schäffer, E. Ruppin Deconvolving Clinically Relevant Cellular Immune Cross-talk from Bulk Gene Expression Using CODEFACS and LIRICS Stratifies Patients with Melanoma to Anti-PD-1 Therapy

Mike van Santvoort, Óscar Lapuente-Santana, Maria Zopoglou, Constantin Zackl, Francesca Finotello, Pim van der Hoorn, Federica Eduati,

Mathematically mapping the network of cells in the tumor microenvironment,

Cell Reports Methods 2025

We propose to extend the discussion with additional methods, notably from before single-cell technology developments. We did not plan to include this two specific methods, as to our knowledge, they don't provide output directly comparable to ReCoN's purpose.

• The first work proposes to deconvolute the bulk RNA-seq profile into cell-type-specific expression profiles. It is an interesting reference, as it could allow applying ReCoN even to bulk RNA-seq, but they do not provide comparable results, as their final task corresponds to inferring the ligand-receptor interactions, without providing downstream molecular mechanisms.
• The second method proposed in this paper, RaCInG builds cell-to-cell networks for individual patients. They do not explore the molecular interactions inside the cells themselves, which could be used to build personalised ReCoN's model but seem to be more a prior to recent CCC than ReCoN itself.

• *

• *

Reviewer #2

R2.1. It is not clear how well it performs in independent validations. Authors showed that it can predict the effect of cytokine perturbations in the immune dictionary by selecting an optimal alpha. Authors should validate that using the same alpha value of 0.8, it is possible to accurately predict the effect of cytokine perturbations in independent datasets. This is particularly concerning for cytokine-cell type pairs where the optimal alpha is not known. Therefore, the potential utility of Recon to estimate the effect of multicellular perturbations is not well established.

• *

Response:

• *

*The reviewers raised a very relevant point by pointing out that the alpha coefficient might vary between datasets. *

• *

The value of 0.8 was chosen because it produced the best results in two independent datasets, the immune dictionary and the heart failure showcases. We could here observe some cross-dictionary reproducibility. To complete these findings, we will also verify that 0.8 provides the best performance in a new showcase: the Human Cytokine Dictionary (Oesinghaus et al. 2025)

• *

We tried to contrast this choice by opening on the need to confirm the importance of the indirect effect. We propose to add a sentence explicitly commenting on the impact of these new findings on the alpha coefficient and its robustness value.

• *

It is also accurate to say that ReCoN cannot currently estimate the alpha parameter autonomously. We proposed this default value as it worked on both datasets, but it is possible that no default value could fit them all. The value of alpha is currently a default value, but users are completely free in the current implementation of ReCoN to modify its value depending on their needs

If it was not the case, one option could be to fit its value using similar prior perturbations, when such data is available. For example, perturbing one or a few cytokines, a user could choose the value that explained the best the gene expression responses.

• *

R2.2. Authors claimed that optimal alpha value of 0.8 implies the dominance of indirect effect. But in contrast to this claim, the performance across cytokine-celltype pair only increased from 0.72 to 0.76, which seem to imply that indirect effects do not add much.

*Response: *

• *

The range of performance improvement is an interesting point to discuss for us, as it roughly doubles the computational time and consequently a trade-off between resource usage and this improvement.

• *

While the average improvement from combining the direct and indirect effects observed on the first showcase was around 5%, it reached more than 10% in some cell types. We consider that it still corresponds to an interesting improvement for the current task. Indeed, it here "only" incorporates the coordination of immune cells to a cytokine stimulation, which should not necessarily change their profile drastically compared to isolated exposition.

R2.3. How does the cell-type specific effects prediction perform by just considering the intracellular layers? The authors constructed multiple variants of ReCoN to estimate unicellular and multicellular effects. How is the variant ReCoN-grn different from full ReCoN where gamma is set to zero.

*Response: *

• *

We are thankful for this comment, which will help to restructure the section 2.2.

• *

As the ReCoN-GRN differs from the full ReCoN model, even with a gamma value of 0, as the latest include ligand-to-receptor weights. However, the ReCoN-GRN would correspond to the ReCoN-generic with an alpha of 0, which does not weight ligand-to-receptor links.

• *

We propose to clarify this detail in the section 2.2.2 by adding after the introduction of the ReCoN-generic model the sentence: "Note that ReCoN-grn corresponds to the ReCoN-generic model with alpha set to zero, where no indirect effects are considered. It differs from the full ReCoN model with alpha set to zero, which still includes ligand-to-receptor weights through the receptor-gene bipartite network."

R2.4. In section 2.2, authors assert that if matching datasets are not available, GRN layer can be extracted from other datasets. How well does the GRN layer from one system generalizes to the other system in terms of perturbation prediction?

*Response: *

• *

It is, of course, a complex question, as it probably strongly depends on the studied system. However, we believe while it is important to consider similar systems, using the same samples for the cell-communication and the GRN layer is not necessary.

• *

The first showcase that we propose explores exactly this case. We built the GRN from two unpaired datasets, and the cell communication from a third one. It provided convincing performances, justifying our earlier claim. It is additionally something done in most methods contextualising prior knowledge, which usually comes from other samples and sometimes even other organs (Browaeys, Saelens, and Saeys 2020, Jin et al. 2021, Badia-i-Mompel et al. 2023).

• *

To provide additional insights, we will run the new Human Cytokine Dictionary showcase using both 1) multiomics methods on external PBMC datasets, and 2) a single-cell RNA-seq only method on the Human Dictionary directly. We will then be able to show performances using both data and corresponding methods.

• *

To justify more clearly our claim according to reviewer's comment, we propose highlighting in the showcase itself this justification: ".... this showcase highlights the possibility to combine networks obtained from distinct datasets...".

Related to combining datasets, we propose to clarify the reasons behind our choices for the Immune Dictionary showcase with the additional supplementary text proposed in response to the comment R1.4.

• *

Badia-i-Mompel P, Wessels L, Müller-Dott S et al. Gene regulatory network inference in the era of single-cell multi-omics. Nat Rev Genet 2023;24(11):739-54. https://doi.org/10.1038/s41576-023-00618-5.

Browaeys R, Saelens W, Saeys Y. NicheNet: modeling intercellular communication by linking ligands to target genes. Nat Methods 2020;17(2):159-62. https://doi.org/10.1038/s41592-019-0667-5.

Jin S, Guerrero-Juarez CF, Zhang L et al. Inference and analysis of cell-cell communication using CellChat. Nat Commun 2021;12(1):1088. https://doi.org/10.1038/s41467-021-21246-9.

R2.5. In the abstract, authors claimed that ReCoN can predict the effect of gene knockouts. But authors did not show any application or validation to support this claim.

Response:

• *

We indeed had no showcase that could explicitly measure the performance of ReCoN directly for gene knockout, while the possible application was introduced in the abstract.

* We believe that ReCoN could be used in the future to infer such perturbations, but we fully agree that this claim cannot be presented without justification.

We propose to remove the introduction of gene-knockout there, and to introduce it in the discussion opening instead, specifying that it will require specific experience and constitutes a possible future extension of the work.*

R2.6. The communication between cells might be dependent on their spatial proximity. Is it possible to construct the CCC layer by incorporating the context-matched spatial data? How would that affect the performance of multicellular response prediction?

Response:

• *

*This is a very interesting comment as numerous methods using spatial transcriptomic data have been published recently. *

• *

In the current formulation, the beta coefficient Bi_j modulates the impact of the cell type i on the cell type j. If the spatial transcriptomic data can inform on the proximity between cell types, and its overall impact on their communication, users could enforce more communication between some.

• *

However, as ReCoN is a cell-type centric model, adding spatial information can only be done at a general scale, or by modelling independently spatial regions such as presented in the Microenvironments heart infarction showcase. It means that ReCoN cannot beneficiate from the potential of spatial transcriptomic as much as models representing the tissue structure.

R2.7. In the fibroblast application in Fig 4d, based on the cardiac cell types expression in region type, they are predicting fibroblast gene expression. Wouldn't the most direct benchmarking be comparison with observed fibroblast expression from the ST (after deconvolution perhaps)?

Response:

• *

This was a helpful comment to guide the restructuration of the microenvironment heart infarction showcase, as we believe the whole showcase objective was not formulated clearly enough.

• *

We aim at modelling the impact of the environment on the transcriptome. As the complete transcriptome of a cell results from numerous interacting variables, we believe that comparing the correlation between ReCoN's scores and the transcriptome would not evaluate the prediction of the environment impact.

• *

For this reason, we wanted to compare the results to the specific differences from the microenvironment. We focused on gene set enrichment that seemed less noisy for such a comparative experiment, in particular from Visium10X data that has a particularly high dropout rate.

• *

We propose to strengthen the validation by providing molecular insights into the three groups of cells studied.

The spatial data themselves are bulk, adding a layer of noise over the small number of genes captured by Visium. Instead of a correlation with the deconvoluted spots, we have equivalent single-cell RNA-seq fibroblast data annotated in the same study, which matches the three modelled niches. We propose to conduct a differential expression here and try to compute a correlation between these groups and ReCoN scores, providing a quantitative analysis.

If the correlation was low because of the noise in the data (notably leading to the permutation of individual gene orders even if overall biological signals and gene set orders are conserved), we will additionally do a pathway enrichment over this data, enriching also the qualitative validation.

R2.8. Section 2.6 Besides the cytokine section, it is difficult to assess the added value of this approach. Likely there is a lot of valuable findings here but difficult to say because the assessment is very qualitative.

Response:

• *

One of the challenges around this work was to find relevant dataset to evaluate ReCoN. We tried to complete the direct quantitative evaluation from the Immune Dictionary with another quantitive evaluation from the heart atlas multicellular programs, despite a much less direct validation.

• *

We hope that the production of new perturbation experiments over multicellular datasets, especially cell-type targeted perturbations, will provide more opportunities to validate the different findings and claim from our current manuscript.

• *

On a similar note, no method seemed proposing similar predictions to be compared to. It led to the use of Nichenet score and the current decomposition of the ReCoN model in the section 2.2.1 to evaluate the contribution of the model.

R2.9. The article is dense and writing should be reorganized for better readability.

Minor issues -

No p-values in figures.

*Response: *

• *

We agree that integrating values directly in the panels would make the reading of the figure easier. We would like to introduce the p-values in the panels 2d, 2e, 2f, 2g. We had forgot to indicate in the legend of the panel 4.d that all bold scores were associated with a p-value *

R2.10. Typo - ReCoN-genetic should be - ReCoN-generic.

• *

Response:

• *

We are thankful for noticing the typo and corrected it in the new version.

• *

R2.11. Authors may consider adding figures to describe their results on balance between direct and indirect effects in section 2.2.2.

• *

Response:

• *

Depending on the new findings on the indirect effect iterations, we propose adding an additional panel on their combination or a supplementary figure.

• *

R2.12. Redundancy in the following two lines -

o While these approaches effectively describe what tissue-wide programs are coordinated, they generally offer limited insight into the molecular mechanisms that establish or regulate these programs.

o Despite their ability to identify coordinated tissue-wide programs, multicellular program analyses typically offer limited insight into the underlying molecular mechanisms that orchestrate these programs.

• *

Response:

• *

We propose in the version of the manuscript to remove the first sentence. In our opinion, starting the next paragraph by this clarification seems more helpful to guide the reader than having it at the end of the previous one.

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

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

• *

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

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

R2.13. The direct and indirect effects are treated in two separate steps. In reality of course these effects are operating simultaneously. I wonder if this could be better modelled by iterating through the two steps. It might be worthwhile

trying to see if that improves the performance.

We thank the reviewer for this interesting idea, and propose to add a supplementary text to present the result of this discussion to the readers.

• *

The direct effect is supposed to be measurable from the first iteration only, as we try to represent the effect of direct receptor binding. Regarding the indirect effect, iterations could be done to model the indirect effect, which could represent more distant effect in time.

• *

On an algorithmic note, the indirect effect already allow several "iterations" of this effect, as each random walk can loop between all cell types until restart. However, it does not allow to control the weight of the different successive transition. In practice, with a high restart probability, an extreme weight is given to the first "iteration" over the second, as there is three layers to cross to explore the next cell.

• *

First, we propose clarifying this section of the manuscript, to explain the depth of the indirect effect explorations.

• *

Biologically, it is highly possible that these iterations have an important role to explain the complete reaction of the cells. However, we believe that it hits a major limitation of our modelling, and RWR based exploration in general, as it goes against the enforcement of restarts.

• *

We aim to represent pairwise measurements, representing the impact of one node on another. But random walks without restart are not naturally well fitted to this problem, as they naturally converge to a stationary distribution ((László, Lov, and Erdos 1996)). In the case of ReCoN, it means that each gene and receptor, if we pushed the exploration indefinitely, would have the same probability to end up on each node of the system.

• *

The restart mitigates this impact and enforces the impacts of the seeds by ensuring that the walkers stay close to the seed. (Tong, Faloutsos, and Pan 2006). By iterating successively from the new distribution obtained from the RWR, we would go against this important probability and progressively converge toward the stationary distribution from classical random walks.

• *

So we completely share the opinion of the reviewer that the iterative nature of the indirect effect should be explored too, but we don't believe that ReCoN can model them accurately. We hope that new exploration methods will be able to decipher the importance of these iterations, once additional arguments have been gathered to justify the global interest of considering the indirect effect.

• *

Bibliography:

• *

László L, Lov L, Erdos O. Random Walks on Graphs: A Survey. 1 Jan. 1996:1-46.

• *

Tong H, Faloutsos C, Pan J yu. Fast Random Walk with Restart and Its Applications. Sixth Int Conf Data Min ICDM06 Dec. 2006:613-22. https://doi.org/10.1109/ICDM.2006.70.

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Referee #2

Evidence, reproducibility and clarity

Summary - This is an interesting paper where the authors predict the multicellular response to the molecular perturbations. The idea is somewhat novel and offers a conceptual enhancement by modelling the multicellular response as collective outcome of cell intrinsic gene regulatory changes coupled with cell-cell communication by using a simple network diffusion-based approach. We have a few comments to help strengthen the work.

• It is not clear how well it performs in independent validations. Authors showed that it can predict the effect of cytokine perturbations in the immune dictionary by selecting an optimal alpha. Authors should validate that using the same alpha value of 0.8, it is possible to accurately predict the effect of cytokine perturbations in independent datasets. This is particularly concerning for cytokine-cell type pairs where the optimal alpha is not known. Therefore, the potential utility of Recon to estimate the effect of multicellular perturbations is not well established.
• Authors claimed that optimal alpha value of 0.8 implies the dominance of indirect effect. But in contrast to this claim, the performance across cytokine-celltype pair only increased from 0.72 to 0.76, which seem to imply that indirect effects do not add much.
• How does the cell-type specific effects prediction perform by just considering the intracellular layers? The authors constructed multiple variants of ReCoN to estimate unicellular and multicellular effects. How is the variant ReCoN-grn different from full ReCoN where gamma is set to zero.
• In section 2.2, authors assert that if matching datasets are not available, GRN layer can be extracted from other datasets. How well does the GRN layer from one system generalizes to the other system in terms of perturbation prediction?
• In the abstract, authors claimed that ReCoN can predict the effect of gene knockouts. But authors did not show any application or validation to support this claim.
• The communication between cells might be dependent on their spatial proximity. Is it possible to construct the CCC layer by incorporating the context matched spatial data? How would that affect the performance of multicellular response prediction?
• The direct and indirect effects are treated in two separate steps. In reality of course these effects are operating simultaneously. I wonder if this could be better modelled by iterating through the two steps. It might be worthwhile trying to see if that improves the performance.
• In the fibroblast application in Fig 4d, based on the cardiac cell types expression in region type, they are predicting fibroblast gene expression. Wouldn't the most direct benchmarking be comparison with observed fibroblast expression from the ST (after deconvolution perhaps)?
• Section 2.6 Besides the cytokine section, it is difficult to assess the added value of this approach. Likely there is a lot of valuable findings here but difficult to say because the assessment is very qualitative.
• The article is dense and writing should be reorganized for better readability.

Minor issues

• No p-values in figures.
• Typo - ReCoN-genetic should be - ReCoN-generic.
• Authors may consider adding figures to describe their results on balance between direct and indirect effects in section 2.2.2.
• Redundancy in the following two lines -
  • While these approaches effectively describe what tissue-wide programs are coordinated, they generally offer limited insight into the molecular mechanisms that establish or regulate these programs.
  • Despite their ability to identify coordinated tissue-wide programs, multicellular program analyses typically offer limited insight into the underlying molecular mechanisms that orchestrate these programs.

Significance

This is an interesting paper where the authors predict the multicellular response to the molecular perturbations. The idea is somewhat novel and offers a conceptual enhancement by modelling the multicellular response as collective outcome of cell intrinsic gene regulatory changes coupled with cell-cell communication by using a simple network diffusion-based approach.

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 propose an approach to model complex regulatory processes in tissue or cell collections in specific environments taking into account intra- cellular regulatory processes at multiple levels and inter-cellular communication, importantly offering a chance to estimate the importance of indirect effects of perturbations on one cell type via processes in other cell types. Increasingly more complete models allow testing the impact of each component and of integrating data as context-specific information versus general prior knowledge. 3 main use cases are provided exploiting public datases: prediction of the effect of specific in-vivo cytokine perturbations on mouse lymph node tissues Healthy and disease myocardium in a heart failure multiome dataset Myocardial infarction spatial transcriptomics to identify how different cellular neighbourhoods are related to fibroblast phenotype and fibrosis The main framework is an extension of their previous HuMMus framework to investigate multilayer networks of regulation within a single cell type to also consider inter-cellular interactions, thus including i) tf-target GRN, ii) receptor a receptor layer based on PPI, and cell-cell communication based on LR interactions. These complex networks are then explored within the framework of Random Walk with Restart, which allows to establish 'interaction weights' between different nodes in the network, based on repeated simulations of spreading on the network that thus produce scores of proximity between network nodes, across possible paths. In this study first RWR that only allow intra-cell type walks are performed to calculate direct interaction of perturbation on node states, then RWRs across layers are also enabled, to calculate the importance of inter-cell interactions (via coeff gamma). The importance of each cell type is given by another coeff B that can either correspond to cell type proportions or spatial proximity of cell pairs and finally the scores of within and inter-cell interactions are weighted with a coefficient alpha.

The central contribution that allows coupling of intra with inter-cellular interactions is the establishment of receptor-gene links. Instead of inferring it from data, they propose to express the receptor-gene matrix as: R = L ⋅ G taking ligand-receptor (L) and ligand-gene (G) adjacency matrices from NicheNet and using NNLS to compute R.

Generally, for all these cases, comparison between performance in inferring the effect of perturbation or the upstream regulators or downstream targets are provided with assessment of AUROC/AUPRC values.

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

This is a very well-written paper, the methods used are adequate and the use cases are relevant and broad, exploiting state of the art datasets and tools.

The author's claims are mostly justified. The authors could make an effort to more explicitly cite other efforts in similar directions. The claim 'We envision ReCoN as a extension to prior multicellular modelling, offering an interesting compromise between prediction of cell type responses and understanding of their molecular coordination.' is very general and could be better substantiated. In fact, the authors do not really give examples of alternative approaches to study systems of interacting cells, other than mechanistic agent based models, that clearly are very different. Moreover, the exploration of the multilayer networks with RWR is a very reasonable choice but could there be other approaches? I think the authors could discuss this issue to briefly support their choice of this method.

Generally the discussion should provide the reader the context in the existing literature in which the work can be set, detailing its impact. I think this could be improved.

Regarding the choice of datasets, it is clear that the method is quite demanding, requiring single cell and different omics to build the model, in addition to the expression dataset that is used as a use case. This inevitably leads to using a mix of datasets. For example in the mouse experiments the gene regulatory network was inferred from both a lymph node scRNA-seq dataset and a splenic scATAC-seq dataset, presumably due to the lack of multiome data in this setting. However the cell-cell communication network was inferred from the control case of the Immune Dictionary. Why can't the authors use the control data also for inferring GRNs? Is atac-seq really necessary in the inference of the GRN? What is the impact of the fact that lymph node and spleen samples might be different?

'

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

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

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

• Are the data and the methods presented in such a way that they can be reproduced? The code is very clear, we were able to install and run it and it is quite well-documented. However, a few more details should be given in the text regarding how the evaluation of the performance is carried out. For example: If I understand correctly, when predicting the impact of cytokine perturbations the ReCoN predictions of genes impacted are compared to differentially expressed genes identified through traditional DEG analysis. What is compared is the ranking of these genes from ReCoN with the ranking provided by DEseq2. There is no description of how this comparison of ranking gives rise to AUROC values. Also, is it just the ranking that is predicted or can they also estimate how well they can predict the effect size?

When describing the use cases, I think a bit more detail would help. For example 'To identify the cell-type-specific genes associated with HF, we used the MOFAcell scores of the multicellular factor 1 (MCP1) reported in ReHeat236' I supposed the explanation is on the dataset but for the sake of clarity it would be good to expand this sentence to give at least an idea of the approach.

Regarding the calculation of the R matrix from the NichNet matrices L and G, I gather that the R matrix is calculated once and is thus fully data-independent and available just like the L and G matrices from NichNet. This was not very clear in the tutorials.

Also, this might just be a typo in the tutorial: 'The default α = 0.8 gives more weight to direct effects, which has been empirically validated. You can adjust this based on your biological question." I believe the manuscript says alpha>0.5 refers to indirect effects dominating.

Same for the pre-processing of the spatial data for the third use case, a little more details on how this was done would help the users and readers.

• Are the experiments adequately replicated and statistical analysis adequate? I don't see issues with the statistical power of the analysis. Rather, I think the authors should provide some examination of the parameter space for their model. Whereas ana analysis of the impact of the Alpha parameter is provided, I believe there are several more parameters that have a crucial impact and choices for their values should be discussed.

For example 'In the GRN reconstruction only the links with a score above 1.5e-7 were retained in ReCoN's gene regulatory layer. How was this chosen?

We have identified the following parameters that are somehow justified but could be explored to have a better feel for how they impact the results

Restart probability: How often the walker goes back to the starting seed/molecule Layer transition probability: How often the walker stays in the same layer - different cell? - different layers? Gamma Node transition within a layer: How often one jumps to a different layer Weighting parameters: How much weight for direct or indirect effect to account for the combined effect - alpha - this is the only one that is explicitly explored.

Finally, this might be considered OPTIONAL but would greatly improve the work in our opinion: The method crucially depends on the networks that are used in the different layers and to connect layers and cell types. As we know, biological data is noisy and incomplete (FP and FN) at each level and in each datatype. It would be really useful to estimate what is the robustness of the results to this noise. Particularly, from personal experience, we think the GRNs reconstructed from data are often almost fully connected and it is exceedingly difficult to validate them in specific contexts. This means that some 'errors' are likely to be present. Since several methods exist for inferring GRNs one could simply compare the results using different methods for this part of the network. A related point involves the characteristics of the RWR algorithm, that will be quite impacted by the presence of hubs in these networks (either in single layers or across several) that is likely to impact the exploration. If proteins that are hub are effectively important, that is not a problem, but in some layers, for example, the receptor-receptor layer that presumably will contain PPIs, there might be biases in hubs being just better studied proteins, and these hubs might have an 'unjustified' weight in the walks. One potential approach to assess the robustness of the method to these issues could be an empirical one that just randomly perturbs the networks in ReCoN to see to what extent similar predictions are achieved.

Minor comments:

• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately?
• Are the text and figures clear and accurate?
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Please add page numbers. Figures are nice and clear. Some specific minor points are listed here below.

Define hMLN on first appearance fig1 caption (no page numbers..;) 2nd appearance heterogeneous multilayer structure (HMLN) ... Bi_j not so clear to what it refers when first mentioned personalized interaction specificity. - maybe better word than personalised (contextualised?) ReCoN-genetic and ReCoN, ( generic?) responses. It is expected to observe common behaviors in-between cell-type, that the GRN and the generic CCC network already contribute captures. - not very clear

Figure 2b the icon of cells with double arrows might suggest phenotype shift when instead this is just communication eTACs explain acronym and what they are Due to very few genes being differentially expressed, only cDC1 was conserved and evaluated for IL22, Not so clear In this showcase (not very clear, use case?) different fibroblast specializations - maybe phenotypes?

Figure 4b b) Schematic view of the deconvolution process and cell type-specific count inference from the spatial niches. Not so clear what the heatmap shows, rows and columns Spots heatmap : label niche on rectangles in cols And each col is a spot Rows are cell types or cells? In the cell types x spot

Cell2location. Add reference, maybe explain basic functionality?

reconstructing different patients, tissues, and microenvironments to predict context-specific molecular treatments. Unclear fibrosis in different - at molecular levels

Figure 5d myeloid and endothelial colour code inversed from 5 BC 5d indicate important pathways in organe should not change the colour of the nodes (purple=common, blue or green specific). Use border colour maybe? 5e is not a venn diagram e) Venn diagram showing the overlap between transcription factors (TFs) predicted by ReCoN (green) and those previously implicated in fibrosis (orange) or cardiac diseases (violet). Only the top 10 TFs were annotated from literature sources; full sizes of fibrosis- and cardiac disease-related receptor sets can therefore not be represented. f) also not a venn diagram e/f now in supp the "NABA ECM collagens" gene set. Nodes are grouped by molecular type (e.g., transcription factors, receptors, ligands), and links represent the weighted, direct regulatory interactions present in the ReCoN-constructed

Why Sankey plot? Normally sankey plot represents flow (of regions changing from 1 state to another) but here this is just a weighted network? No communication from firbos back to other cell types? No communication between ventricular/myeloid/lymphoid?

as a extension to - an underrepresented in the current. - current framework? However, it can't represent more - cannot Borrowing representation from hypergraphs, which introduces The network exploration implementation of ReCoN also present some limitations. limitations. While random walks with restarts offer a stable and fast exploration workflow for multilayer networks, it currently only considers positive weights to predict regulation strengths. It involves that the nature of the regulation, as activation or inhibition, has to be identified a posteriori.

• check concordance/grammar

Only the nodes that are included in one of the layers are present in the final results, ignoring the ones present only in bipartites. Unclear a scATAC - an Barsi et al is published https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1013188 effects, allowing for modulating in a second time their contribution. - word order

others. However, it is possible to adjust the Beta coefficient to represent it based on the available information for each dataset. Represent- adjust?

We use the latter to compare the different models. - what is the latter?

It resulted in the scRNA-seq in 1,789 cells with 13,167 genes, and for the scATAC-seq in 3,759 cells with 254,545 regions. Check english GRETA pipeline.- reference

We kept all the cells whose annotations through unsupervised clustering, followed by marker gene annotations, through scANVI were coherent. Word order In parallel, pairs of ligands and receptors with both associated with scores above an absolute gene loading of 0.1 were considered potential driver interactions in HF. Unclear gseapy Python - reference?

and to calculate average for each spatial context the average cell type expression. Unclear

We only used the loadings of all cell types but the fibroblasts to consider the effect of the sole environment. Unclear We realised a downstream - performed

The profiles inferred by ReCoN were first very correlated in all three contexts. - unclear

Significance

Provide contextual information to readers (editors and researchers) about the novelty of the study, its value for the field and the communities that might be interested.

This is a very timely paper, dealing with an important gap in the literature. It is not an entirely new framework, but it integrates different existing approaches to solve a complex issue in a creative way. To my knowledge, it is the first attempt to consider and formalise regulation processes involving both intra- and inter-cellular interactions. The results support the importance of distinguishing the different paths that can relate the impact of a perturbation to specific genes/functions in different cells and their overall ecosystem.

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?

The tool offers a combination of approaches, providing a coherent framework. The code is well documented and functional. The use cases are quite compelling. Sadly, the only type of validation possible involves confirmation of known facts from the literature, which makes it hard to evaluate the full impact of some of the predictions. I think the details of how the method works and especially how the performance was evaluated could be expanded and an assessment of how different parameters and choices impact the results would also be very helpful. An effort to compare the presented variations of the method to some other approach would be very welcome, but I am finding it hard to identify what an alternative approach could be comparable.

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,...).

Potentially the closest results are models that can predict the effect of perturbations on cell line cultures. Several approaches in the literature employ either transformers or optimal transport to predict the effect of perturbations in single cell datasets. One of the main issues is an underlying necessary assumption that the perturbation effect will be larger than the heterogeneity (in cell lines for example), which becomes increasingly difficult when considering in-vivo experiments. ReCoN obviously goes beyond this by considering explicitly the presence of different cell types but distinctions of cell types are sometimes quite arbitrary and potentially application of ReCoN to some of the in-vitro culture datasets, even on cell lines, could be a way to test its performance and benchmark it against other methods. The main bottleneck in the application of this framework to 'personalisation' of therapies, mentioned even in the abstract as a potential future goal for such an approach, will be the lack of data. This approach requires single cell level descriptions of the system at hand, plus additional datasets to build the model structure. To a certain extent, public data of related tissues/contexts can be used, but it will be necessary to test the dependence of performance on coherence of the input data to develop sufficient trust to use it for new predictions, especially in a medical field.

The authors could comment on how their method compares to others that do not require single cell level information. Despite clear differences, it might be important to show the advantage of using this more complex approach that requires data that is less available. Given the ease with which bulk profiles can be constructed from single cell data, it might be possible to compare the approaches directly. For example, see K. Wang, S. Patkar, J.S. Lee, E.M. Gertz, W. Robinson, F. Schischlik, D.R. Crawford, A.A. Schäffer, E. Ruppin Deconvolving Clinically Relevant Cellular Immune Cross-talk from Bulk Gene Expression Using CODEFACS and LIRICS Stratifies Patients with Melanoma to Anti-PD-1 Therapy

Mike van Santvoort, Óscar Lapuente-Santana, Maria Zopoglou, Constantin Zackl, Francesca Finotello, Pim van der Hoorn, Federica Eduati, Mathematically mapping the network of cells in the tumor microenvironment, Cell Reports Methods 2025

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?

Broad interest to biomedical researchers and also biologists in other fields. While the method allows advances in basic research on biological process regulation, a clear clinical application can be envisaged in immuno-oncology for example/ immunology and even general molecular medicine.

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 am a computational biologist with expertise in network models, regulatory networks, agent-based models and especially familiar with the tumour microenvironment and processes therein. I can more or less appreciate the meaningfulness of the biological findings related to the mouse lymphnode example. I am much less of an expert on heart tissue modeling, heart failure, fibrosis etc, required to fully comprehend the impact of the second and third use cases.

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Reviewer #1 (Evidence, reproducibility and clarity (Required)): __ In this manuscript, the authors describe the discovery of a molecular regulator of the immune transcriptional program, which is activated by intestinal distension upon bacterial colonization of the C. elegans intestine. Taking advantage of the fact that inhibition of aex-5 is known to cause intestinal distension and a C-type lectin gene clec-60 as a marker for the immune response to intestinal distension (clec-60p::gfp), the authors performed a forward genetic screen for suppressors of the immune response activation. Of the two mutants isolated, they focused on the stronger suppressor, which corresponded to a cysteine-type DUB, the Ubiquitin Specific Peptidase-14 (usp-14). Through rescue experiments, phenocopy analyses, and quantitative RT-PCR, they validated usp-14 as the causal gene and initiated characterization of its role in immune response activation. To this end, the authors investigated the tissue of action, identifying the intestine as the tissue in which usp-14 mediates the regulation of the immune response. Through transcriptomic analyses, they found that the signalling pathway likely regulated by usp-14 in response to intestinal distension is the Wnt pathway, as they have observed reduction in the transcriptional level of some of the Wnt pathway components in usp-4(tm1481), in response to infection with S. aureus. Additionally, transcriptomic data indicate that usp-14 plays a role in immunity regulation even in the absence of infection. Based on these findings, the authors propose that usp-14 has a dual role in immune regulation: one in surveillance immunity, preventing overactivation of immune responses, and another as a mediator of pathogen-induced responses, such as those triggered by P. aeruginosa or S. aureus. The experiments are rigorous and the results robust; however, some points would benefit from further investigation or clarification. __Response: We thank the reviewer for an excellent summary of our work and for the valuable feedback.

Comment: The expression domain of usp-14 appears to be quite expanded based on single cell RNAseq data (e.g. PMID: 28818938) therefore it is likely that the transgenes used for expression analysis are lacking key regulatory information. Alternative methods like smFISH would be more appropriate to characterise the spatiotemporal pattern of usp-14 expression in more detail. Response: We thank the reviewer for this valuable suggestion. In the original version of the manuscript, we used a 714 bp region upstream of the usp-14 start codon to generate the transcriptional reporter. In the revised manuscript, we reconstructed the reporter using a longer 1924 bp upstream promoter region together with a portion of exon 1. Using this updated reporter, we observed substantially broader expression of usp-14, particularly during the early larval stages. These results are described on page 6, lines 147-152: “We next examined the spatiotemporal expression pattern of usp-14 in C. elegans. To this end, we generated transgenic worms expressing GFP under the control of the usp-14 promoter (usp-14p::gfp). During early larval development, usp-14 was broadly expressed across multiple tissues (Figure 3A). However, in L4 larvae and adult animals, expression became more restricted and was predominantly observed in the intestine and a subset of neuronal cells. Notably, both intestinal and neuronal expression persisted throughout development (Figure 3A).”

Comment: __The mutation mapped in usp-14(jsn19) is a missense mutation (E122K) that suppresses the immune response to a degree comparable to the usp-14(tm1481) deletion allele. However, the authors do not show the functional domains in Fig. 1E potentially affected by this missense mutation. __Response: We have now updated Figure 1E to include the functional domains of USP-14 and mapped both the usp-14(jsn19) missense allele and the usp-14(tm1481) deletion allele onto the protein schematic.

Comment: __How USP-14 regulates Wnt and how Wnt signalling relates to activation of immune responses is not fully supported. Are the Wnt components mentioned in the study induced specifically in the intestine upon infection and does USP-14 act in the intestine in the context of this regulation? How do the authors interpret that both Wnt ligands and receptors are induced ? Does Wnt signalling appear as a GO term in the transcriptomic analysis? The authors can include Wnt signalling components in the analysis of the transcriptomic results. __Response: We thank the reviewer for these insightful comments. Previous studies have shown that the Wnt pathway components examined in our study are induced in the intestine upon infection and function within the intestine to regulate host defense against bacterial pathogens (PMID: 29768179; PMID: 36323254).

We did not observe significant enrichment of Wnt signaling terms in the GO analysis of our transcriptomic dataset. We believe this is likely due to the stringent thresholds used for differential expression analysis (fold change > 2 and p At present, the precise mechanism by which USP-14 regulates Wnt pathway components remains unclear. One possibility is that USP-14 influences Wnt signaling indirectly through additional substrates or interacting proteins that regulate transcriptional outputs. We have now clarified this point in the Discussion (page 12, lines 340–345): “These observations raise the possibility that additional USP-14 substrates or interacting proteins modulate transcriptional outputs downstream of intestinal distension. Future studies aimed at identifying the direct substrates of USP-14 and defining how USP-14 interfaces with neuronal ACC-4 signaling and other distension-responsive pathways will provide important mechanistic insight into how intestinal distension is coupled to innate immune activation.”

Regarding the simultaneous induction of Wnt ligands and receptors, we interpret this as a potential amplification or reinforcement mechanism that enhances Wnt/β-catenin signaling during infection-induced intestinal distension. However, further studies will be required to determine the mechanistic significance of this coordinated transcriptional regulation.

Comment: __Overall, in most of the figures, the micrographs are in general quite dark and exhibit poor contrast between signal and background, particularly in Fig. 1, panels B and J, and Fig. 2, panels B and F (upper rows). Even though these panels are intended to show absence of response, the outlines of the worms are difficult to discern. __Response: We thank the reviewer for the feedback. We have now improved the image presentation throughout the manuscript by either increasing the intensity or adding dotted outlines to more clearly indicate worm positions.

Comment: __In Figure S3, panels A and B, the pmk-1(km25); usp-14(tm1481) animals subjected to aex-5 RNAi show some level of fluorescence/response induction comparable to pmk-1(km25) alone. This observation is not discussed in the text. __Response: We have now discussed this observation in the text. These results are described on page 9, lines 240-244: “Although pmk-1(km25);usp-14(tm1481) worms displayed relatively higher GFP levels than usp-14(tm1481) single mutants upon aex-5 RNAi treatment, this effect likely reflects the elevated basal GFP expression observed in pmk-1(km25) mutants (Figure S4B). Importantly, pmk-1(km25);usp-14(tm1481) animals still exhibited significantly lower GFP levels than pmk-1(km25) single mutants.”

Reviewer #1 (Significance (Required)): __ __Comment: __The work is interesting because it expands some previous work in the field demonstrating immune response induction as a consequence of intestinal distension even in the absence of bacterial infection. This is known to be mediated by the neuronal acetylcholine receptor ACC-4, which signals to the intestine where it regulates immune genes via the Wnt pathway. However, how USP-14 relates to ACC-4 is currently unclear and whether USP-14 function is really required in the intestine to control Wnt signalling is not demonstrated. The authors should include a model to describe how their findings relate to the previous literature and how USP-14 may link mechanistically to Wnt signalling pathway activation. __Response: We thank the reviewer for this insightful comment. We agree that the relationship between USP-14, ACC-4, and Wnt signaling requires further clarification. As suggested by the reviewer, we have now included a model summarizing the current understanding of intestinal distension-induced immune activation and integrating our findings with previous literature (Figure 6H).

Comment: __It remains also unclear whether usp-14 is the only deubiquitinase involved in intestinal distension-induced signalling via the Wnt pathway, or whether other paralog usp genes might also contribute to regulation of immune-responsive transcription. Notably, several mammalian deubiquitinases have established roles in cancer suppression and inflammatory response and innate immunity in other systems so this would increase the potential significance of the work. __Response: We thank the reviewer for this valuable suggestion. To systematically examine whether additional DUBs contribute to intestinal distension-induced immune activation, we performed an RNAi screen targeting all DUBs available in the Ahringer RNAi library using the aex-5(sa23);clec-60p::gfp reporter strain. Among the DUBs tested, knockdown of usp-14 produced the strongest suppression of clec-60p::gfp expression. Although knockdown of usp-5 also partially suppressed GFP induction, usp-5 RNAi did not affect survival during P. aeruginosa infection, suggesting that usp-5 is not required for host defense under these conditions. Together, these findings identify USP-14 as the major DUB required for intestinal distension-induced immune activation in our experimental system. These results are now included in Figure 1G, H, and Figure S2.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): __ Summary C. elegans are soil-dwelling nematodes that feed on bacteria and fungi and thus must be able to distinguish between innocuous and pathogenic species of microbes to survive. Though they lack adaptive immunity, these animals have an ancient version of an innate immune system that has no circulating sentinel or phagocytic cells yet can still mount a response to pathogen exposure. A consequence of the mode of infection of some ingested bacterial pathogens is intestinal distension which by itself, even in the absence of pathogens, is sufficient to trigger the expression of genes encoding immune effectors, including proteins that are bactericidal. The complete mechanistic scheme connecting intestinal distension to the expression of immunity genes has not been resolved, motivating the authors to perform a forward genetic screen for additional components of this pathway. One mutant that the authors isolated was usp-14, encoding an evolutionarily conserved deubiqutinating enzyme. Functional analysis revealed that usp-14 confers protection from microbial pathogens and that the intestine is its primary site of action for its role in host defense. The authors' data indicate that while USP-14 regulates the expression of innate immunity genes that are induced by intestinal distension, surprisingly it functions independently of several canonical innate immune signaling pathways, including the pmk-1/p38 MAPK pathway. Instead, USP-14 appears to act through Wnt signaling to regulate immune effectors by upregulating the expression of several components of that pathway, including the C. elegans ß-catenin ortholog bar-1. This places usp-14 within a gut-brain axis previously shown to control the C. elegans innate immune response through acetylcholine-mediated activation of Wnt signaling. The authors' findings provide new mechanistic insight to this pathway and add to the understanding of ubiqutination as an immune regulatory module. __Response: We thank the reviewer for providing an excellent summary of our work.

Major comments __1. There are three types of experiments in which the authors use the same set of controls across several different figure panels, as stated in the legend to Figure 2. First, when quantifying GFP levels of clec-60::gfp in RNAi-treated animals, the authors use the same clec-60p::gfp and usp-14(jsn19);clec-60p::gfp controls for Fig. 1K, 2C, and 2G. For infection assays with S. aureus NCTC8325, the survival plots for the clec-60p::gfp and usp-14(jsn19);clec-60p::gfp controls shown in Fig. 2E are the same as the ones used in Fig. 1M. Similarly, for infection assays with P. aeruginosa PA14, the survival plots for the clec-60p::gfp and usp-14(jsn19);clec-60p::gfp controls shown in Fig. 2I is the same as was used for Fig 1I. In each case, if the authors in fact collected all of the data for each strain that they studied at the same time but then chose to parse larger datasets into separate figure panels to make it more clear to the reader, then this approach is valid but the authors need to explicitly state that this is what they did. However, if the data pertaining to the control strains were collected at a different time or if it comes from a separate biological replicate, then re-using data from the controls is not appropriate because it would not accurately reflect the specific conditions of the experiment to which the data are being compared. If this is indeed the scenario, then the authors will need to repeat these experiments and include the appropriate control in each iteration. __Response: While preparing the manuscript, these experiments were performed simultaneously. Therefore, all panels that share controls have results from experiments performed simultaneously and represent the same biological replicate. We have added this additional information in the relevant figure legends.

Comment: __2. From the legends describing figure panels that include data pertaining to clec-60p::gfp expression levels as assessed by fluorescence microscopy it seems that, in general, the authors measured GFP fluorescence in about 30 animals to produce quantitative data. How many biological replicates of these types of experiments were carried out? This is not explicitly stated in the section describing fluorescence imaging in the Methods section. Following the description of their methodology regarding statistical analysis of survival curves from microbial infection assays, however, the authors state that, "[a]ll experiments were performed independently at least three times unless otherwise noted." Does this statement apply to microscopy or only to experiments involving infection assays? If the data reporting quantitation of GFP signal is based on only 30 animals, then additional biological replicates are necessary, along with appropriate statistical analyses. __Response: The quantified GFP fluorescence data are derived from three independent biological replicates. In each experiment, we typically imaged and quantified approximately 10 worms per condition, yielding a total of ~30 worms analyzed per genotype or treatment across all replicates (except Figure S1B, where we had two independent replicates). We have added the number of experiments in the figure legends for these data.

Comment: __3. The authors have made all of the RNASeq data publicly available on the Sequence Read Archive, and they include data from several pairwise comparisons for differential gene expression analysis in their supplemental files. One of the most important facts to come out of the authors' Gene Ontology analyses of their RNASeq data is that the genes that are upregulated in a usp-14-dependent manner upon intestinal distension are enriched for those whose products play a role in innate immunity/host defense. The authors should say more about these genes. Are there any commonalities between them with regard to function? Are any of them targets of transcription factors that are known to function in C. elegans innate immunity? If so, this could provide clues as to what the substrates of USP-14 might be. Importantly, the specific identity of the genes assigned in the GO analyses to biological processes pertaining to innate immunity and host defense should be revealed in a supplemental file, and designated as being dependent on or independent of usp-14 for their expression during intestinal distension. __Response: We thank the reviewer for this insightful suggestion. We have now expanded the Results section to describe the functional categories enriched among the USP-14-dependent intestinal distension-induced immune genes, including C-type lectins, ShK toxin domain-containing proteins, and lysozymes (page 7, lines 193-195).

In addition, we compared our transcriptomic dataset with previously published transcription factor-regulated gene sets using WormExp analysis and identified a substantial overlap with genes regulated by the GATA transcription factor ELT-2. These new analyses are described on page 7, lines 196-206: “To identify transcription factors potentially involved in intestinal distension-induced immune activation, we performed transcription factor enrichment analysis using WormExp on genes upregulated in N2 worms following aex-5 RNAi treatment. This analysis revealed a substantial overlap between aex-5 RNAi-induced genes and genes regulated by the GATA transcription factor ELT-2 (Figure S3D). We next examined whether USP-14-dependent immune genes overlapped with ELT-2-dependent immunity genes induced by intestinal distension. To this end, we identified innate immune genes common to both ELT-2-regulated gene sets and aex-5 RNAi-induced genes. Strikingly, these ELT-2-dependent intestinal distension-induced immune genes showed substantial overlap with USP-14-dependent immune genes (Figure S3E and Table S5), suggesting that USP-14 may regulate distension-induced immunity, at least in part, through ELT-2-dependent transcriptional programs.”

Finally, we have created a new table (Table S5) that specifies the identity of the genes assigned in the GO analyses to biological processes pertaining to innate immunity and host defense, for USP-14-dependent and independent genes.

Comment: __4. The authors' data suggest that in response to bacterial infection USP-14 upregulates the expression of bar-1, along with other components of the Wnt signaling pathway, which in turn upregulates innate immunity genes. This could be further substantiated by directly demonstrating that there are USP-14-regulated innate immunity genes whose induced expression in the presence of microbial pathogens also requires bar-1. Along those lines, an initial test would be to assess clec-60p::gfp expression in bar-1 animals versus bar-1;usp-14 double mutants, similar to the experiment whose results are reported in Fig. S4. If generating the bar-1;usp-14 double mutant is not feasible, then RNAi could be used to knockdown bar-1 expression in clec-60p::gfp;usp-14(tm1481) animals. To expand this analysis, the expression of the six innate immunity genes shown to be regulated upon intestinal distension in usp-14-dependent manner could be measured in the presence and absence of intestinal distension or microbial infection in bar-1 and bar-1;usp-14 animals by qRT-PCR. At a minimum, the authors should conduct a bioinformatics analysis to compare the USP-14-regulated innate immunity genes identified in their RNAseq studies to lists of known BAR-1 transcriptional targets to look for potential overlap. __Response: We agree that extending these analyses to qRT-PCR experiments examining additional immune genes would be informative. However, both bar-1 mutants and bar-1 RNAi-treated worms exhibited severe developmental and physiological defects, including sick and dead animals during development, likely reflecting the pleiotropic developmental roles of BAR-1. Although fluorescence imaging and survival assays could be performed by selectively transferring surviving adults, we were concerned that bulk collection of worms for qRT-PCR analyses would introduce confounding effects arising from developmental defects and reduced viability.

To further address the reviewer’s suggestion, we carried out a comparative analysis between USP-14-dependent intestinal distension-induced immune genes and previously identified BAR-1-dependent immune genes. Although transcriptome-wide datasets for BAR-1-dependent pathogen-induced immune genes are not currently available, an earlier study identified seven immune response genes regulated by BAR-1 during infection (PMID: 18981407). We found that six of these genes overlap with the USP-14-dependent intestinal distension-induced immune genes identified in our study. These analyses have now been added to the Results section and included in Table S5.

Comment: __5. While in their Discussion section the authors mention evolutionarily conserved roles for protein ubiquitination as means of immunomodulation, there are few if any comments regarding ubiqutination as a regulatory scheme in C. elegans innate immunity or how their findings enhance our understanding of this phenomenon. Ubiquitination affects C. elegans immunity at multiple levels, from avoidance behavior to gene regulation, and it seems appropriate for the authors to address this in order to more fully contextualize their findings. __Response: We thank the reviewer for the suggestion. We have now added a new paragraph to the Discussion that places our findings in the context of the existing literature on ubiquitination, deubiquitination, and innate immunity in C. elegans. The discussion is added on pages 10-11, lines 295-308: “Although ubiquitin-mediated signaling has emerged as a central regulator of innate immunity across metazoans (Jiang & Chen, 2011; Mello-Vieira & Dikic, 2026), the contribution of DUBs to host defense in C. elegans remains poorly understood. Previous studies in C. elegans have shown that ubiquitin-dependent processes regulate diverse aspects of immunity, including immune surveillance, xenophagy, and pathogen tolerance (Garcia-Sanchez et al, 2021). Perturbations in proteasome function have also been shown to activate surveillance immunity (Ghosh & Singh, 2026; Troemel et al, 2026), highlighting the importance of ubiquitin-associated pathways in sensing pathogen-induced cellular damage. However, most prior studies have focused on ubiquitin ligases, proteasome-associated pathways, or global ubiquitin signaling rather than on specific DUBs directly regulating antibacterial immune responses. To our knowledge, our study provides the first direct evidence that a specific DUB regulates antibacterial innate immunity in C. elegans. Thus, our findings establish USP-14 as a previously unrecognized regulator of host defense and identify deubiquitination as an important regulatory layer in intestinal distension-mediated immunity.”

__Minor comments __1. In the Results section, the authors state that "[k]nockdown of cec-10 led to only a marginal decrease in survival during P. aeruginosa infection" (lines 92 and 93) and that cec-10 "has minimal impact on C. elegans survival during infection" (lines 93 and 94). However, as reported in Supplemental Table 5 the magnitude of the calculated difference in mean survival time between animals treated with RNAi targeting cec-10 and untreated control animals (-20% to -24% and statistically significant in 3/3 replicates) closely approximates the difference in mean survival between usp-14 mutants and controls (-19% to -28% and statistically significant in 3/3 replicates), which the authors clearly find to be significant. If by this metric usp-14 is important for host defense, then so too is cec-10. In light of this, the authors should use different language to describe the impact of cec-10 knockdown on the susceptibility of C. elegans to microbial infection and the potential role of cec-10 in immunity.

Response: We chose not to pursue cec-10 further primarily because it lacks a clear human homolog and because the mutant exhibited reduced expression of the co-injection marker, raising the possibility of broader transgene-related effects. We have modified the text on page 4, lines 92-96: “Knockdown of cec-10 resulted in a significant reduction in survival during P. aeruginosa infection (Figure S1C). However, we did not pursue cec-10 further for two reasons: (i) cec-10(jsn20) mutants exhibited a modest but significant reduction in the myo-2p::mCherry co-injection marker (Figure 1D), raising the possibility of broader transgene-related defects, and (ii) cec-10 lacks a clear human homolog.”

Comment: __2. All of the micrographs in Fig. 1B appear very dark. The GFP expression in the control animals appears dim, making it difficult for the reader to compare the signal in those animals to the GFP expression levels in the mutants. I recommend adjusting the brightness level in an equivalent manner across all of the micrographs to account for this. __Response: We have increased the brightness of all the images, as suggested by the reviewer.

__Comment: __3. Fig. 1E depicts a gene structure diagram for usp-14 with the position of the point mutation in the jsn19 allele isolated in the authors' forward genetic screen indicated by the amino acid substitution symbol drawn over the second exon. Instead of mixing gene- and protein-level information about the jsn19 allele, I recommend replacing the gene structure diagram with a domain structure diagram of the USP-14 protein that depicts the conserved C19 peptidase and ubiquitin-like domains. The relative position of the E122K substitution should still be noted. __Response: __We have now updated Figure 1E to include the functional domains of USP-14 and mapped both the usp-14(jsn19) missense allele and the usp-14(tm1481) deletion allele onto the protein schematic.

Comment: __4. Since all of the information in Fig. 1F appears elsewhere in the text, I recommend eliminating this panel. __Response: We have removed it.

Comment: __5. Regarding the RNAseq analysis, the authors state that 1241 genes are upregulated upon aex-5 knockdown (line 162). The authors then ask which of these genes are regulated by usp-14 in the context of intestinal distension and find that 633 are upregulated a usp-14-dependent manner when aex-5 is targeted by RNAi and that 595 are upregulated even in the absence of usp-14 (Fig. 3D). This accounts for 1228 genes in total, not 1241. Can the authors explain this discrepancy? __Response: We thank the reviewer for carefully noting this discrepancy. The difference arises from the criteria used to classify genes into the categories shown in Figure 5D (previously Figure 3D). Specifically, genes uniquely upregulated in usp-14(tm1481) worms were defined as genes that were either exclusively induced in usp-14(tm1481) worms or expressed at levels more than 2-fold higher in usp-14(tm1481) worms compared to N2 worms. During this classification, 13 genes that were initially identified as upregulated in N2 worms following aex-5 RNAi were found to be expressed at levels more than 2-fold higher in usp-14(tm1481) worms than in N2 worms (Table S4). These genes were therefore reassigned to the “usp-14(tm1481)-specific” category in the Venn diagram. Consequently, the total number of genes represented in the Venn diagram becomes 1228 instead of 1241. To clarify this point, we have now added an explanation to the figure legend.

Comment: __6. For the sake of clarity, in the legend to Fig. 3D I recommend expanding the description of the categories of genes depicted in the Venn diagram by using the same language as in the first worksheet of Supplemental Table 4. __Response: We thank the reviewer for the suggestion. We have now added these details to the legend of Figure 5D (previously Figure 3D). The legend reads: “(D) Venn diagram showing the overlap between genes upregulated upon aex-5 RNAi in N2 and usp-14(tm1481) worms. The GO analyses for the biological processes of unique and common genes are shown. USP-14-dependent genes were defined as genes that were either exclusively upregulated in N2 worms or expressed at levels greater than 2-fold higher in N2 worms than in usp-14(tm1481) worms. USP-14-independent genes were defined as genes upregulated in both N2 and usp-14(tm1481) worms with expression differences of less than 2-fold between the two strains. Genes uniquely upregulated in usp-14(tm1481) worms were defined as genes that were either exclusively induced in usp-14(tm1481) worms or expressed at levels greater than 2-fold higher in usp-14(tm1481) worms than in N2 worms. Thirteen genes classified as upregulated in N2 worms were more than 2-fold higher in usp-14(tm1481) worms than in N2 worms (Table S4) and were therefore included in the usp-14(tm1481)-specific category.”

Comment: __7. In Fig. 4B, the authors' annotation indicates that there is a statistically significant difference (**, p __Comment: __8. In Fig. S5, the shade of blue used to represent the data from the nhr-49(nr2041);usp-14(tm1481);clec60p::gfp animals in panel E is different from that used to represent data from the same animals in panel B. This breaks the pattern of all of the other panels of this figure in which the data pertaining to a given phenotype are depicted in the same color. Also, in the symbol key in panel E there is an extra semi-colon before clec-60p::gfp that should be eliminated in the second genotype notation. __Response: We thank the reviewer for carefully examining the figure and for bringing these issues to our attention. We have made the changes.

Comment: __9. The authors' data show that USP-14 regulates bar-1 expression, and in the Discussion section they mention that in mammals beta-catenin is a substrate of USP14. Can the authors comment on the possibility of/evidence for BAR-1 autoregulation in C. elegans and the prospect of it being facilitated by USP-14? This could be a minor point to add to the Discussion. __Response: In both contexts, USP-14 appears to stabilize BAR-1 by regulating it at either the transcriptional or post-translational level. However, it is currently unknown whether BAR-1 regulates USP-14 expression and thereby participates in an autoregulatory mechanism. Nevertheless, we have added to the Discussion that USP14 may regulate the Wnt pathway through both transcriptional and post-translational mechanisms, depending on the biological context. __Reviewer #2 (Significance (Required)): __ The study described in this manuscript ties in to the findings from two prior genetic screens carried out in C. elegans that aimed to identify immune regulators (Ren et al., Cell Reports, 2022 and Labed et al., Immunity, 2018). Though their strategies differed, both of these previous studies uncovered a role for acetylcholine receptors in modulating the response to ingested microbial pathogens, especially when infection is associated with intestinal distension, indicating that a neuron-to-gut axis controls innate immunity in C. elegans. Labed and colleagues were the first to show that activation of this pathway results in the upregulation of genes encoding Wnt signaling pathway components, including the worm ortholog of beta-catenin called bar-1, which are necessary for the expression of immune effectors in the intestine. The Labed study also revealed that protein ubiquitination could contribute to regulating host defense gene induction because knockdown of lin-23, the substate binding subunit of a ubiquitin ligase complex that mediates BAR-1 degradation, results in constitutive expression of clec-60p::gfp, the same transcription reporter used by Ghosh and Singh as a readout for the expression of innate immunity genes. In their screen that revisits the Ren et al. approach, Ghosh and Singh find that another protein implicated in regulating protein stability via ubiquitination status, USP-14, also controls the expression of innate immunity genes in response to intestinal distension. Interestingly, their data indicate that it does so by upregulating bar-1. This discovery therefore adds an element of mechanistic detail regarding the regulation of Wnt signaling in immunity. While the Labed data suggest that ubiquitination may regulate BAR-1 at the post-translational level, Ghosh and Singhs' results indicate a second layer of regulation of bar-1 at the transcriptional level that also appears to involve ubiquitination. In this case, USP-14 is predicted to modulate the ubiquitination status of a yet-to-be-identified substrate that directly or indirectly governs bar-1 expression. The authors' findings thus bring the field closer to having a complete picture of the Ach-Wnt pathway in C. elegans. As they point out in the Discussion section of their manuscript, ubiquitination is an evolutionarily conserved yet complex means of tuning the immune system. The work described here helps to shed light on this important immune regulatory mode and could have implications for aspects of epithelial immunity that are in common to both invertebrates and vertebrates.

Response: We thank the reviewer for providing such a thoughtful overview of the field and for placing our findings in the context of previous studies on intestinal distension-induced immunity in C. elegans. We also sincerely appreciate the reviewer’s constructive feedback and insightful comments, which have helped us improve the quality and clarity of the manuscript.

My research interest and specific area of expertise pertains to evolutionarily conserved genetic pathways that control healthspan through affecting cellular resilience later in life. Using C. elegans as a surrogate for aging humans, my group studies age-dependent changes in the activity of regulatory modules that protect older animals from the molecular damage associated with intrinsic and extrinsic sources of cellular stress, with a particular emphasis on microbial infection and oxidative stress.

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Referee #2

Evidence, reproducibility and clarity

Summary

C. elegans are soil-dwelling nematodes that feed on bacteria and fungi and thus must be able to distinguish between innocuous and pathogenic species of microbes to survive. Though they lack adaptive immunity, these animals have an ancient version of an innate immune system that has no circulating sentinel or phagocytic cells yet can still mount a response to pathogen exposure. A consequence of the mode of infection of some ingested bacterial pathogens is intestinal distension which by itself, even in the absence of pathogens, is sufficient to trigger the expression of genes encoding immune effectors, including proteins that are bactericidal. The complete mechanistic scheme connecting intestinal distension to the expression of immunity genes has not been resolved, motivating the authors to perform a forward genetic screen for additional components of this pathway. One mutant that the authors isolated was usp-14, encoding an evolutionarily conserved deubiqutinating enzyme. Functional analysis revealed that usp-14 confers protection from microbial pathogens and that the intestine is its primary site of action for its role in host defense. The authors' data indicate that while USP-14 regulates the expression of innate immunity genes that are induced by intestinal distension, surprisingly it functions independently of several canonical innate immune signaling pathways, including the pmk-1/p38 MAPK pathway. Instead, USP-14 appears to act through Wnt signaling to regulate immune effectors by upregulating the expression of several components of that pathway, including the C. elegans ß-catenin ortholog bar-1. This places usp-14 within a gut-brain axis previously shown to control the C. elegans innate immune response through acetylcholine-mediated activation of Wnt signaling. The authors' findings provide new mechanistic insight to this pathway and add to the understanding of ubiqutination as an immune regulatory module.

Major comments

1. There are three types of experiments in which the authors use the same set of controls across several different figure panels, as stated in the legend to Figure 2. First, when quantifying GFP levels of clec-60::gfp in RNAi-treated animals, the authors use the same clec-60p::gfp and usp-14(jsn19);clec-60p::gfp controls for Fig. 1K, 2C, and 2G. For infection assays with S. aureus NCTC8325, the survival plots for the clec-60p::gfp and usp-14(jsn19);clec-60p::gfp controls shown in Fig. 2E are the same as the ones used in Fig. 1M. Similarly, for infection assays with P. aeruginosa PA14, the survival plots for the clec-60p::gfp and usp-14(jsn19);clec-60p::gfp controls shown in Fig. 2I is the same as was used for Fig 1I. In each case, if the authors in fact collected all of the data for each strain that they studied at the same time but then chose to parse larger datasets into separate figure panels to make it more clear to the reader, then this approach is valid but the authors need to explicitly state that this is what they did. However, if the data pertaining to the control strains were collected at a different time or if it comes from a separate biological replicate, then re-using data from the controls is not appropriate because it would not accurately reflect the specific conditions of the experiment to which the data are being compared. If this is indeed the scenario, then the authors will need to repeat these experiments and include the appropriate control in each iteration.
2. From the legends describing figure panels that include data pertaining to clec-60p::gfp expression levels as assessed by fluorescence microscopy it seems that, in general, the authors measured GFP fluorescence in about 30 animals to produce quantitative data. How many biological replicates of these types of experiments were carried out? This is not explicitly stated in the section describing fluorescence imaging in the Methods section. Following the description of their methodology regarding statistical analysis of survival curves from microbial infection assays, however, the authors state that, "[a]ll experiments were performed independently at least three times unless otherwise noted." Does this statement apply to microscopy or only to experiments involving infection assays? If the data reporting quantitation of GFP signal is based on only 30 animals, then additional biological replicates are necessary, along with appropriate statistical analyses.
3. The authors have made all of the RNASeq data publicly available on the Sequence Read Archive, and they include data from several pairwise comparisons for differential gene expression analysis in their supplemental files. One of the most important facts to come out of the authors' Gene Ontology analyses of their RNASeq data is that the genes that are upregulated in a usp-14-dependent manner upon intestinal distension are enriched for those whose products play a role in innate immunity/host defense. The authors should say more about these genes. Are there any commonalities between them with regard to function? Are any of them targets of transcription factors that are known to function in C. elegans innate immunity? If so, this could provide clues as to what the substrates of USP-14 might be. Importantly, the specific identity of the genes assigned in the GO analyses to biological processes pertaining to innate immunity and host defense should be revealed in a supplemental file, and designated as being dependent on or independent of usp-14 for their expression during intestinal distension.
4. The authors' data suggest that in response to bacterial infection USP-14 upregulates the expression of bar-1, along with other components of the Wnt signaling pathway, which in turn upregulates innate immunity genes. This could be further substantiated by directly demonstrating that there are USP-14-regulated innate immunity genes whose induced expression in the presence of microbial pathogens also requires bar-1. Along those lines, an initial test would be to assess clec-60p::gfp expression in bar-1 animals versus bar-1;usp-14 double mutants, similar to the experiment whose results are reported in Fig. S4. If generating the bar-1;usp-14 double mutant is not feasible, then RNAi could be used to knockdown bar-1 expression in clec-60p::gfp;usp-14(tm1481) animals. To expand this analysis, the expression of the six innate immunity genes shown to be regulated upon intestinal distension in usp-14-dependent manner could be measured in the presence and absence of intestinal distension or microbial infection in bar-1 and bar-1;usp-14 animals by qRT-PCR. At a minimum, the authors should conduct a bioinformatics analysis to compare the USP-14-regulated innate immunity genes identified in their RNAseq studies to lists of known BAR-1 transcriptional targets to look for potential overlap.
5. While in their Discussion section the authors mention evolutionarily conserved roles for protein ubiquitination as means of immunomodulation, there are few if any comments regarding ubiqutination as a regulatory scheme in C. elegans innate immunity or how their findings enhance our understanding of this phenomenon. Ubiquitination affects C. elegans immunity at multiple levels, from avoidance behavior to gene regulation, and it seems appropriate for the authors to address this in order to more fully contextualize their findings.

Minor comments

1. In the Results section, the authors state that "[k]nockdown of cec-10 led to only a marginal decrease in survival during P. aeruginosa infection" (lines 92 and 93) and that cec-10 "has minimal impact on C. elegans survival during infection" (lines 93 and 94). However, as reported in Supplemental Table 5 the magnitude of the calculated difference in mean survival time between animals treated with RNAi targeting cec-10 and untreated control animals (-20% to -24% and statistically significant in 3/3 replicates) closely approximates the difference in mean survival between usp-14 mutants and controls (-19% to -28% and statistically significant in 3/3 replicates), which the authors clearly find to be significant. If by this metric usp-14 is important for host defense, then so too is cec-10. In light of this, the authors should use different language to describe the impact of cec-10 knockdown on the susceptibility of C. elegans to microbial infection and the potential role of cec-10 in immunity.
2. All of the micrographs in Fig. 1B appear very dark. The GFP expression in the control animals appears dim, making it difficult for the reader to compare the signal in those animals to the GFP expression levels in the mutants. I recommend adjusting the brightness level in an equivalent manner across all of the micrographs to account for this.
3. Fig. 1E depicts a gene structure diagram for usp-14 with the position of the point mutation in the jsn19 allele isolated in the authors' forward genetic screen indicated by the amino acid substitution symbol drawn over the second exon. Instead of mixing gene- and protein-level information about the jsn19 allele, I recommend replacing the gene structure diagram with a domain structure diagram of the USP-14 protein that depicts the conserved C19 peptidase and ubiquitin-like domains. The relative position of the E122K substitution should still be noted.
4. Since all of the information in Fig. 1F appears elsewhere in the text, I recommend eliminating this panel.
5. Regarding the RNAseq analysis, the authors state that 1241 genes are upregulated upon aex-5 knockdown (line 162). The authors then ask which of these genes are regulated by usp-14 in the context of intestinal distension and find that 633 are upregulated a usp-14-dependent manner when aex-5 is targeted by RNAi and that 595 are upregulated even in the absence of usp-14 (Fig. 3D). This accounts for 1228 genes in total, not 1241. Can the authors explain this discrepancy?
6. For the sake of clarity, in the legend to Fig. 3D I recommend expanding the description of the categories of genes depicted in the Venn diagram by using the same language as in the first worksheet of Supplemental Table 4.
7. In Fig. 4B, the authors' annotation indicates that there is a statistically significant difference (**, p<0.01) in the fluorescence signal from clec-60p::gfp in usp-14(jsn19);aex-5(sa23);clec-60p::gfp_EV versus usp-14(jsn19);aex-5(sa23);clec-60p::gfp_bar-1 animals. This is likely a typographical error that should be changed to "ns" to indicate no significant difference in the fluorescence signal between these two groups, which is consistent with what the data show and with the authors' description of these data in the text (lines 211-214).
8. In Fig. S5, the shade of blue used to represent the data from the nhr-49(nr2041);usp-14(tm1481);clec60p::gfp animals in panel E is different from that used to represent data from the same animals in panel B. This breaks the pattern of all of the other panels of this figure in which the data pertaining to a given phenotype are depicted in the same color. Also, in the symbol key in panel E there is an extra semi-colon before clec-60p::gfp that should be eliminated in the second genotype notation.
9. The authors' data show that USP-14 regulates bar-1 expression, and in the Discussion section they mention that in mammals beta-catenin is a substrate of USP14. Can the authors comment on the possibility of/evidence for BAR-1 autoregulation in C. elegans and the prospect of it being facilitated by USP-14? This could be a minor point to add to the Discussion.

Significance

The study described in this manuscript ties in to the findings from two prior genetic screens carried out in C. elegans that aimed to identify immune regulators (Ren et al., Cell Reports, 2022 and Labed et al., Immunity, 2018). Though their strategies differed, both of these previous studies uncovered a role for acetylcholine receptors in modulating the response to ingested microbial pathogens, especially when infection is associated with intestinal distension, indicating that a neuron-to-gut axis controls innate immunity in C. elegans. Labed and colleagues were the first to show that activation of this pathway results in the upregulation of genes encoding Wnt signaling pathway components, including the worm ortholog of beta-catenin called bar-1, which are necessary for the expression of immune effectors in the intestine. The Labed study also revealed that protein ubiquitination could contribute to regulating host defense gene induction because knockdown of lin-23, the substate binding subunit of a ubiquitin ligase complex that mediates BAR-1 degradation, results in constitutive expression of clec-60p::gfp, the same transcription reporter used by Ghosh and Singh as a readout for the expression of innate immunity genes. In their screen that revisits the Ren et al. approach, Ghosh and Singh find that another protein implicated in regulating protein stability via ubiquitination status, USP-14, also controls the expression of innate immunity genes in response to intestinal distension. Interestingly, their data indicate that it does so by upregulating bar-1. This discovery therefore adds an element of mechanistic detail regarding the regulation of Wnt signaling in immunity. While the Labed data suggest that ubiquitination may regulate BAR-1 at the post-translational level, Ghosh and Singhs' results indicate a second layer of regulation of bar-1 at the transcriptional level that also appears to involve ubiquitination. In this case, USP-14 is predicted to modulate the ubiquitination status of a yet-to-be-identified substrate that directly or indirectly governs bar-1 expression. The authors' findings thus bring the field closer to having a complete picture of the Ach-Wnt pathway in C. elegans. As they point out in the Discussion section of their manuscript, ubiquitination is an evolutionarily conserved yet complex means of tuning the immune system. The work described here helps to shed light on this important immune regulatory mode and could have implications for aspects of epithelial immunity that are in common to both invertebrates and vertebrates.

My research interest and specific area of expertise pertains to evolutionarily conserved genetic pathways that control healthspan through affecting cellular resilience later in life. Using C. elegans as a surrogate for aging humans, my group studies age-dependent changes in the activity of regulatory modules that protect older animals from the molecular damage associated with intrinsic and extrinsic sources of cellular stress, with a particular emphasis on microbial infection and oxidative stress.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors describe the discovery of a molecular regulator of the immune transcriptional program, which is activated by intestinal distension upon bacterial colonization of the C. elegans intestine. Taking advantage of the fact that inhibition of aex-5 is known to cause intestinal distension and a C-type lectin gene clec-60 as a marker for the immune response to intestinal distension (clec-60p::gfp), the authors performed a forward genetic screen for suppressors of the immune response activation. Of the two mutants isolated, they focused on the stronger suppressor, which corresponded to a cysteine-type DUB, the Ubiquitin Specific Peptidase-14 (usp-14). Through rescue experiments, phenocopy analyses, and quantitative RT-PCR, they validated usp-14 as the causal gene and initiated characterization of its role in immune response activation. To this end, the authors investigated the tissue of action, identifying the intestine as the tissue in which usp-14 mediates the regulation of the immune response. Through transcriptomic analyses, they found that the signalling pathway likely regulated by usp-14 in response to intestinal distension is the Wnt pathway, as they have observed reduction in the transcriptional level of some of the Wnt pathway components in usp-4(tm1481), in response to infection with S. aureus. Additionally, transcriptomic data indicate that usp-14 plays a role in immunity regulation even in the absence of infection. Based on these findings, the authors propose that usp-14 has a dual role in immune regulation: one in surveillance immunity, preventing overactivation of immune responses, and another as a mediator of pathogen-induced responses, such as those triggered by P. aeruginosa or S. aureus. The experiments are rigorous and the results robust; however, some points would benefit from further investigation or clarification.

The expression domain of usp-14 appears to be quite expanded based on single cell RNAseq data (e.g. PMID: 28818938) therefore it is likely that the transgenes used for expression analysis are lacking key regulatory information. Alternative methods like smFISH would be more appropriate to characterise the spatiotemporal pattern of usp-14 expression in more detail.

The mutation mapped in usp-14(jsn19) is a missense mutation (E122K) that suppresses the immune response to a degree comparable to the usp-14(tm1481) deletion allele. However, the authors do not show the functional domains in Fig. 1E potentially affected by this missense mutation.

How USP-14 regulates Wnt and how Wnt signalling relates to activation of immune responses is not fully supported. Are the Wnt components mentioned in the study induced specifically in the intestine upon infection and does USP-14 act in the intestine in the context of this regulation? How do the authors interpret that both Wnt ligands and receptors are induced ? Does Wnt signalling appear as a GO term in the transcriptomic analysis? The authors can include Wnt signalling components in the analysis of the transcriptomic results.

Overall, in most of the figures, the micrographs are in general quite dark and exhibit poor contrast between signal and background, particularly in Fig. 1, panels B and J, and Fig. 2, panels B and F (upper rows). Even though these panels are intended to show absence of response, the outlines of the worms are difficult to discern.

In Figure S3, panels A and B, the pmk-1(km25); usp-14(tm1481) animals subjected to aex-5 RNAi show some level of fluorescence/response induction comparable to pmk-1(km25) alone. This observation is not discussed in the text.

Significance

The work is interesting because it expands some previous work in the field demonstrating immune response induction as a consequence of intestinal distension even in the absence of bacterial infection. This is known to be mediated by the neuronal acetylcholine receptor ACC-4, which signals to the intestine where it regulates immune genes via the Wnt pathway. However, how USP-14 relates to ACC-4 is currently unclear and whether USP-14 function is really required in the intestine to control Wnt signalling is not demonstrated. The authors should include a model to describe how their findings relate to the previous literature and how USP-14 may link mechanistically to Wnt signalling pathway activation.

It remains also unclear whether usp-14 is the only deubiquitinase involved in intestinal distension-induced signalling via the Wnt pathway, or whether other paralog usp genes might also contribute to regulation of immune-responsive transcription. Notably, several mammalian deubiquitinases have established roles in cancer suppression and inflammatory response and innate immunity in other systems so this would increase the potential significance of the work.

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Reply to the reviewers

Please see the uploaded "Response to Reviewers" PDF file which contains figures.

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Referee #2

Evidence, reproducibility and clarity

In the manuscript titled "Multiple Molecular Pathways to Longevity: Opposing Gene Expression Programs Define Distinct Aging Strategies", the authors investigated diverse genetic pathways that contribute to lifespan extension in Caenorhabditis elegans and aimed to identify shared and distinct molecular mechanisms among various longevity mutants. Through comprehensive RNA sequencing of different longevity mutants representing seven distinct pathways, the authors showed that these mutants cluster into three primary groups based on their gene expression profiles. This transcriptomic analysis revealed that while some longevity genes are commonly regulated across multiple pathways, others exhibit opposing expression patterns, suggesting that distinct molecular strategies can lead to increased lifespan. Specifically, they identified a set of 196 genes that are consistently upregulated in most longevity mutants, many of which are involved in innate immunity and stress defense. By performing RNAi-based screening, the authors further validated the functional roles of several candidates, including C08F11.7, ugt-62, and K05C4.9, supporting their contributions to longevity and stress resistance. The authors conclude that longevity is mediated through multiple molecular pathways and provide a public online tool to study these complex transcriptomic landscapes.

Major comments

1. While the authors identified a set of 196 upregulated genes, the rationale for narrowing these down to the three final candidates (C08F11.7, ugt-62, and K05C4.9) is not clearly described. The authors show that genetic inhibition of several genes, including DC2.5, C05B5.5, T07C4.5, and W03B1.7, decreases lifespan in both nuo-6 mutants and wild-type animals. However, the authors did not describe why these additional validated candidates, which also showed significant effects on longevity, were not pursued for further characterization. The authors should explicitly state the criteria used to prioritize these three genes over the other validated genes.
2. The authors conclude that longevity can be mediated by multiple molecular pathways. However, it remains unclear whether these distinct strategies can operate simultaneously or are mutually exclusive. The authors need to test whether lifespan extension in a Group 1 mutant is further enhanced or suppressed by the knockdown of a key Group 2-specific genes. These experiments would help determine these pathways act additively, antagonistically, or as partially redundant survival programs.
3. The authors provide interesting data on overexpression of the three candidate genes. However, whereas C08F11.7 clearly demonstrates both necessity and sufficiency for lifespan extension, overexpression of ugt-62 and K05C4.9 does not independently extend lifespan. To strengthen the manuscript, the authors should expand the discussion of these divergent results and clarify possible explanations.
4. Key citations are missing and the authors should add multiple citations including the following ones. Please cite the following paper and discuss the authors' finding with respect to the related work (Lee et al PMID: 40814218). Add citations in the sentence describing changes in the transcriptome of C. elegans associated with age (Lee et al., PMID: 38508494). Furthermore, please cite papers describing the overviews of survival assay using C. elegans (Kwon et al., PMID: 40436148, Hwang et al., PMID: 40436147).

Minor comments

1. To improve readability, please provide the full names for all abbreviations at their first appearance in the manuscript.
2. Please ensure that the labels in the figures match the text exactly. For instance, if different promoters are used for generating overexpression animals, it may be helpful to indicate the specific promoter in the figure panel or legend for clarity.
3. For all lifespan and stress resistance assays, please include the total number of animals (n) and the number of independent biological replicates (N) in the figure legends to confirm statistical reliability.
4. Please clearly specify the exact developmental stage of the animals used for the survival assays in the Materials and Methods section.

Referees cross-commenting

I also agree with reviewer #1's comments and recommend revision to further improve the manuscript.

Significance

This study provides a systematic, side-by-side transcriptomic comparison of nine genetically distinct long-lived C. elegans mutants, revealing that lifespan extension arises from both shared and opposing gene expression programs. By identifying three distinct longevity groups and demonstrating that key pathways can be modulated in opposite directions to achieve long life, the work challenges the notion of a single universal transcriptional signature of aging. Importantly, functional validation shows that select commonly regulated genes can directly modulate lifespan and stress resistance, highlighting actionable molecular targets for promoting healthy aging.

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript by Rudich ZD et al. systematically profiled the transcriptomic changes in nine long-lived C. elegans mutants and presented a careful and informative comparative analysis of these aging-related changes. In addition to these valuable datasets and bioinformatics analyses, the authors performed a large-scale RNAi screen to assess the role of the differentially expressed genes (DEGs) in these mutants and identify several potential targets to promote healthy aging. Moreover, the authors have provided a user-friendly website to examine genes of interest in those longevity mutants from their datasets.

Major comments

The conclusions of this manuscript are generally well supported. The study is also technically sound. Yet, I still have a few concerns that should be carefully addressed.

1. Although I myself believe that the datasets in this study should be more consistent and comprehensive, the authors should perform a data mining analysis of previously reported transcriptomic changes of these mutants or similar mutants in the same longevity pathway and compare the reported changes with their findings to highlight the necessity and advances of this study.
2. This manuscript does not perform any regulon or transcription factor (TF) analyses. TFs are the drivers of the transcriptomic changes and multiple conserved TFs (e.g., daf-16) have already been identified in these pathways. Therefore, it is necessary to examine and compare the regulons/TFs in these new datasets by bioinformatics. Such analyses can: a) provide more information of the driving force of these transcriptomic changes; b) show the role of these known longevity TFs; c) propose new TFs driving longevity; d) support the findings of 'longevity strategies' and 'longevity groups' from the perspective of TFs.
3. osm-5 and daf-2 are categorized into two different groups in this study. Since the longevity of cilia (-) mutants is through daf-16, the same master TF driving daf-2 longevity, please perform further analyses or discussion to clarify this issue.
4. This manuscript focused on genes whose RNAi suppressed the mutants longevity. Please also use bioinformatics to analyze the functions of those whose RNAi extends the mutants longevity, because these genes could tell the health price these mutants pay and help improve ageing interventions by reducing side effects.
5. (OPTIONAL) I strongly suggest a comprehensive comparison of these transcriptomic changes in long-lived mutants with published age-related transcriptomic changes in wild type worms. This comparison will significantly All the suggested analyses are pure bioinformatics and should be realistic to finish in several months.

Minor comments

I also have a few minor comments on data presentation: 1. Please further clarify the analysis of DEGs correlated with lifespan extension in Fig. 2 by a depiction. In Fig. 2C and D, please label data dots from different strains with different colors. 2. In Fig. 3 and S20, please label the percentage of overlapping genes on top of each bars.

Referees cross-commenting

I agree with Reviewer #2's comments and would suggest giving the authors enough time to revise their manuscript.

Significance

Compared to previous transcriptomic analyses of these mutants in differen reports, this study minimized the technical variations and benefitted from the advances in RNA-Seq technology and bioinformatics tools. Therefore, it should provide a more consistent and comprehensive view of the molecular mechanisms underlying the longevity of these mutants. The datasets in this manuscript are valuable to other researchers in the biology of aging.

Meanwhile, since these mutants have been extensively studied, the advance of this study in unknown mechanisms remains limited. Therefore, I would recommend its publication as a 'Resource' article after addressing my concerns.

(I am an expert in the biology of ageing, using C. elegans and mouse as major models.)

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Reply to the reviewers

1. General Statements

We thank the reviewers for their constructive evaluation of our manuscript. We are pleased by the overwhelmingly positive consensus regarding the quality and significance of our data. In particular, the reviewers highlighted that this is a "nice, clean study with interesting data" and noted that our in vivo functional genetic findings in the Drosophila wing are "clearly a strength" that "moves the paper beyond cell-culture correlations" to provide a "simple, straightforward take-home message".

The principal critique across the reports concerns the extent of direct mechanistic evidence linking Groucho (Gro) to regulation of the early elongation checkpoint. Several reviewers suggested additional genomic experiments, including RNA-seq, PRO-seq, or Pol II ChIP approaches, to further examine transcription and pausing behaviour. However, we would like to flag up that genomic datasets addressing these questions across multiple Drosophila cell lines have already been published previously, including work from our own group and others.

The primary objective of the current study is therefore not to replicate these existing genomic analyses, but rather to build directly upon them. We identify a consistent genomic association between Gro and pausing/elongation factors across cell types. Importantly, we extend these findings beyond genomic correlations through in vivo genetic analysis in the developing Drosophila wing.

1. Description of the planned revisions

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• *

Reviewer 1

The figures and text could lay out the logic of the genetic interactions for non-Drosophila readers. For example, the comparison of single and double copies of Gro-RNAi to combinatorial knockdowns, when it is additive, and when it is interpreted as synergistic.

The statistical analyses presented in Figure 5C, including Fisher’s exact tests comparing phenotype distributions between genotypes, were intended to address the distinction between additive and synergistic genetic interactions. However, we agree that the presentation of these comparisons could potentially be made clearer for readers less familiar with Drosophila genetic interaction assays. We would therefore be open to revising the presentation of Figure 5 and the accompanying explanatory text following editorial guidance and with consideration of the intended readership of the eventual journal.

The statistical analysis of the phenotype distributions should be shown more clearly (Fig. 5B).

Figure 5B is intended to present the distribution of observed phenotypic classes and does not include statistical comparisons. A similar analysis has been published for experiments looking at the phenotypes of moderate Groucho overexpression in the wing in the presence of HDAC inhibitors (Winkler et al., 2010 doi.10.1371/journal.pone.0010166). Statistical analyses of the genetic interaction experiments are presented separately in 5C. We therefore believe the current presentation of Figure 5B is appropriate for illustrating phenotype frequencies rather than statistical inference, but we will consider moving this panel to the Supplementary material.

Minor comments

-Figure 5 would gain clarity if the phenotype classes/panel letters were shown more clearly on the images. -The legends of the wing figures should be expanded, especially for readers outside the Drosophila field. -"in vivo" should be italicised consistently.

We agree that clearer labelling of phenotype classes, panel annotations and expanded figure legends could improve the accessibility of Figure 5, particularly for readers less familiar with Drosophila wing phenotypes and genetic interaction assays. We would therefore be open to revising the presentation of this figure and its accompanying legends in a future revised version.

We thank the reviewer for noting the typographical inconsistency of italics for in vivo. This will be corrected during manuscript revision and proofing.

__Reviewer #2 __

Reviewer #2 (Significance (Required)):

I think this is nice little paper providing a simple, straightforward take-home message. It does not conceptually shake the world, and the evidence consists of (nice) correlations, with no direct proof put forward for the conclusions. I am not a Drosophila geneticist but probably rather an 'expert' on basic transcription mechanisms. I think the data in the paper are of high quality, if limited in scope, and that the conclusions are supported by the results, but I do not think the results or conclusions will have a big audience. Having said that, I found it interesting to learn about this group of repressors and their likely mode of action.

On the other hand, it is worth emphasizing that proteins such as NELF and CDK9 would arguably be expected to be found at very many genes, as promoter-proximal pausing does exist at a plethora of genes, also genes that are house-keeping genes, ie not regulated by cell type or stimuli. So, lots of genes with pausing are not regulated by modulation of pausing. So, basically, the fact that knockdown of the repressor Groucho and loss of pausing is additive does not in my opinion necessarily mean that Groucho works by stabilizing pausing. Although it is admittedly a reasonably assumption, Groucho could also work by repressing transcription initiation; the genetic outcomes of 'double relief' would be the same, ie higher transcription levels. I think a brief comment to this effect might be appropriate, especially in the absence of (difficult to obtain) direct evidence that the transcription initiation step is not affected by Groucho.

While we agree that the current study does not directly exclude possible effects of Groucho on transcription initiation, previously published work has already provided evidence arguing against repression by Groucho occurring primarily through inhibition of transcription initiation or prevention of pre-initiation complex assembly. Groucho-bound transcriptional start sites were previously shown to retain RNAP II occupancy, active chromatin features, and detectable basal transcriptional activity despite repression (Kaul et al., 2014).

To acknowledge this possibility and explain why it is unlikely, we will add the sentence “While effects on transcription initiation cannot be completely excluded, previous work argues against Gro repressing transcription primarily through inhibition of transcription initiation. Gro-bound promoters remain accessible, overlap RNAP II occupancy, and retain active chromatin features and basal transcriptional activity” to the start of the third paragraph of the Discussion.

Reviewer #3

The methods section is lacking details on how ChIP-seq was performed in the BG3 cell line. The methods section does a good job of indicating how the data were processed. Information on the antibodies and conditions used is critical, as is whether spike-in controls were used.

The generation of the ChIP-seq data from BG3 cells has already been published. __We will add the line “The production of ChIP-seq datasets for Gro binding in Kc167, S2R+ and BG3 cells has been described elsewhere (Kaul, Schuster and Jennings, 2014; Bar-Cohen et al., 2023)” in the Analysis of ChIP-seq data subsection of the Methods. __

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

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__Reviewer #1 __ Major comments 1. The main weakness is the lack of a mechanistic link between Gro and the early elongation checkpoint. This is really the main point for this reviewer. The manuscript builds an interesting model, and the data support a functional connection between Gro and pausing-related factors, but the mechanistic link is absent. At present, the paper relies on co-localisation of ChIP peaks and genetic interaction in vivo. This is interesting and supportive, but with several possible interpretations. The title and some parts of the text are thus a bit stronger than what is directly demonstrated. Two possibilities could be proposed: either tone down the mechanistic claim or strengthen it experimentally. A more direct assay of pause release or productive elongation after Gro depletion at endogenous targets would be highly valuable. For example, Gro-KD followed by Pol II Ser2-P ChIP, or promoter vs. gene body analysis on Gro-bound genes, ideally comparing genes with Gro at TSS vs. not-TSS, would greatly support the proposed model. If the assay is established, this seems feasible in about 4 months.

We thank the reviewer for this thoughtful comment. We agree that the current study does not directly measure genome-wide RNAP II pause release following Gro depletion. However, several key observations linking Gro with promoter-proximal pausing have already been published and are summarised in the Introduction. Previous work demonstrated that Gro occupancy correlates with paused genes and that depletion of Gro reduces RNAP II pausing and increases elongating RNAP II at the endogenous E(spl)mbeta-HLH locus, an established target gene of Groucho-mediated repression (Kaul et al., 2014; doi.10.1371/journal.pgen.1004595). We also note that several of the experiments proposed by the reviewer have already been addressed in previous work. Specifically, Kaul et al. (2014) demonstrated that Gro depletion increases elongating RNAP II (Ser2-P) at the endogenous E(spl)mbeta-HLH locus while total promoter-associated RNAP II occupancy remains largely unchanged. Promoter versus gene body analyses in that study further supported a role for Gro in regulating progression through the early elongation checkpoint rather than transcription initiation.

The aim of the current manuscript was therefore to build upon these earlier mechanistic and genomic observations by asking whether the relationship between Gro and pausing-associated factors extends across multiple cell types and whether it has functional significance in vivo. By integrating comparative genomic analyses with sensitised developmental genetic assays in the wing, we provide evidence that Gro functionally interacts with multiple regulators of the early elongation checkpoint during development.

The bioinformatic part could be strengthened on "distinct TF repertoires" between cell types.The authors interpret the cell type-specific Gro recruitment as reflecting distinct transcription factor repertoires in BG3, Kc167 and S2R+ cells. This is interesting, but not really shown. To make this point more strongly, the author could provide a map of TF expression across different cell types, especially for the TFs corresponding to the enriched motifs they discuss. Otherwise, this remains speculative.In line, the manuscript discusses enriched motifs in BG3 and compares them to Kc167 and S2R+ cells, but this remains a bit descriptive. A clearer side-by-side comparison would strengthen the paper. This is particularly relevant to the motifs used in interpreting cell type-specific recruitment.

The interpretation that cell type-specific Gro recruitment reflects differences in transcription factor repertoires is based on several previously established observations already described in the manuscript. BG3 cells are derived from the larval CNS, whereas Kc167 and S2R+ cells are embryonic haemocyte-like lines (Cherbas et al., 2011; doi.10.1101/gr.112961.110). Transcriptomic analyses have further shown that these Drosophila cell lines maintain stable and distinct lineage-associated transcriptional identities, including differences in transcription factor expression (Cherbas et al., 2011). Given the diversity of transcription factors known to recruit Gro, the observed cell-type-specific binding patterns and motif enrichments are consistent with the distinct lineage-associated transcriptional programmes previously described for these cell lines.

1. Several overlap analyses could be discussed more in depth. A few statements feel too strong for the actual percentages. For example, the GAF overlap in BG3 is around 51% genome-wide and 56% at TSS, which is meaningful, but not especially high. The text already states that it is not universal, and this point could be discussed more clearly.

We note that the manuscript already explicitly states that overlap between Gro and GAF is not universal. Given the diversity of factors known to recruit Gro and the broad genomic distribution of GAF, we consider overlap frequencies of approximately 50% to represent a substantial association, particularly at transcription start sites. Importantly, the interpretation does not rely on complete co-occupancy between these factors, but rather on the observation that Gro-bound regions show significant enrichment for multiple factors associated with promoter-proximal pausing across different cell types.

Similarly, for the UpSet plot, the wording around the "most frequent" combination could be toned down, because this is not a dominant pattern.

The statement that the overlap between Gro, Nelf-E, GAF, Cdk9 and RNAP II represents the “most frequent” combination refers specifically to the relative frequency of the intersection categories within the UpSet analysis. In this context, the overlap between all five factors represents the largest intersection category identified (306 of 649 Gro peaks), with the next most frequent category containing substantially fewer peaks (90 of 649). We therefore feel that the current wording accurately describes the distribution observed in the analysis.

More generally, I think the manuscript needs a clearer quantitative breakdown of TSS versus non-TSS peaks for the overlap analyses with NELF, GAF, Cdk9 and CycT. Several interpretations depend on this distinction, and right now, this is not always clear enough.

The overlap analyses presented in Figure 3 explicitly distinguish between TSS and non-TSS peaks, and the corresponding quantitative overlap frequencies are described in the Results section. We do not consider that additional breakdowns are required for interpretation of the current data as this distinction is already incorporated into both the analyses and figure presentation.

The "enhancer chromatin" interpretation is interesting, but not fully integrated with the genomic distribution. The observation that Gro is enriched in open enhancer-type chromatin is interesting and supports the idea that Gro does not act mainly through classical repressed chromatin. However, Gro peaks are also enriched at promoters and introns, and this reviewer feels that the manuscript does not fully connect these observations. Where are these enhancer-type peaks located exactly? Are they often intronic? Can this be correlated with the distribution of Gro peaks? This would help the reader and also strengthen the discussion because intronic Gro peaks are present in the data, but are not well integrated into the model.

In the current manuscript, “enhancer chromatin” refers to chromatin states defined by combinations of enhancer-associated histone modifications, including H3K4me1, H3K27ac and H3K56ac as defined by Skalska et al.,2015 (doi.10.15252/embj.201489923), rather than exclusively to distal intergenic regulatory regions. As described in the chromatin-state analysis, these enhancer-associated chromatin signatures do occur at intronic regulatory regions, including regions classified as active intron chromatin. We therefore do not consider the enrichment of Gro peaks at promoters, enhancers and intronic regions to be mutually exclusive observations within this framework.

Intronic enhancer localisation is common in Drosophila, where the compact organisation of the genome results in many developmental regulatory elements residing within introns (Arnold et al., 2013; doi.10.1126/science.1232542). We therefore consider the presence of Gro peaks within intronic regions to be fully consistent with the observed enrichment of Gro binding within enhancer-associated chromatin states.

The in vivo part is a strength, but some important points need clarification.The in vivo section is a clear highlight of the manuscript. It gives functional relevance to the model and moves the paper beyond cell-culture correlations. That said, a few points need to be clearer:-RNAi efficiency is not clear for the tested genes, especially the pausing factors. This is important because the differential effects between NELF subunits could simply reflect differences in knockdown efficiency.

While differences in RNAi efficiency could potentially contribute to variation in phenotype strength between individual knockdowns, multiple biological explanations could also account for the differing effects observed between NELF subunits, including differences in protein stability, residual complex activity, or subunit-specific functions. Importantly, the central conclusion of the manuscript does not depend on quantitative comparison of phenotype strength between individual NELF components, but rather on the observation that perturbation of multiple pausing-associated factors genetically interacts with Gro in vivo.

If RNAi validation is possible with existing reagents, this seems realistic within 3 months.

The manuscript focuses on the genetic interactions observed between Gro and pausing-associated factors in vivo rather than on quantitative comparison between individual RNAi lines. As no specific validation experiments were proposed, we are not currently planning additional RNAi validation analyses for the present study.

The discussion could be expanded, especially because the mechanism is not fully shown.Since the direct mechanism is still missing, the discussion could compensate. Right now, the proposed model is interesting, but it still leaves many open questions. For example:-Is Gro affecting the recruitment or activity of elongation factors?-Could looping or enhancer-promoter communication contribute?-How should the intronic Gro peaks be interpreted in the model?-In the wing, could the phenotype be discussed more mechanistically, in light of what is already known about Gro and derepression of vein-promoting genes?For example, a model figure could help here.

We thank the reviewer for these thoughtful suggestions.

Several of the points raised by the reviewer are discussed in the manuscript already. For example, we discuss the possibility that Gro influences the activity or recruitment of elongation-associated factors. We agree that enhancer-promoter communication and chromatin looping are a plausible component of this mechanism. As the Drosophila genome is compact and intronic enhancers are highly prevalent, topological looping provides a clear physical framework for how Gro molecules distributed at non-TSS sites regulate promoter-proximal machinery. Indeed, we have previously published this model (Kaul, Schuster, and Jennings, 2015; see Figure 1C; doi.10.1080/21541264.2014.1000709). Our current in vivo and genomic findings build directly upon this model, suggesting that within these established looped configurations, Gro acts locally to interface with and stabilize the pausing machinery.

With respect to the wing phenotypes, the Discussion focuses primarily on the interpretation of the observed genetic interactions between Gro and pausing-associated factors rather than on defining the precise downstream target genes contributing to vein phenotypes. We agree that additional mechanistic dissection of these developmental phenotypes would be interesting. However, this would require a substantial expansion of the study into the detailed developmental and signalling mechanisms underlying vein specification, which lies beyond the primary focus of the current manuscript.

OPTIONAL: It would be interesting to know whether the same peak distribution / functional logic is observed in mammalian TLE orthologs. This is not essential for the current conclusions, but it would broaden the impact.

Determining whether similar genomic distributions and functional relationships are conserved for mammalian TLE orthologues will be an important future project. However, relatively little comparable genome-wide TLE occupancy data are currently available, meaning that such analyses would require a substantial independent undertaking beyond the scope of the present study.

Minor comments -Please explain why promoters were defined as {plus minus}250 bp from the TSS. This seems rather narrow.

Promoters were defined as ±250 bp from annotated transcription start sites. This window size is commonly used in Drosophila genomic studies, where the compact organisation of the genome means that broader windows frequently overlap adjacent genes.

-Please clarify why S2R+ cells are included in the comparative part but are not followed in the same way in some downstream analyses.

S2R+ cells were included in the comparative analyses to determine which aspects of Gro recruitment were shared across multiple cell types and which were cell-type specific. Some downstream analyses focused on BG3 and Kc167 cells because these lines had the most extensive corresponding datasets available for the chromatin and pausing-factor analyses performed in the current study.

__Reviewer #3 __ Here Martínez Quiles and Jennings investigate the role of the Groucho repressor in BG3 cells. This extends a previous study that used S2R+ cells, published previously by one of the authors, as well as Kc167 cells. They find that Gro is recruited to gene promoters in a cell-type-specific manner. Gro associates with open chromatin, is mostly associated with enhancer regions, and is primarily excluded from regions of the genome that are repressed by Polycomb. After studying its function in cell culture, the authors investigate the role of Gro in a wing-specific background. The findings here are mostly correlative, showing that loss of Gro results in stronger phenotypic defects when combined with loss of factors including NELF-B or NELF-D, LARP7, and bin3. They propose that Gro acts to attenuate gene expression during early gene expression. This claim would be greatly strengthened if the authors provided RNA-seq data in addition to the ChIP-seq data shown in this manuscript, especially to examine gene expression patterns among the different cell lines studied here. At present, this is a correlative study that does not illuminate the mechanism of Gro in directly regulating promoter-proximal pausing or RNA polymerase behavior.

We thank the reviewer for this suggestion. However, extensive transcriptomic analyses of Drosophila cell lines, including Kc167, S2R+ and BG3-derived lines, have already been published (Cherbas et al., 2011), together with RNA-seq analyses following Gro depletion (Kaul et al., 2014). In addition, the association between Gro occupancy and paused genes has also been reported previously (Kaul et al., 2014; Chambers et al., 2017; doi. 10.1186/s12864-017-3589-6).

While additional RNA-seq analyses could further characterise transcriptional differences between cell lines, RNA-seq alone would not directly determine whether altered transcript levels arise specifically through changes in promoter-proximal pausing, as opposed to effects on transcription initiation, transcript stability, or indirect downstream regulatory effects. We therefore do not consider additional RNA-seq analyses necessary to support the central conclusions of the present study.

Figure 2-3: For the ChIP-seq data, scale the y-axis in the same manner to better understand enrichment between the samples.

These ChIP-seq datasets were generated independently using different antibodies and experimental conditions, direct comparison of enrichment magnitudes across datasets would not be biologically meaningful. Accordingly, our analyses focus on significant peak calls and overlap relationships rather than relative signal intensity. Applying identical y-axis scaling across all tracks would obscure significant enrichment in several datasets and could therefore be misleading.

RNA-seq data between different cell lines would greatly enhance the authors findings or Pro-Seq to really show a relationship with Gro binding and promoter proximal pausing.

We note that RNA-seq datasets for Gro depletion in Kc167 and S2R+ cells have already been published previously (Kaul et al., 2014), together with evidence linking Gro occupancy to paused genes (Kaul et al., 2014; Chambers et al., 2017). We therefore do not consider that additional RNA-seq analysis would substantially strengthen the central conclusions of the current manuscript.

Moreover, RNA-seq alone cannot distinguish if altered transcript abundance reflects changes in promoter-proximal pausing from other mechanisms influencing transcript abundance. While PRO-seq approaches could provide further mechanistic information regarding RNAPII dynamics, such experiments are beyond the scope of the present study.

This study helps to further clarify how Gro binds DNA in different cell types and indicates that may intersect with factors involved in promoter proximal pausing. The study is highly correlative and would require additional work to show a mechanistic link between Gro and transcription attenuation due to promoter proximal pausing.

While we agree that PRO-seq approaches could provide additional mechanistic information regarding RNAPII dynamics, establishing an appropriate experimental and analytical framework for these analyses would require a substantial extension beyond the scope of the present study. In addition, several aspects of the relationship between Gro occupancy, transcriptional repression, and promoter-proximal pausing that underpin these suggestions have already been addressed in previously published work, including RNA-seq analyses following Gro depletion (Kaul et al., 2014), evidence linking Gro occupancy with paused genes (Kaul et al., 2014; Chambers et al., 2017), and studies demonstrating that Gro-mediated repression does not occur through inhibition of pre-initiation complex assembly. The current manuscript is therefore intended to build upon these existing findings by integrating comparative genomic analyses with new in vivo genetic interaction data.

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Referee #3

Evidence, reproducibility and clarity

Here Martínez Quiles and Jennings investigate the role of the Groucho repressor in BG3 cells. This extends a previous study that used S2R+ cells, published previously by one of the authors, as well as Kc167 cells. They find that Gro is recruited to gene promoters in a cell-type-specific manner. Gro associates with open chromatin, is mostly associated with enhancer regions, and is primarily excluded from regions of the genome that are repressed by Polycomb. After studying its function in cell culture, the authors investigate the role of Gro in a wing-specific background. The findings here are mostly correlative, showing that loss of Gro results in stronger phenotypic defects when combined with loss of factors including NELF-B or NELF-D, LARP7, and bin3. They propose that Gro acts to attenuate gene expression during early gene expression. This claim would be greatly strengthened if the authors provided RNA-seq data in addition to the ChIP-seq data shown in this manuscript, especially to examine gene expression patterns among the different cell lines studied here. At present, this is a correlative study that does not illuminate the mechanism of Gro in directly regulating promoter-proximal pausing or RNA polymerase behavior.

Major comments:

Figure 2-3: For the ChIP-seq data, scale the y-axis in the same manner to better understand enrichment between the samples.

The methods section is lacking details on how ChIP-seq was performed in the BG3 cell line. The methods section does a good job of indicating how the data were processed. Information on the antibodies and conditions used is critical, as is whether spike-in controls were used.

RNA-seq data between different cell lines would greatly enhance the authors findings or Pro-Seq to really show a relationship with Gro binding and promoter proximal pausing.

Significance

This study helps to further clarify how Gro binds DNA in different cell types and indicates that may intersect with factors involved in promoter proximal pausing. The study is highly correlative and would require additional work to show a mechanistic link between Gro and transcription attenuation due to promoter proximal pausing.

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Referee #2

Evidence, reproducibility and clarity

This paper describes experiments designed to determine the mechanism of repression by the Groucho co-repressor in flies. The authors first characterize DNA binding by Groucho by ChIP-Seq analysis. This turns out to be consistent with recruitment driven by cell-type specific transcription factors. Nevertheless, its distribution across genomic features is similar across cell types, with enrichment in promoters and introns. It appears to bind in regions otherwise transcriptionally active (ie 'open chromatin'), rather than chromatin that is compacted and repressed. This suggest that Groucho regulates transcription through promoters or promoter-proximal pausing rather than by reducing chromatin accessibility. Groucho binding overlaps with NELF and GAF binding, seemingly consistent with a role in regulating pausing. However, Gro binding was also observed at promoters where P-TEFb components are detected, arguing against Gro repressing transcription P-TEFb exclusion from pausing sites. The authors next switched to investigating the consequences of Groucho kd and tested the idea that co-depletion of pausing factors might inform about the manner of gene repression, the idea being that if Groucho attenuates transcription by promoting or stabilizing promoter proximal pausing, then partial reduction of the pausing factors it affects should enhance the Groucho knock-down phenotype. Interestingly, simultaneous knock-down of Groucho and GAF resulted in enhanced patterning defects relative to Groucho knock-down alone, with the severity of the phenotypes resembling that observed upon increasing Groucho knock-down. Similarly, the knock-down of either Nelf-B or Nelf-D significantly enhanced Groucho phenotype. Finally, Kd of regulators of the pausing regulator CDK9 were tested. The 7SK snRNA complex inhibits CDK9, so any treatment leading to less 7SK will free CDK9 to positively affect pausing release. Larp kd fits that category as it directly leads to less 7SK and thus more CDK9 activity, while Bin3 kd results in less 5'-methyl capping, and thus more 7SK destabilization (less 7SK), again freeing CDK9 from inhibition - so, increasing pause release (like Nelf kd). Gratifyingly, this separate way of de-regulating/decreasing pausing again had an additive effect to Groucho depletion. Together, these genetic data thus overall support the idea that the (non-chromatin regulating) repressor Groucho works by stabilizing pausing complexes at specific genes.

Significance

I think this is nice little paper providing a simple, straightforward take-home message. It does not conceptually shake the world, and the evidence consists of (nice) correlations, with no direct proof put forward for the conclusions. I am not a Drosophila geneticist but probably rather an 'expert' on basic transcription mechanisms. I think the data in the paper are of high quality, if limited in scope, and that the conclusions are supported by the results, but I do not think the results or conclusions will have a big audience. Having said that, I found it interesting to learn about this group of repressors and their likely mode of action.

On the other hand, it is worth emphasizing that proteins such as NELF and CDK9 would arguably be expected to be found at very many genes, as promoter-proximal pausing does exist at a plethora of genes, also genes that are house-keeping genes, ie not regulated by cell type or stimuli. So, lots of genes with pausing are not regulated by modulation of pausing. So, basically, the fact that knockdown of the repressor Groucho and loss of pausing is additive does not in my opinion necessarily mean that Groucho works by stabilizing pausing. Although it is admittedly a reasonably assumption, Grouch could also work by repressing transcription initiation; the genetic outcomes of 'double relief' would be the same, ie higher transcription levels. I think a brief comment to this effect might be appropriate, especially in the absence of (difficult to obtain) direct evidence that the transcription initiation step is not affected by Groucho.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript entitled "the co-repressor Groucho limits progression through the early transcription elongation checkpoint in vivo", the authors study how the co-repressor Groucho (Gro) may repress transcription in Drosophila. They combine Gro ChIP-seq analysis in BG3 cells with published data from Kc167 and S2R+ cells, chromatin-state and overlap analyses with pausing/elongation factors, and functionally link these interactions in vivo by genetic interaction assays in the wing. The manuscript shows that Gro recruitment is largely cell type-specific, while Gro binding is detected as discrete peaks with similar genomic distribution across cell types. Gro peaks are enriched in open enhancer-type chromatin and overlap with factors linked to promoter-proximal pausing. In vivo, knock-down (KD) of several pausing-related factors enhances the gro RNAi phenotype in the wing. Overall, this is a nice, clean study with interesting data, and the in vivo findings are clearly a strength. However, the mechanistic link between Gro and the early elongation checkpoint remains unclear, and several bioinformatics and presentation points could be strengthened.

Major comments

1. The main weakness is the lack of a mechanistic link between Gro and the early elongation checkpoint. This is really the main point for this reviewer. The manuscript builds an interesting model, and the data support a functional connection between Gro and pausing-related factors, but the mechanistic link is absent. At present, the paper relies on co-localisation of ChIP peaks and genetic interaction in vivo. This is interesting and supportive, but with several possible interpretations. The title and some parts of the text are thus a bit stronger than what is directly demonstrated. Two possibilities could be proposed: either tone down the mechanistic claim or strengthen it experimentally. A more direct assay of pause release or productive elongation after Gro depletion at endogenous targets would be highly valuable. For example, Gro-KD followed by Pol II Ser2-P ChIP, or promoter vs. gene body analysis on Gro-bound genes, ideally comparing genes with Gro at TSS vs. not-TSS, would greatly support the proposed model. If the assay is established, this seems feasible in about 4 months.
2. The bioinformatic part could be strengthened on "distinct TF repertoires" between cell types. The authors interpret the cell type-specific Gro recruitment as reflecting distinct transcription factor repertoires in BG3, Kc167 and S2R+ cells. This is interesting, but not really shown. To make this point more strongly, the author could provide a map of TF expression across different cell types, especially for the TFs corresponding to the enriched motifs they discuss. Otherwise, this remains speculative. In line, the manuscript discusses enriched motifs in BG3 and compares them to Kc167 and S2R+ cells, but this remains a bit descriptive. A clearer side-by-side comparison would strengthen the paper. This is particularly relevant to the motifs used in interpreting cell type-specific recruitment.
3. Several overlap analyses could be discussed more in depth. A few statements feel too strong for the actual percentages. For example, the GAF overlap in BG3 is around 51% genome-wide and 56% at TSS, which is meaningful, but not especially high. The text already states that it is not universal, and this point could be discussed more clearly. Similarly, for the UpSet plot, the wording around the "most frequent" combination could be toned down, because this is not a dominant pattern. More generally, I think the manuscript needs a clearer quantitative breakdown of TSS versus non-TSS peaks for the overlap analyses with NELF, GAF, Cdk9 and CycT. Several interpretations depend on this distinction, and right now, this is not always clear enough.
4. The "enhancer chromatin" interpretation is interesting, but not fully integrated with the genomic distribution. The observation that Gro is enriched in open enhancer-type chromatin is interesting and supports the idea that Gro does not act mainly through classical repressed chromatin. However, Gro peaks are also enriched at promoters and introns, and this reviewer feels that the manuscript does not fully connect these observations. Where are these enhancer-type peaks located exactly? Are they often intronic? Can this be correlated with the distribution of Gro peaks? This would help the reader and also strengthen the discussion because intronic Gro peaks are present in the data, but are not well integrated into the model.
5. The in vivo part is a strength, but some important points need clarification. The in vivo section is a clear highlight of the manuscript. It gives functional relevance to the model and moves the paper beyond cell-culture correlations. That said, a few points need to be clearer:
   • RNAi efficiency is not clear for the tested genes, especially the pausing factors. This is important because the differential effects between NELF subunits could simply reflect differences in knockdown efficiency.
   • The figures and text could lay out the logic of the genetic interactions for non-Drosophila readers. For example, the comparison of single and double copies of Gro-RNAi to combinatorial knockdowns, when it is additive, and when it is interpreted as synergistic.
   • The statistical analysis of the phenotype distributions should be shown more clearly (Fig. 5B). If RNAi validation is possible with existing reagents, this seems realistic within 3 months.
6. The discussion could be expanded, especially because the mechanism is not fully shown. Since the direct mechanism is still missing, the discussion could compensate. Right now, the proposed model is interesting, but it still leaves many open questions. For example:
   • Is Gro affecting the recruitment or activity of elongation factors?
   • Could looping or enhancer-promoter communication contribute?
   • How should the intronic Gro peaks be interpreted in the model?
   • In the wing, could the phenotype be discussed more mechanistically, in light of what is already known about Gro and derepression of vein-promoting genes? For example, a model figure could help here.

OPTIONAL:

It would be interesting to know whether the same peak distribution / functional logic is observed in mammalian TLE orthologs. This is not essential for the current conclusions, but it would broaden the impact.

Minor comments

• Please explain why promoters were defined as {plus minus}250 bp from the TSS. This seems rather narrow.
• Please clarify why S2R+ cells are included in the comparative part but are not followed in the same way in some downstream analyses.
• Figure 5 would gain clarity if the phenotype classes/panel letters were shown more clearly on the images.
• The legends of the wing figures should be expanded, especially for readers outside the Drosophila field.
• "in vivo" should be italicised consistently.

Referee cross-commenting

My main concerns are broadly echoed by Reviewer 2, notably regarding the need to clarify the level of mechanistic support for the proposed model. Reviewer 3 also raises related points about the correlative nature of the evidence. Overall, I think the reports converge on the need to better align the conclusions with the current data, while recognising the value of the functional in vivo results, though with different levels of requested additional analysis.

Significance

General assessment

This is a nice paper, with clean data and an interesting model. The strongest point is the attempt to connect the Gro genomic localisation with functional interaction in a developmental context. The observation that Gro is found in open enhancer-type chromatin, together with the in vivo genetic interactions, makes the study significant. The main limitation is that the mechanistic link is still missing. Overall, this reviewer finds the study convincing as a functional and descriptive paper but less convincing as a mechanistic one.

Advance

The study extends previous work on Gro by comparing several cell types and by adding in vivo genetic data in the wing. The main advance is thus conceptual and functional: it supports the idea that Gro acts in concert with the pausing/elongation machinery rather than simply through repressed chromatin. However, the mechanistic advance remains limited because a direct link to the early elongation checkpoint has not yet been demonstrated. This is the main thing preventing the paper from being stronger.

Audience

This reviewer feels that the manuscript will mainly interest a specialised basic research audience: scientists working on transcriptional regulation, co-repressors, RNA polymerase II pausing, chromatin regulation, and Drosophila developmental genetics. It can also be relevant to those broadly interested in Gro/TLE biology.

Expertise

This reviewer's expertise includes gene regulation and its nuclear organisation, transcriptional/co-transcriptional and post-transcriptional regulations, transcription factors biology, and Drosophila genetics. This reviewer is comfortable evaluating the developmental genetics, the conceptual aspect, and the interpretation of genomic analyses, but has less competence in evaluating bioinformatic ChIP-seq processing pipelines.

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Reply to the reviewers

Manuscript number: RC-2025-03227R

Corresponding author(s): Dr. David Skerrett-Byrne & Prof. Brett Nixon

1. General Statements

We are grateful to the reviewers and editorial team for their thoughtful and constructive evaluation of our manuscript. The comments provided were insightful and have substantially strengthened the rigor, clarity, and presentation of the study. In response, we have carefully revised the manuscript throughout, including clarification of conceptual interpretations, expansion of methodological detail, refinement and condensation of the Discussion, as well as addition of new supplementary analyses and figures. Collectively, we believe these revisions have improved both the transparency and accessibility of the work while reinforcing the central conclusions of the study.

At its core, this study sought to address a major unresolved question in reproductive biology: how spermatozoa, which are transcriptionally and translationally inert, achieve functional competence during post-testicular maturation. Using deep, stage-resolved phosphoproteomics integrated with functional validation approaches, we demonstrate that the majority of sperm phosphoproteomic remodelling occurs during epididymal maturation rather than during capacitation, challenging long-standing paradigms in the field. Beyond generating one of the deepest sperm phosphoproteomic resources currently available (>14,000 phosphosites), the study also provides functional and physiological context through kinase inhibition studies, in vivo knockout phenotypes, and the development of the ShinySpermPhospho online resource to facilitate community access and future discovery.

Importantly, through the review process we have worked carefully to ensure that the manuscript more clearly distinguishes data-driven conclusions from hypothesis-generating interpretations, particularly in areas relating to kinase prediction, metabolic regulation, and phosphoproteomic remodelling. We believe the revised manuscript now presents a more balanced and rigorous framework while preserving the significance of the central findings.

Overall, we hope the revised manuscript now provides a valuable resource and conceptual advance for the reproductive biology community, with implications extending from fundamental sperm cell biology to translational opportunities in male infertility and contraceptive development.

2. Point-by-point description of the revisions

REVIEWER #1

The manuscript by Skerrett-Byrne and collaborators represents a comprehensive and technically sophisticated phosphoproteomics study. Using high-resolution mass spectrometry on mouse sperm obtained from the caput and cauda regions of the epididymis, both before and after capacitation, the authors generated a more complete database of phosphorylation changes in these cells. One of the most interesting outcomes is that most of these changes occur during sperm maturation, rather than sperm capacitation. The work is important and relevant, and the information obtained could be valuable for reproductive biologists working in basic science, as well as for the identification of novel contraceptive targets.

__Answer: __We thank the reviewer for their positive assessment of our work and for recognising the value of the datasets we have generated for supporting future innovations in both fundamental reproductive biology and the identification of novel contraceptive targets. We are also delighted that the reviewer has recognised the significance that, contrary to previously thought, the majority of the phosphorylation changes we report occur during epididymal maturation, rather than subsequently during capacitation.

• The title should include a reference to sperm capacitation, as most of the study focuses on comparisons between epididymal maturation and capacitation, and the functional experiments are based on the latter. __Answer: __We thank the reviewer for this suggestion and have revised the title to reflect the importance of our focus on both phases of post-testicular sperm maturation, namely epididymal sperm maturation and sperm capacitation (please see line 1).

• Considering the newly reported changes in phosphosites, it would be desirable to include validation at the individual protein level for at least a few examples, using an independent technique such as western blotting. __Answer: __We thank the reviewer for this thoughtful suggestion and fully appreciate the motivation to seek orthogonal validation of phosphoproteomic findings. However, we respectfully wish to express our reservations regarding the use of antibody-based validation of site-specific phosphorylation events, a technique that is increasingly being recognised as problematic and, in many cases, less reliable than modern MS-based approaches (Nature, PMID: 39506148). Indeed, high-resolution mass spectrometry provides direct, site-resolved identification and quantification of phosphorylation events with substantially greater specificity, accuracy, and proteoform resolution than antibody-based methods. For this reason, MS-based phosphoproteomics is now widely regarded as the gold standard for mapping phosphorylation dynamics.

With regard to the use of antibodies, many commercially available phospho-specific antibodies lack sufficient site specificity, often have poorly defined or undocumented epitope recognition, and frequently fail to discriminate between closely related proteoforms or neighbouring phosphorylation sites. Indeed, recent large-scale evaluations have demonstrated that many widely used antibodies do not reliably bind their intended targets, raising concerns about reproducibility and interpretability across the biomedical sciences (PMID: 37995198). In one study, testing the utility of >600 antibodies, two thirds failed to work as described (PMID: 37995198), while the literature also features other studies (e.g. PMID: 31612854) reporting that certain antibodies (SC-138763) do not bind their stated target despite having been "used in 15 published manuscripts to ascribe specific properties to the protein in normal and disease states", collectively cited >3,000 times.

Accordingly, while we recognise the importance of independent validation, we contend that antibody-based validation may not be the most appropriate strategy to improve the robustness of the conclusions in this study. It is for this reason that we elected to strengthen confidence in our findings through multiple complementary approaches, including rigorous statistical filtering, extensive in-silico pathway and kinase analyses, selective pharmacological inhibition of target proteins, and in vivo functional interrogation using knockout mouse models. Together, these orthogonal strategies provide additional biological validation linking the reported phosphorylation changes to aspects of sperm function.

We have clarified this rationale in the revised manuscript and briefly expanded the discussion to touch on these methodological strengths and limitations (please see lines 754 - 759).

• In the knockout models, it is not possible to distinguish between defects in spermatogenesis and those arising during maturation or capacitation. A parameter directly related to spermatogenesis should therefore be included, for example, testicular weight or histology, sperm number, and sperm morphology. __Answer: __We thank the reviewer for raising this important point. We agree that systemic knockout models do not allow definitive discrimination between defects arising during spermatogenesis versus those occurring downstream during post-testicular sperm maturation or capacitation. Unfortunately, the additional parameters suggested by the reviewer do not form part of the standardised phenotyping pipeline implemented by the International Mouse Phenotyping Consortium (IMPC) and the European Mouse Mutant Archive (EMMA). As such, these data are not available for the knockout lines examined in this study and cannot be retrospectively generated. We have therefore clarified this limitation more explicitly in the revised manuscript and have framed the knockout data as physiological validation concerning the functional relevance of the parent protein rather than as definitive evidence of stage-specific or phosphorylation-dependent mechanisms of action. Importantly, the consistency of impaired sperm motility and fertilisation outcomes across multiple independent knockout lines supports the biological importance of the parent proteins identified, while acknowledging that the precise developmental window of their action remains to be resolved. While we regrettably concede that it is beyond the scope of this study, we do acknowledge that future studies will be required to dissect these mechanisms with greater resolution, ideally using germ cell-specific or temporally controlled knockout models, or targeted manipulation of key phosphoproteins and/or their phosphorylation motifs. Such approaches will be essential if we are to be able to distinguish roles of target proteins in spermatogenesis from those that occur downstream during epididymal maturation and capacitation (please see lines 725 - 733).

• Error values, sample size, and statistical analyses are missing from Figure 7 and should be provided for clarity. __Answer: __We apologise for this omission and have now updated Figure 7 and its legend to include sample sizes, error values, and details of the statistical analyses used, thereby improving clarity and reproducibility of these data.

In addition, we have clarified that sperm functional data derived from EMMA knockout lines are generated from cryopreserved samples comprising pooled cauda epididymal spermatozoa collected from 10 heterozygous males per line (PMID: 17709347, 38839949). As such, each data point represents a pooled biological sample, consistent with standardised EMMA/INFRAFRONTIER protocols (PMID: 25414328, 27262858, 38839949). Where appropriate, we have also included additional reproductive metrics at the level of IVF cycle (where available) and individual litters, including average litter size and fetal sex distribution (with exceptions for specific lines where such data are not available). These details are now captured in both the Methods and relevant figure legends (please see lines 453 - 457, 1228 - 1234, 1431 - 1434, 1533 - 1536, 1572 - 1575, Figure 7 & S6).

REVIEWER #2

In this manuscript, the authors examine dynamic modifications of the sperm phosphoproteome during epididymal transit and capacitation. They compare three distinct populations differing in anatomical localization and activation status: caput sperm, non capacitated cauda sperm, and capacitated cauda sperm. Using high resolution tandem mass spectrometry, they reveal that phosphorylation changes during epididymal passage are far more extensive than previously appreciated. These findings are further validated in genetically modified animal models, where disruption of selected genes encoding for phosphoproteins results in marked defects in sperm motility and fertilization capacity.

__Answer: __We thank the reviewer for their positive and thoughtful evaluation of our study and for recognising both the depth of the phosphoproteomic dataset and the importance of the functional validation experiments; sentiments that we whole heartly agree with.

• Throughout the text, and particularly in the paragraph entitled 'Epididymal maturation accounts for the majority of maturation associated sperm cell signaling,' it seems that phosphorylation is interpreted as inherently activatory and dephosphorylation as inhibitory (lines 248-252). Since this relationship is not universally applicable, it would be valuable to address this issue at the outset of the paragraph and to discuss how phosphorylation events are context dependent in their effects on protein function. __Answer: __We thank the reviewer for highlighting this important conceptual point. We fully agree that phosphorylation is not inherently activatory, nor is dephosphorylation necessarily inhibitory, and that the functional consequences of phosphorylation are highly context dependent. We have revised the indicated paragraph to explicitly acknowledge this at the outset to ensure that phosphorylation changes are interpreted as regulatory rather than intrinsically directional (please see lines 219 - 222).

• Lines 392-393: the claim that "the introduction of each inhibitor to populations of capacitating spermatozoa led to a significant reduction..." is not fully supported by data and should be toned down. In fact, two out of three inhibitors, do not significantly affect the acrosome reaction. __Answer: __We thank the reviewer for this careful assessment and agree that the original wording overstated the nuances of the effects of individual inhibitors. We have revised the text to explicitly report the corresponding p-values and to distinguish between statistically significant and non-significant trends. Specifically, inhibition of PAK1 produced a statistically significant reduction in the acrosome reaction, whereas inhibition of STK33 (p = 0.0574) and HIPK4 (p = 0.0911) resulted in consistent, but non-significant, reductions. Importantly, combined inhibition of all three kinases yielded a robust and statistically significant suppression of acrosomal exocytosis. The revised wording now accurately reflects the quantitative data (please see lines 419 - 424, 700 - 703).

• The discussion section, spanning 11 pages, is overly long and contains considerable repetition. I recommend transferring the detailed description of experiments to the 'Results' section and using the discussion primarily to synthesize and highlight the novel findings while limiting speculative content. For example, the content in lines 509-530 could be condensed and relocated to the Results. Likewise, other detailed examples would be more appropriately presented within their respective result paragraphs. __Answer: __We thank the reviewer for this constructive feedback. We agree that the Discussion was overly long and on reflection does contain some unnecessary repetition. In response, we have substantially condensed the Discussion (shorten by 641 words), relocated and shorten detailed descriptions of experimental observations to the Results section where appropriate (including the suggestion made), and focused the revised Discussion on synthesis of the key findings and their broader implications. We should note, to address certain review comments, this require further additions to the discussion but we have endeavour to keep this brief (please see lines 309 - 326 and throughout the discussion).

• Minor points:

• To improve reproducibility, the suppliers of all reagents should be specified together with their catalogue numbers
• Figure 7: it is unclear which data are statistically significant
• Figure 7B: fertilization capacity should be assessed at an earlier stage, as the cleavage rate to 2-cell embryo may be affected by factors unrelated to the sperm ability to fertilize

__Answer: __We thank the reviewer for these suggestions. We have now added supplier information and catalogue numbers for all reagents to the Methods section to improve reproducibility (please see lines 1256 - 1257, 1295, 1299, 1310, 1333 - 1334, 1343 - 1344, 1388 - 1389, 1401, 1406). We have revised Figure 7 and its legend to clearly indicate statistically significant differences, including sample sizes and statistical tests used. Lastly, we agree that assessment at earlier fertilisation stages would complement our featured assessment of sperm fertilisation competence. Regrettably, all IVF data were generated via standardised and unbiased IMPC/EMMA pipelines. As such, cleavage rate to the 2-cell stage represents the earliest uniformly available endpoint across all knockout lines. We have clarified this limitation in the revised manuscript (please see lines 723 - 724).

REVIEWER #3

This is technically sophisticated phosphoproteomic study of mouse sperm maturation across the epididymis and during capacitation. The dataset is deep (>14,000 phosphosites) and the analyses integrate high-resolution MS, immunofluorescence, IPA, kinase mapping, pharmacological inhibition, and knockout mouse models. The manuscript represents a nice resource for the field. However, several issues limit clarity, mechanistic interpretation, and robustness of the conclusions. In particular, the manuscript's scope is extremely large, making some conclusions insufficiently supported, and some analyses require better control, methodological transparency, or deeper mechanistic connection. It gives the impression that some mechanistic data was added to descriptive data in order to increase the manuscript's impact, although the current mechanistic data is not convincing.

Major concerns

1. Conceptual Overreach - "Epididymal maturation accounts for 86% of phosphorylation changes" The manuscript repeatedly emphasizes that epididymal maturation causes the majority of phosphoproteomic remodeling. While the data indeed show large quantitative differences, several conceptual issues remain:

2. • The caput vs. cauda comparison includes differences in protein abundance, not only phosphorylation*
3. • Many phosphosites lost in the cauda may reflect protein loss, not dephosphorylation (the authors acknowledge this, but quantitative controls are insufficient)*
4. • The normalization method for phosphopeptide abundance vs total protein abundance is needed*
5. • It is unclear whether the same amount of starting material and equal protein loading were used across stages I would suggest to perform (or explicitly describe) normalization using matched proteome intensities. Provide supplementary plots showing phosphosite/parent-protein normalization to avoid overinterpreting phosphosite loss as dephosphorylation*

__Answer: __We thank the reviewer for this important and constructive critique and agree that interpretation of phosphoproteomic changes during epididymal maturation must carefully consider concurrent remodelling of the underlying sperm proteome.

To directly address the concern that phosphosites lost in the cauda may reflect protein loss, not dephosphorylation, we have now explicitly compared these phosphoproteins lost during caput-to-cauda transit with proteins shown to be lost or reduced over the same maturation window in a previously published matched proteomic analysis of the same sperm populations. This comparison revealed that 527 phosphoproteins, out of a total of 966 phosphoproteins lost, overlapped with proteins lost during epididymal maturation, while a further 88 phosphoproteins aligning with proteins exhibiting reduced abundance during transit. While these data indicate that a subset of phosphosite loss can be attributed to complete loss of the parent protein, the remaining phosphoproteomic changes (45.4%) cannot be fully explained by protein disappearance alone and are therefore consistent with extensive phosphoproteomic remodelling. We have documented this information in a new panel of Supplementary Figure 1 (Figure S1B) and the corresponding text has been revised accordingly (please see lines 182 - 188).

With respect to normalisation strategies, we respectfully note that normalisation of phosphopeptide intensities to total protein abundance is not universally accepted in large-scale phosphoproteomic analyses (PMID: 30190555, 34857927, 38576152), particularly in systems undergoing extensive proteome remodelling such as maturing spermatozoa. In many contexts, including our own previous work, phosphoproteomic analyses are performed on equal protein input and interpreted at the level of phosphopeptide abundance, with functional relevance established through orthogonal biological validation rather than ratio-based correction to total protein levels.

Lastly, all samples in this study were diluted to equal total protein amounts prior to phosphopeptide enrichment, ensuring consistent input material across all sperm populations (originally noted in the manuscript, please see line 1339). We have now clarified this explicitly in the Results section to ensure this is not missed (please see lines 146 - 147). Moreover, our conclusions are supported by independent in-silico analyses, pharmacological inhibition studies, and in vivo knockout models, collectively providing functional validation that extends beyond phosphosite quantification alone.

Finally, to address concerns regarding potential conceptual overreach, we have revised the language surrounding the statement that epididymal maturation accounts for ~86% of phosphorylation changes to ensure precise interpretation. Specifically, we have clarified that this value refers to the proportion of statistically significant differences in phosphopeptide abundance detected across maturation stages, to avoid implying direct measurement of net enzymatic dephosphorylation (please see lines 519 - 520).

Importantly, having addressed the reviewer's concerns detailed above, we believe the data do support the conclusion that the majority of sperm phosphoproteomic remodelling occurs during epididymal maturation rather than during capacitation. While we have tempered our language to improve clarity, the central quantitative observation that epididymal transit represents the dominant phase of phosphoproteomic remodelling remains supported by the revised analyses.

• Capacitation analysis is underpowered and oversimplified*

The authors state that capacitation leads to "modest" changes. However:

• • The capacitation protocol uses dibutyryl-cAMP + pentoxifylline, which may bypass early physiological signaling. This is a important red flag __Answer: __We thank the reviewer for this important point and agree that the choice of capacitation conditions influences the nature and magnitude of signalling events detected. The use of dibutyryl cAMP and pentoxifylline represents a well-established and widely adopted experimental model to induce robust and synchronised capacitation-associated signalling in mouse spermatozoa, acting specifically via the activation of the canonical cAMP/PKA signalling axis (PMID: 36384108, 22458710, 16221991). While we acknowledge that this approach bypasses some upstream physiological signalling events that initiate capacitation during sperm transit of the female reproductive tract, it is intentionally employed to provide a reproducible capacitation stimulus, specifically enabling us to discriminate phosphorylation changes associated with the attainment of sperm fertilization competence. This strategy also directly addresses a limitation of working with mouse spermatozoa in which these cells rapidly succumb to cell senescence/death within a matter of ~1-3 hours in an in vitro* setting. In our previous studies, we have noted that this time period is insufficient to achieve high levels of capacitation among populations of mouse spermatozoa, unless pharmacological agents (i.e. dibutyryl-cAMP + pentoxifylline) are supplemented to accelerate capacitation (PMID: 15252132). This is now a widely accepted paradigm in the field and one that enables us to deliver on our stated objective of assessing the phosphorylation status of fertilization competent spermatozoa, as opposed to those that are captured during early phases of the capacitation cascade.

Importantly, our conclusion that capacitation is associated with comparatively fewer phosphoproteomic changes is based on direct quantitative comparison with epididymal maturation under identical analytical conditions, and is not intended to downplay the biological importance of this critical maturation event. Even under the capacitation-inducing conditions employed herein, the scale of phosphoproteomic remodelling observed was substantially smaller than that occurring during epididymal transit, underscoring the influence of epididymal maturation over the status of the sperm phosphoproteome.

To address this concern, we have revised the manuscript to clarify that the capacitation-associated phosphoproteomic changes reported here are specific to the experimental model used and likely represent a conservative estimate of signalling complexity under physiological conditions. We have also tempered language implying generalisation beyond this context (please see lines 329 - 332, 488 - 491, 673 - 677).

• *

• Kinase prediction and functional validation require more rigor*

The identification of 343 kinases that may regulate phospho-changes is extremely broad. Issues:

• • The kinase-substrate assignments rely heavily on in silico predictions (IPA, PhosphoSitePlus), which often contain non-sperm data. __Answer: __We thank the reviewer for this important observation and fully agree that kinase-substrate assignments inferred from in-silico* resources such as IPA and PhosphoSitePlus are largely derived from non-sperm systems and therefore must be interpreted cautiously.

Importantly, this limitation reflects a broader and well-recognised gap in the field; regrettably comprehensive, experimentally validated kinase-substrate networks do not currently exist for mammalian spermatozoa on this scale, particularly in the context of epididymal maturation and capacitation. The primary objective of the present study was therefore not to define definitive kinase-substrate relationships, but to generate a high-depth, sperm-specific phosphoproteomic resource that can serve as a foundation for hypothesis generation and future mechanistic interrogation.

Accordingly, in-silico kinase prediction tools were employed to contextualise the phosphoproteomic data and to prioritise candidate kinases for functional testing, rather than to assert sperm-specific kinase-substrate specificity. We have revised the manuscript to clarify that these predictions represent informed starting points in a system where such information is currently lacking, and that functional relevance was subsequently assessed using complementary pharmacological and genetic approaches (please see lines 383 - 388, 682 - 686).

By providing a deep, stage-resolved phosphoproteomic dataset encompassing more than 14,000 phosphosites, this study establishes a much-needed reference framework for the reproductive biology community, enabling future targeted validation of kinase-substrate relationships in sperm. We believe this resource-based contribution represents a major strength of the work and addresses a critical knowledge gap in the field.

• *

• • Please explain the rationale by which, from 343 candidate kinases, 3 (STK33, HIPK4, PAK1) are selected.*
• • The pharmacological inhibitors used have off-target effects (ML281 inhibits multiple CMGC kinases; Foretinib inhibits MET/VEGFR; NVS-PAK1-1 inhibits PAK1/2/3).*
• • No control experiments are included to confirm kinase inhibition in sperm (e.g., phosphosite-specific Western blots)* __Answer: __We split this comment from the above, to best address this important critique. We agree that kinase-substrate relationships inferred from phosphoproteomic data must be interpreted with caution. The identification of 343 kinases in this study was not intended to represent a definitive catalogue of all sperm-specific kinase-substrate interactions, but rather to provide insights into kinases that potentially contribute to phosphoproteomic remodelling of mouse spermatozoa during the different phases of their post-testicular maturation. These kinases were identified through integration of multiple complementary approaches, including direct detection within the phosphoproteome, upstream regulator prediction using IPA, curated kinase-substrate databases, and comparison with previously published epididymal sperm proteomes.

From this broader resource, we deliberately restricted functional interrogation to a small subset of kinases putatively associated with capacitation-induced phosphoproteomic changes. STK33, HIPK4, and PAK1 were selected based on their predicted association with capacitation-specific phosphorylation events, representation across distinct kinase families, lack of prior functional characterisation in terms of either sperm maturation or function, and availability of well-characterised pharmacological inhibitors suitable for functional perturbation. We fully acknowledge that the inhibitors employed are not absolutely kinase-specific and may exhibit off-target effects. Accordingly, we have revised the manuscript to clarify that these experiments are intended to test functional dependence on kinase activity rather than to establish direct kinase-substrate relationships. The observation that combined inhibition of three mechanistically distinct kinases produced a robust and additive suppression of the acrosome reaction supports the conclusion that kinase activity is required for this process, while avoiding overinterpretation of individual kinase specificity.

We have revised the language throughout the manuscript to more clearly reflect these limitations and to frame the kinase inhibition experiments as functional validation of phosphoproteomic predictions rather than definitive mechanistic proof (please see lines 383 - 388, 405 - 406, 682 - 686, 705 - 710).

• *

• *

• The knockout-mouse validation section is underdeveloped*

The linkage of KO phenotypes to phosphorylation changes is potentially powerful but currently weak.

Issues:

• • Most KOs are systemic deletions, not sperm-specific; phenotypes could stem from developmental defects.*
• • Some proteins validated (e.g., ACO2, CMPK1) regulate core metabolism; their phenotypes may not reflect phosphoregulation but loss of essential protein function.*
• • No evidence is provided that the KO affects the specific phosphosites detected in the MS dataset.* __Answer: __We thank the reviewer for this important clarification. We agree that since the knockout models employed represent systemic deletions, they cannot directly resolve sperm-specific or phosphosite-specific mechanisms, and it was not our intention to suggest otherwise. We have revised the manuscript to explicitly frame the knockout phenotypes as evidence of physiological relevance of the identified phosphoproteins, rather than as direct validation of individual phosphorylation events (please see lines 723 - 734).

We further clarify that for proteins with central metabolic roles, the observed phenotypes likely reflect loss of essential protein function rather than isolated disruption of phosphoregulation. Accordingly, we have tempered our language and emphasise that these data support functional importance while highlighting the need for future studies employing germ cell-specific or phosphosite-targeted models (please see discussion).

• *

• Immunofluorescence and Western blots need improved quantification*

Figures showing PKA substrate, pY, pT, pS changes are visually compelling but lack:

• • quantification across biological replicates*
• • explanation of antibody specificity (e.g., pan-PKA sites include RRXS/T motifs; cross-reactivity possible). __Answer: __We thank the reviewer for this comment and appreciate the emphasis on rigor in antibody-based analyses. We would like to clarify that the immunofluorescence and immunoblot data presented in this study do include densitometric based quantification taking into account data generated from three independent biological replicates. This is indicated by the inclusion of error bars and as stated in the relevant figure captions. (please see lines 1164 - 1168 "All immunoblotting experiments were repeated with at least three biological replicates. Densitometric data normalization was performed against the loading control protein GAPDH, and each value subsequently expressed as a fold change relative to the caput sperm. Data were analyzed by one way ANOVA with GraphPad Prism.).*

With respect to antibody specificity, we fully agree that phospho-specific and motif-based antibodies have inherent limitations, including epitope ambiguity and the inability to resolve site-specific phosphorylation with amino acid precision (please see our answer to Comment #2 from Reviewer #1 above). For this reason, the antibodies employed here represent well-established, widely used markers in sperm biology and were included to illustrate global phosphorylation trends rather than to validate individual phosphosites. Importantly, quantitative and site-resolved interpretation of phosphorylation dynamics throughout the manuscript is derived from mass spectrometry based phosphoproteomics, which provides substantially greater specificity and resolution than antibody-based approaches.

• *

• Many interpretations about metabolism, storage, oxidative stress, and quiescence are speculative*

The discussion provides attractive models linking phosphorylation to:

• • suppression of glycolysis*
• • quiescent metabolic state in cauda epididymis*
• • activation of antioxidant pathways*
• • UPR and proteostasis modifications However, no direct functional evidence is provided for any of these pathways.*

__Answer: __We thank the reviewer for this thoughtful observation and agree that several interpretations linking phosphorylation changes to metabolic regulation, oxidative stress, proteostasis, and cellular quiescence are necessarily inferential in the absence of direct functional assays. With this in mind, we have revised the Discussion to more clearly distinguish data-driven observations from hypothesis-generating interpretations and have tempered language accordingly. These models are now explicitly framed as conceptual frameworks arising from large-scale phosphoproteomic analysis, intended to guide future targeted investigation rather than to assert definitive mechanistic conclusions (please see lines 588, 590, 596 - 599, 609, 613, 621 - 625 ).

Given the breadth and depth of the dataset, only a limited number of functional pathways could be explored experimentally within the scope of the current study. We anticipate that the phosphoproteomic resource generated here, supported by the accompanying ShinySpermPhospho application, will enable the wider community to interrogate additional pathways and to design focused mechanistic studies building on these findings.

• Acrosome reaction evaluation*

I have encountered significant deficiencies in this approach. On one side, testing the effect of a single dose of inhibitors on a specific readout is too preliminary, as stated above. In addition, and due to the presence of possible off target effects, more than one inhibitor is expected to be tested, or a direct biochemical assay to confirm at least targeted action. Even KO models, as proposed for other proteins in Figure 7.

Acrosome reaction values are expected to be presented, as regularly done, by indicating acrosome reacted percentages, without normalizations that complicate understanding. In addition, consider Pg as a more physiological stimulus instead of A23187 for triggering AR.

__Answer: __We thank the reviewer for these constructive comments and agree that careful assessment of inhibitor effects on sperm viability and motility is essential. We would like to clarify, in case this was overlooked, that these controls were performed and are presented in Supplementary Figure S4. Specifically, sperm were exposed to four concentrations of each inhibitor and assessed over time (0 and 60 minutes) for viability, total motility, and progressive motility. Across all concentrations, time points, and treatment conditions, including combined inhibitor treatments, no significant reductions in sperm viability or motility parameters were observed. These data support the conclusion that the effects on acrosome reaction are not secondary to general sperm toxicity.

With respect to data presentation, acrosome reaction values were expressed relative to matched capacitated vehicle-treated controls to account for biological variability in absolute acrosome reaction rates observed between independent sperm preparations and experimental days. This normalisation strategy was used to facilitate direct comparison between treatment groups, and respectfully, we have elected to retain this presentation format in Figure 6. Nonetheless, in the interest of transparency, we have now included the raw acrosome reaction values/ranges in the supplementary material (Table S6) and have provide these as a figure to the reviewer for reference.

We agree that the use of progesterone represents a more physiological stimulus for inducing the acrosome reaction. However, there is no single universally accepted approach for acrosome reaction induction, and calcium ionophore-based assays remain widely used to assess the capacity for acrosomal exocytosis under defined experimental conditions. In the present study, this approach was selected to provide a robust and reproducible functional readout suitable for comparative analysis.

We have revised the manuscript to more clearly describe the dose-response and viability control experiments, to acknowledge potential off-target effects of kinase inhibitors, and framed the acrosome reaction assays as functional screening experiments rather than definitive mechanistic dissection (please see lines 415, 705 - 710, Table S7).

• *

• Figure legend to Figure 7. How many oocytes, how many replicates were performed. How many transfers. Please add important data to the legend.*

__Answer: __We thank the reviewer for highlighting this omission. In line with comment 4 from Reviewer #1 (please see above), we have revised the Figure 7 legend and Methods section to provide detailed information regarding sample size and experimental design, including the number of oocytes used per IVF experiment performed and the number of biological replicates.

Specifically, IVF and oocyte isolation procedures were conducted according to standardised INFRAFRONTIER protocols (PMID: 25414328, 27262858, 38839949). Across knockout lines, IVF experiments were performed over 1 - 6 independent cycles per line, with an average of 24.2 oocytes used per cycle. To provide transparency regarding this variability, we have included a new supplementary figure (Figure S6) summarising the average number of oocytes used per IVF cycle alongside the corresponding cleavage rates (%CR).

Sperm samples used in these assays were derived from cryopreserved cauda epididymal spermatozoa pooled from 10 heterozygous males per knockout line, as per EMMA guidelines (PMID: 17709347). Additionally , where available, we have incorporated reproductive outcome measures at the level of individual litters (e.g. average pup number and sex distribution) to provide further biological context. These additions improve transparency and ensure that the experimental design and data interpretation are clearly defined (please see lines 453 - 457, 1228 - 1234, 1431 - 1444, 1533 - 1536, 1572 - 1575, Figure 7 & S6).

• *

This is technically sophisticated phosphoproteomic study of mouse sperm maturation across the epididymis and during capacitation. The dataset is deep (>14,000 phosphosites) and the analyses integrate high-resolution MS, immunofluorescence, IPA, kinase mapping, pharmacological inhibition, and knockout mouse models.

__Answer: __We thank the reviewer for this positive assessment and for recognising the technical sophistication and integrative nature of the study. We are also grateful for the constructive feedback provided, which has helped us to substantially strengthen the clarity, rigor, and presentation of the 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 is technically sophisticated phosphoproteomic study of mouse sperm maturation across the epididymis and during capacitation. The dataset is deep (>14,000 phosphosites) and the analyses integrate high-resolution MS, immunofluorescence, IPA, kinase mapping, pharmacological inhibition, and knockout mouse models. The manuscript represents a nice resource for the field. However, several issues limit clarity, mechanistic interpretation, and robustness of the conclusions. In particular, the manuscript's scope is extremely large, making some conclusions insufficiently supported, and some analyses require better control, methodological transparency, or deeper mechanistic connection. It gives the impression that some mechanistic data was added to descriptive data in order to increase the manuscript's impact, although the current mechanistic data is not convincing.

Major concerns

1. Conceptual Overreach - "Epididymal maturation accounts for 86% of phosphorylation changes" The manuscript repeatedly emphasizes that epididymal maturation causes the majority of phosphoproteomic remodeling. While the data indeed show large quantitative differences, several conceptual issues remain:
   • The caput vs. cauda comparison includes differences in protein abundance, not only phosphorylation.
   • Many phosphosites lost in the cauda may reflect protein loss, not dephosphorylation (the authors acknowledge this, but quantitative controls are insufficient).
   • The normalization method for phosphopeptide abundance vs total protein abundance is needed.
   • It is unclear whether the same amount of starting material and equal protein loading were used across stages.

I wwould suggest to perform (or explicitly describe) normalization using matched proteome intensities. Provide supplementary plots showing phosphosite/parent-protein normalization to avoid overinterpreting phosphosite loss as dephosphorylation. 2. Capacitation analysis is underpowered and oversimplified The authors state that capacitation leads to "modest" changes. However: - The capacitation protocol uses dibutyryl-cAMP + pentoxifylline, which may bypass early physiological signaling. This is a important red flag 3. Kinase prediction and functional validation require more rigor The identification of 343 kinases that may regulate phospho-changes is extremely broad. Issues: - The kinase-substrate assignments rely heavily on in silico predictions (IPA, PhosphoSitePlus), which often contain non-sperm data. - Please explain the rationale by which, from 343 candidate kinases, 3 (STK33, HIPK4, PAK1) are selected. - The pharmacological inhibitors used have off-target effects (ML281 inhibits multiple CMGC kinases; Foretinib inhibits MET/VEGFR; NVS-PAK1-1 inhibits PAK1/2/3). - No control experiments are included to confirm kinase inhibition in sperm (e.g., phosphosite-specific Western blots). 4. The knockout-mouse validation section is underdeveloped The linkage of KO phenotypes to phosphorylation changes is potentially powerful but currently weak. Issues: - Most KOs are systemic deletions, not sperm-specific; phenotypes could stem from developmental defects. - Some proteins validated (e.g., ACO2, CMPK1) regulate core metabolism; their phenotypes may not reflect phosphoregulation but loss of essential protein function. - No evidence is provided that the KO affects the specific phosphosites detected in the MS dataset. 5. Immunofluorescence and Western blots need improved quantification Figures showing PKA substrate, pY, pT, pS changes are visually compelling but lack: - quantification across biological replicates - explanation of antibody specificity (e.g., pan-PKA sites include RRXS/T motifs; cross-reactivity possible). 6. Many interpretations about metabolism, storage, oxidative stress, and quiescence are speculative The discussion provides attractive models linking phosphorylation to: - suppression of glycolysis - quiescent metabolic state in cauda epididymis - activation of antioxidant pathways - UPR and proteostasis modifications However, no direct functional evidence is provided for any of these pathways. 7. Acrosome reaction evaluation I have encountered significant deficiencies in this approach. On one side, testing the effect of a single dose of inhibitors on a specific readout is too preliminary, as stated above. In addition, and due to the presence of possible off target effects, more than one inhibitor is expected to be tested, or a direct biochemical assay to confirm at least targeted action. Even KO models, as proposed for other proteins in Figure 7. Acrosome reaction values are expected to be presented, as regularly done, by indicating acrosome reacted percentages, without normalizations that complicate understanding. In addition, consider Pg as a more physiological stimulus instead of A23187 for triggering AR. 8. Figure legend to Figure 7. How many oocytes, how many replicates were performed. How many transfers. Please add important data to the legend.

Significance

This is technically sophisticated phosphoproteomic study of mouse sperm maturation across the epididymis and during capacitation. The dataset is deep (>14,000 phosphosites) and the analyses integrate high-resolution MS, immunofluorescence, IPA, kinase mapping, pharmacological inhibition, and knockout mouse models.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors examine dynamic modifications of the sperm phosphoproteome during epididymal transit and capacitation. They compare three distinct populations differing in anatomical localization and activation status: caput sperm, non‑capacitated cauda sperm, and capacitated cauda sperm. Using high‑resolution tandem mass spectrometry, they reveal that phosphorylation changes during epididymal passage are far more extensive than previously appreciated. These findings are further validated in genetically modified animal models, where disruption of selected genes encoding for phosphoproteins results in marked defects in sperm motility and fertilization capacity.

Major points:

Throughout the text, and particularly in the paragraph entitled 'Epididymal maturation accounts for the majority of maturation‑associated sperm cell signaling,' it seems that phosphorylation is interpreted as inherently activatory and dephosphorylation as inhibitory (lines 248-252). Since this relationship is not universally applicable, it would be valuable to address this issue at the outset of the paragraph and to discuss how phosphorylation events are context‑dependent in their effects on protein function.

Lines 392-393: the claim that "the introduction of each inhibitor to populations of capacitating spermatozoa led to a significant reduction..." is not fully supported by data and should be toned down. In fact, two out of three inhibitors, do not significantly affect the acrosome reaction.

The discussion section, spanning 11 pages, is overly long and contains considerable repetition. I recommend transferring the detailed description of experiments to the 'Results' section and using the discussion primarily to synthesize and highlight the novel findings while limiting speculative content. For example, the content in lines 509-530 could be condensed and relocated to the Results. Likewise, other detailed examples would be more appropriately presented within their respective result paragraphs.

Minor points:

• To improve reproducibility, the suppliers of all reagents should be specified together with their catalogue numbers.
• Figure 7: it is unclear which data are statistically significant
• Figure 7B: fertilization capacity should be assessed at an earlier stage, as the cleavage rate to 2-cell embryo may be affected by factors unrelated to the sperm ability to fertilize

Significance

A key novel finding of this work is that extensive changes in the sperm phosphoproteome occur during epididymal maturation, whereas capacitation is associated with comparatively modest modifications. This research provides a finely resolved description of phosphorylation events associated with the signaling pathways underlying functional sperm maturation. The methodological innovation -high‑resolution MS‑based phosphoproteomics- unlocks a level of detail and comprehensiveness in phosphorylation analysis that was previously unattainable. Moreover, the identification of previously unrecognized phosphoproteins in sperm cells, together with the development of a dedicated application hosting the complete dataset, represents a valuable resource for researchers in reproductive biology and particularly for experts in sperm development and maturation.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Skerrett-Byrne and collaborators represents a comprehensive and technically sophisticated phosphoproteomics study. Using high-resolution mass spectrometry on mouse sperm obtained from the caput and cauda regions of the epididymis, both before and after capacitation, the authors generated a more complete database of phosphorylation changes in these cells. One of the most interesting outcomes is that most of these changes occur during sperm maturation, rather than sperm capacitation. The work is important and relevant, and the information obtained could be valuable for reproductive biologists working in basic science, as well as for the identification of novel contraceptive targets.

Minor comments:

1) The title should include a reference to sperm capacitation, as most of the study focuses on comparisons between epididymal maturation and capacitation, and the functional experiments are based on the latter.

2) Considering the newly reported changes in phosphosites, it would be desirable to include validation at the individual protein level for at least a few examples, using an independent technique such as western blotting.

3) In the knockout models, it is not possible to distinguish between defects in spermatogenesis and those arising during maturation or capacitation. A parameter directly related to spermatogenesis should therefore be included, for example, testicular weight or histology, sperm number, and sperm morphology.

4) Error values, sample size, and statistical analyses are missing from Figure 7 and should be provided for clarity.

Significance

This study shows by high-resolution phosphoproteomics that most phosphorylation changes occur during epididymal transit rather than capacitation, challenging long-standing assumptions. The integration of the new datasets with functional validation of key kinases and knockout models strengthens the study; however, the work lacks single-protein validation of phosphorylation events, and the use of systemic knockouts does not allow confirmation of sperm-specific effects. The open ShinySpermPhospho dataset will be worthwhile to a broad audience of reproductive biologists and cell signaling specialists, and may be of value for future studies on male fertility and the development of novel male contraceptives.

Field of expertise: reproductive physiology, sperm biology and capacitation, gamete interaction.

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Reply to the reviewers

We thank the reviewers and we are glad that they acknowledge this work to be a timely contribution to a quickly moving field and a valuable tool to generate testable hypothesis. We are pleased that reviewer #2 highlights that “a major strength is the combination of orthogonal evidence types” and that the tool serves to generate novel hypothesis. The revised manuscript will sharpen the positioning of the study within this context. Additional experimental evidence will be provided to address the points raised by reviewers #1 and #3.

Reviewer #1* 1.The authors do not co-IP ARF1. This does not surprise me as small GTPases often hydrolyse their GTP during lysis. *

We agree that this is likely due to transient association and GTP hydrolysis during lysis and will add a section to the manuscript.

There have been a number of ARF1 bioID screens done- have the authors checked if their complex has turned up here?

We will include this in the revised manuscript.

1. I am a bit confused by some of the interpretation about KO and loss of JTB staining. They interpret: "The SYS1 acts as a Golgi recruitment factor for both ARFRP1 and JTB". The ARFRP1 has been published and is a cytosolic protein, so that makes sense. However, the JTB is not cytosolic by a membrane protein, so cannot be "recruited". Now maybe it is retained in the Golgi by this interaction, but if that is the case you would still expect signal on another organelle or the plasma membrane (and we see it isnt degraded in the lysosome due to the western blot). I am confused by the authors model here.

We will clarify the phrasing and will provide a clearer interpretation, also considering the other improved imaging experiments that will be included in the revised manuscript.

4.The authors validate their JTB antibody and confirm the fact that there are not reduced SYS1 levels in the JTBKO- this is very clear (albeit unquantified). What I do not see validated is the SYS1KO. I think this is quite important.

We will validate SYS1 KO using TIDE and/or western blotting.

5.The colocalisation in panel 3D is weak and unclear to me. It is not quantified. It is not clear if there have been 3 repeats.

The revised manuscript will include improved imaging data. We will repeat relevant experiments, include appropriate controls and quantify where necessary.

6.The imaging in figure 3 is not clear in places, and it stands out in a very clear manuscript. I cannot see the JTB in panel F. There are no scale bars. The dynamic range of the image is not utalised. I do not see the stain in the JTB in either of the sys1 KO, i do not see the SYS1-FLAG staining in the complement, and it is not quantified at all. It may all seem trivial, but (to me) this is an absolutely critical bit of biology data to support the informatics.

The revised manuscript will include improved imaging data. We will repeat relevant experiments, include appropriate controls and quantify where necessary.

7.I am a bit unconvinced by the interpretation of it being a retrograde trafficking complex. This is for 2 key reasons- 1) the VSV-G is antrograde (despite unusually they interpret a "severe defect in retrograde transport"). 2) Even if it was only having an effect in the retrograde direction I would still remain a little open minded about it as you can easily mistake trafficking of a protein in one direction for another if an unknown protein (SNARE for example) has defective trafficking.

We used VSVG-KDEL in this assay. This setup specifically measures retrograde trafficking. We will clarify this in the revised manuscript. We will clarify in the Discussion that we confirmed a role in retrograde trafficking but cannot exclude a role in anterograde trafficking

Reviewer #2

Major comment: scope and interpretation of DepMap-derived functional evidence The manuscript could benefit from more clearly defining the scope of the functional evidence used to nominate complexes. The central co-dependency signal is derived from DepMap 24Q2 CRISPR gene-effect profiles, which are primarily cancer cell-line fitness/proliferation data. This is an important limitation because the resulting correlations may preferentially capture complexes or pathways that influence viability in proliferating cancer cells, while missing complexes active in differentiated, tissue-specific, stimulus-dependent, or non-proliferative contexts. Conversely, some correlations may reflect shared cancer-lineage or fitness dependencies rather than direct participation in a stable complex. The authors are appropriately cautious in stating that DepCom is not a complete inventory of human protein complexes, but the title, framing, and resource description could still be read as implying a more general catalogue of functional protein complexes. The authors might consider adding a clearer introduction to DepMap and explicitly discuss how the cancer-cell-line origin of the data affects interpretation of the 518 predicted complexes. This could be addressed without new experiments, for example by adding text early in the Results section explaining what the CRISPR gene-effect scores measure, and by expanding the Discussion to clarify that DepCom represents structurally plausible complexes prioritized by co-dependency across cancer cell lines, rather than an unbiased or context-independent map of human protein complexes. The selection of highlighted examples would also benefit from clearer justification. The peroxisome, actin, WNK/TSC22D2, and Golgi/JASS examples are biologically interesting, but the rationale for choosing them is not always explicit. Were they selected because they were novel, high-confidence, disease-associated, experimentally tractable, or representative of different resource categories? Briefly stating the selection criteria would help readers understand whether these examples are illustrative case studies or representative outcomes of the pipeline.

We agree with the reviewers' assessment that this resource should be viewed as hypothesis-generating and that the overall framing should be improved. We will revise the manuscript at the appropriate sections, according to the more detailed comments of all reviewers.

Minor comments

1. Clarify post-clustering removal of large/problematic protein families and complexes. In the Methods, the authors state that "clusters of histones and keratin clusters, as well as the mito-ribosome, complexes of the electron transport chain and the mediator complex" were removed because of their large sizes. This filtering step would benefit from additional detail. Please specify the criteria used to define these removed clusters, how many clusters/proteins were removed at this stage, and whether removal was based only on size or also on biological/manual curation. It would also be helpful to explain why these proteins or clusters were removed after clustering rather than excluded before graph construction and clustering, since highly connected or compositionally biased protein families could potentially influence neighboring cluster assignments. If available, a brief robustness check showing that pre-removal of these proteins gives similar candidate complexes would strengthen confidence in the clustering procedure.

We will add the requested information to the relevant section. Alongside the manuscript we will also provide lists of the complexes before and after every filtering step

1. Clarify the rationale for excluding complexes larger than 5000 residues. The 5000-residue cutoff is understandable for AF3 computational cost, but the manuscript should briefly state how many candidate complexes were excluded by this cutoff and whether this preferentially removes known large assemblies. This would help readers understand the scope of complexes that DepCom is expected to miss.

Alongside the manuscript we will now also provide lists of the complexes before and after every filtering step.

1. Improve wording in the CAP1/CFL1/WDR1/ACTB example. The sentence "Additionally, CAP1 works in concert with CFL1 to accelerate depolymerisation, though if a four-protein complex consisting of actin, WDR1, CAP1 and CFL1 is relevant is not clear" is difficult to parse. Possible revision might be something like: "Additionally, CAP1 works in concert with CFL1 to accelerate depolymerisation, although it remains unclear whether actin, WDR1, CAP1 and CFL1 form a stable four-protein complex in cells." This more clearly separates known biology from the speculative interpretation of the DepCom prediction.

Wording will be improved.

1. Improve reproducibility details for AF3 predictions. The Methods state that predictions were run using a local AF3 installation, but reproducibility would be improved by reporting relevant AF3 settings, number of seeds/models per complex, whether templates were used, how disordered regions were handled, and whether predictions were repeated for all complexes or only selected examples. This is especially important because the manuscript notes that multiple predictions can yield different subunit arrangements.

We will provide detailed settings in the methods section. Regarding disordered parts: All predictions used full length sequences (canonical UNIPROT ID) for each protein, so disordered residues are included. If disordered regions have low PLDDT and poor PAE, these regions will simply not score as interfaces in AlphaBridge. The one exception where we did crop structures is Figure 2D, but purely for visualization purposes, the full length complex did score in the pipeline (uncropped).

Reviewer #3

Co-essentiality is not the same as physical complex membership. This is the biggest conceptual concern. Genes in the same pathway are co-essential whether or not their products bind. The authors lean on the structural prediction step to filter this out, but that means the entire pipeline rests on AF3+AlphaBridge being correct about who interacts with whom. There is no independent benchmarking shown of how often AlphaBridge calls a true positive vs a false positive at the chosen 0.5 cutoff. Why 0.5? Where does that number come from? A short benchmarking section using known complexes (CORUM 5.0, hu.MAP 2.0, the PDB) would make the choice defensible. Right now it reads as arbitrary.

We thank the reviewer for bringing up the need for such an important clarification. We fully agree that co-essentiality does not equal physical interaction and structure predictions are imperfect. This is precisely the logic underlying our pipeline design, not a limitation we overlooked. The two data sources are used sequentially and serve distinct roles: first, we construct protein sets that are connected through networks of predicted binary physical interactions; then we cluster these based on DepMap correlations, selecting likely physical complexes that display co-essentiality between their components.

In other words, clustering on DepMap data alone would certainly return many spurious correlations: as the referee points out “Co-essentiality is not the same as physical complex membership”. Anchoring the search space with structural predictions substantially reduces this noise. Neither data source alone is sufficient, nor do we claim either is definitively "correct": the value lies in their combination. We hope improved phrasing in the revised manuscript will highlight this better.

Regarding benchmarking AlphaBridge score: we have benchmarked AlphaBridge, in response to reviewer feedback on the original AlphaBridge paper (Structure, Cell Press). In the figure here it is clear that in our benchmark of PDB structures (with

Comparison to existing resources is incomplete. I can't help but wonder what was found here that would not have been possible by analysing existing resources. CORUM 5.0 (7,193 mammalian complexes, ~71% human-derived; Tsitsiridis et al. 2024 NAR), hu.MAP 2.0 (Drew et al. 2021, ~6,965 complexes from >15,000 MS experiments), BioPlex 3.0 (Huttlin et al. 2021, 118,162 interactions in HEK293T), ad the Complex Portal already cover a large fraction of the human complexome. The authors compare to PDB, the original interactome paper, and Complex Portal, but they explicitly skip CORUM and hu.MAP, both of which are central reference resources in this space. Without including these, the "60 complexes unique to DepCom" number is not really meaningful. This needs to be redone properly.

We will add the comparison with Corum and hu-MAP in the revision.

Validation rate is one out of 518. The JASS work is solid, but a single experimentally validated complex out of 518 gives the reader essentially no estimate of how often the rest of the predictions are correct. Even a smaller systematic effort, say IP-MS on five to ten predicted novel complexes in the same cell line, would do an enormous amount to establish how trustworthy the resource is. The authors already have the V5/IP-MS pipeline running. Right now the manuscript implicitly asks the reader to trust 517 predictions on the strength of one validation.

In this paper we validated one out of the 60 complexes we claim are new. Notably we provide new biological data and demonstrate how consulting our resource, or following the same logic of combining functional and structural information, can lead to new exciting discoveries. We note that out of the 518 complexes we list, 69 complexes are exactly mirrored in the PDB and/or Complex Portal, while for another 389 there is partial evidence. Thus, our dataset is amply validated, and at the same time contains data to enable new discoveries. We also note, that following the release of our resource eight months ago, a new high-impact publication “validated” a complex we have independently picked in DepMap (Oosterheert et al, Choreography of rapid actin filament by coronin, cofilin and AIP1, Cell, 2025). We will rephrase relevant sections (also in response to reviewer 2) to increase clarity about validation.

The functional and disease clustering is potentially circular. GO terms and STRING associations are themselves derived in large part from the published literature on protein function, including text mining channels in STRING, much of which is downstream of complex membership. Of course complexes cluster into "DNA repair" and "vesicle trafficking" if you cluster on GO and STRING. The same applies to Open Targets, which integrates GWAS Catalog, ClinVar, literature mining, and other sources. The clustering is fine as a navigation aid for the website, but it is not, as currently presented, an independent validation of anything. I would tone the discussion down accordingly.

We did not mean to present the clustering as an independent validation. We will tone down the discussion accordingly.

AF3 limitations on this class of problem. AF3 itself acknowledges limitations (Abramson et al. 2024, including the December 2024 addendum), and subsequent benchmarking has flagged disordered regions, dynamic/large assemblies, and certain transmembrane systems as known weak points. The JASS complex is largely transmembrane, the WNK1-TSC22D2 example involves disorder-to-order transitions, and several flagship examples involve large multi-domain proteins. The authors acknowledge some of this in passing but should state explicitly which complexes were trimmed, how the trimming choices were made, and whether predictions were repeated with different seeds to check stability. Figure S4 is a good start, but for a resource paper a more systematic seed-stability analysis is warranted.

No complexes were trimmed for the initial AF3 predictions. The WNK1-TSC22D2 example was trimmed and re-predicted only for visualization purposes. We apologize for the misunderstanding and will state this more clearly.

AF3 certainly has limitations. Regarding disordered regions, these will almost always be assigned a poor pLDDT (also if AF3 wrongly folds them into helices). AlphaBridge will not pickup these low pLDDT regions as interfaces. Regarding dynamic assemblies, these might again lead to poor confidence scores and consequently these will not be picked up as interfaces by AlphaBridge. If AF3 confidence metrics are analyzed properly, the main concern for both disordered regions and dynamic assemblies is to miss true positive interactions, rather than finding false positive. As we did not aim to identify all possible human complexes, we consider focusing on the most confidently predicted interactions to be a fair trade off.

While the JASS complex is indeed a membrane protein complex, the predictions are exceptionally confident across multiple seeds (we can provide predictions from multiple seeds for revision), and validates experimentally. Of course, structure predictions are no substitute for experimental structures, as cautioned multiple times throughout the manuscript.

Figure S4 shows that despite the complex overall geometry being flexible, the interaction sites are predicted with high confidence across different poses. Since the aim of this study was to identify proteins interacting with each other, not accurate structures (which need to be solved experimentally), we argue that recomputing all structures with multiple seeds is disproportionately expensive computationally and would delay publication of a timely study while adding little.

Statistics are thin in several places. On the Fisher exact test for Golgi/ER enrichment in V5-JTB IP-MS (Supplemental Table 1), an odds ratio of 2.77 is modest, and there is no comparison to a matched control IP. Is this more than expected by chance against an appropriate background? The IP-MS volcano plots show many significant proteins, but how was the background controlled? On the LLM section, no quantitative evaluation is presented at all and the assessment is admitted to be subjective.

We will qualify the conclusions drawn from the IP-MS experiments. We maintain that together with the additional cell biology data, we build a compelling and convincing picture for this JASS complex.

Experimentally, the background is controlled by measuring enrichment over WT cell lines that have undergone the same IP procedure as the V5-SYS1/JTB expressing cells (lysis, incubation with the anti-V5 conjugated beads, same wash procedure and sample processing), as is the standard in the field. We will clarify in the Methods section. Regarding identification, FDR rate was set to 1% at protein and peptide level and peptide spectrum matches (PSMs) were additionally filtered for SequestHT Xcorr score >1.

We agree with the referee that the LLM interpretation is subjective and cannot be benchmarked. We suggest revising the resource and the paper, only providing structured LLM prompts to facilitate users asking the right questions, but we will not provide the LLM answers as part of the resource.

The 4�ACTB speculation. The authors themselves note the AlphaBridge score declines from 0.9 (1�ACTB) to 0.78 (4�ACTB), yet they speculate about functional implications. This is exactly the kind of post-hoc rationalisation around weak evidence that should either be supported with experiment or removed. Either remove or qualify as speculative.

We will qualify this as speculative

The LLM-assisted analysis. I am genuinely uncomfortable with releasing 76 LLM-generated complex annotations as part of a published resource when the authors openly state these have "not been systematically validated". Putting these summaries on a website with the imprimatur of a peer-reviewed paper will lead to them being cited and reused. At minimum, the website needs prominent warnings on every page where an LLM summary appears, the prompts must be fully reproducible (not just downloadable as JSON), and a small validation table, say 10 complexes scored by a domain expert for accuracy of each claim, should be included as a supplemental figure. As it stands this section reads like an enthusiastic add-on that has not been thought through with the same care as the rest of the work.

We thank the referee for bringing forward this consideration. We agree to remove the LLM answers for the 78 complexes from the manuscript and from the website, to ensure that the outputs cannot be cited. We will provide two different objective structure prompts for download to encourage variety in responses for curious users who want to explore. We will add a prominent disclaimer noting that responses resulting from these prompts cannot be interpreted as facts without validation.

We cannot guarantee reproducibility with modern LLM inference architecture. Even if seeds are kept the same and temperature=0, floating-point non-determinism in GPU operations, distributed inference, and batch effects may lead to different results. Furthermore, models go through many different iterations rapidly. As a consequence, it is impossible for us to guarantee reproducibility

Cutoffs and cluster numbers need stability analysis. The cutoff for the 75th-percentile DepMap correlation (mean of random + 3 SD = 0.147) is reasonable but should be accompanied by an FDR or precision/recall estimate against a labelled reference set. The choice of 20 final clusters in functional clustering (because that gave a peak in silhouette score) and 14 for disease clustering should also be supported by stability analysis, e.g. resampling.

The 75th percentile cutoff is, in our opinion, well justified and sufficient for our purposes. FDR and precision recall need a set of true and false positives. The DepMap correlation clusters are an intermediate step in our pipeline and do not necessarily hold the final complexes. How can intermediate reference DepMap clusters be constructed and defined as true or false positives? Even if we would score clusters that contain a known complex as true positives, how to define false positives? If clusters do not contain a known complex, that does not necessarily mean that these proteins don’t interact, just that they have not been shown to interact yet.

We will run resampling to improve confidence in the choice of cluster number.

Internal numerical consistency. The bioRxiv preprint abstract refers to 354 high-confidence multi-protein complexes, while the body of the manuscript discusses 518 (224 dimers + 294 multimers). The relationship between these numbers should be stated explicitly. Likewise, the breakdown of "60 unique to DepCom" into 41 heterodimers + 19 multimeric should be reconcilable in the figures and tables. The number "9,764 unique seed proteins" should also be clarified to confirm it is the DepCom-internal seed set and not inherited from the Zhang et al. coverage or hu.MAP 2.0 (9,963 proteins). These are easy fixes but matter for a resource paper.

BioRxiv preprint: The preprint that the reviewer read is an older version, which will be updated. .

The 9,764 unique seed proteins is from the Zhang et al paper, and are the human proteins identified to confidently interact with at least one other human protein. We will make this more clear.

Mander's overlap coefficient. The VSV-G(ts045)-KDELR retrograde-transport assay is well established and the experiment is clean, but MOC has been increasingly criticised in the colocalisation literature (Adler & Parmryd 2010, 2021). Best practice is to also report Manders' M1/M2 coefficients or Pearson's correlation alongside MOC. Adding these would be straightforward and would strengthen Fig 4B.

We will improve co-localization measures where appropriate.

Minor comments 1. Page 4: "candidate sets of potential multi-protein complex members". Pick one, they are either candidates or potential, not both.

Will be addressed.

Page 7: "Complex 294... mechanistic basis for CFL1 and WDR1 cooperation has only recently been described". Please update the reference list and language given how recent this is.

Will be addressed.

Page 7: JTB is described as "poorly characterised". This is a bit too strong. JTB has been studied in the context of TGF-β-induced mitochondrial regulation (Kanome et al. 2007), cytokinesis and chromosomal passenger complex association (Platica et al. 2011), the structural characterisation of its extracellular domain (Rousseau et al. 2012), and breast cancer biomarker work (Jayathirtha et al. 2022). A more accurate framing would be "incompletely characterised, with previously reported but functionally unresolved roles". The novelty here is the Golgi connection, which is genuine.

We will rephrase.

Page 8: the citation of Blomen et al. 2015 Science for "Golgi-related synthetic lethality" should be checked against the actual supplementary data of that paper to confirm the JTB attribution is correct.

Will be check.

Figure 1: as in many omics papers, please think of us colourblind readers. The pink-green DepMap correlation scale will be hard for some of us.

The color scheme in use, alongside others, was tested with two colleagues that have different variants of colour blindness and was judged to be the best compromise.

Figure 5A and 5B: 21 and 14 colour-coded clusters respectively in a single UMAP is too much. Consider splitting into separate panels by broad theme or providing an interactive version only.

We will focus on a subsection, and provide the full interactive version on the homepage

Page 11: "manually evaluated the quality of outputs". By whom, blinded to which model produced which output? Methods are silent on this.

As stated above, we will remove the LLM part

Some figures show "hairballs" with very limited informative content. Fig. 1B left panel and the AlphaBridge wheel plots in particular convey relatively little at the size shown.

We will try and find a way to draw the AlphaBridge circular plots in better resolution; we do not however that the reviewer’s observation might be an artefact of the PDF file distributed to reviewers.

The reference list looks a bit thin on prior systematic complexome efforts. BioPlex 3.0 (Huttlin et al. 2021 Cell), hu.MAP 2.0 (Drew et al. 2021 MSB) and CORUM 5.0 (Tsitsiridis et al. 2024 NAR) should all be cited and discussed.

We will include the additional references where appropriate

The discussion section drifts into general comments about AI in science that don't add much. I would cut about a third of it and use the space for a more careful framing of the actual contribution.

We will shorten the discussion section and phrase more carefully.

General assessment Reviewer #3: The strongest aspect of this study is the JASS complex story. The IP-MS, the SYS1-KO rescue experiment, the VSV-G(ts045)-KDELR transport assay, and the orthogonal CRISPR screens with diphtheria and Pseudomonas exotoxins together build a convincing case for JTB as a regulator of Golgi-to-ER retrograde trafficking. This part of the paper is genuinely nice work and would stand on its own. The pipeline itself, combining structural predictions with functional dependency data and filtering with AlphaBridge, is sensible and timely. It is a reasonable demonstration of how confidence filtering should be done at this kind of scale. The main limitations concern the resource framing. After reading the manuscript several times I am still trying to identify the central novel contribution beyond the JASS validation. The interactome predictions are taken from Zhang et al., DepMap is public, AF3 is public, AlphaBridge is the authors' own previously published tool, and GO/STRING/Open Targets/dbPTM are all public. The manuscript is essentially an integrative pipeline plus a website plus one experimentally followed-up complex. The framing oversells what is genuinely new. The authors' own comparison (Fig. S3) shows 60 complexes "unique to DepCom" out of 518, of which 41 are heterodimers and only 19 are multimeric. Nineteen genuinely novel multi-protein complexes is still a contribution but it is a long way from the 354/518 that the abstract and discussion implicitly emphasise. The validation rate (one of 518) and the missing comparisons to CORUM 5.0 and hu.MAP 2.0 are the two issues that most need addressing.

We will rephrase these issue to adjust the framing. We would put forward that the main contribution of this manuscript is to present an integrative framework that combines data from orthogonal sources to highlight the possibility of structure prediction models to serve as a discovery tool. The reviewer identifies correctly (albeit derogatorily) that this is “essentially” an integrative pipeline. But it is an integrative pipeline that combines genetics and computational structure predictions in a novel (to the best of our knowledge) way and surfaces interesting new biology. The biology of the JASS complex goes well-beyond simple validation experiments, and we believe its discovery (based on our data) carries more value that the reviewer attributes to it.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Uckelmann and colleagues combine the recently published binary human interactome predictions from Zhang et al. (2025) with co-essentiality data from DepMap CRISPR screens to nominate sets of proteins that may form higher-order complexes. They cluster proteins around each "seed" using Leiden community detection on the DepMap correlation matrix, run AlphaFold3 on each candidate set, and apply AlphaBridge to retain only those interfaces predicted with confidence. After filtering they arrive at 518 complexes, of which 224 are dimers and 294 are larger assemblies (note: the abstract of the bioRxiv preprint refers to 354 high-confidence complexes, so the relationship between these numbers should be made explicit). They illustrate the resource with a few worked examples (PEX3/16/19/ACBD5, an actin-CFL1-WDR1-CAP1 assembly, a WNK1-NRBP1-TSC22D2 complex), and they experimentally validate one previously uncharacterised assembly that they name JASS (JTB-ARFRP1-SYS1), placing JTB at the Golgi and showing a role for it in Golgi-to-ER retrograde transport. They also provide a web portal (depcom.eu) with PTM mapping, GO/STRING-based functional clustering, Open Targets disease clustering, and LLM-generated executive summaries.

Major comments:

I am supportive of integrating orthogonal datasets in this kind of framework, but I am much less enthusiastic about how the analyses are carried through, and I think there are several issues that need adressing before this work is publishable.

1. Co-essentiality is not the same as physical complex membership. This is the biggest conceptual concern. Genes in the same pathway are co-essential whether or not their products bind. The authors lean on the structural prediction step to filter this out, but that means the entire pipeline rests on AF3+AlphaBridge being correct about who interacts with whom. There is no independent benchmarking shown of how often AlphaBridge calls a true positive vs a false positive at the chosen 0.5 cutoff. Why 0.5? Where does that number come from? A short benchmarking section using known complexes (CORUM 5.0, hu.MAP 2.0, the PDB) would make the choice defensible. Right now it reads as arbitrary.
2. Comparison to existing resources is incomplete. I can't help but wonder what was found here that would not have been possible by analysing existing resources. CORUM 5.0 (7,193 mammalian complexes, ~71% human-derived; Tsitsiridis et al. 2024 NAR), hu.MAP 2.0 (Drew et al. 2021, ~6,965 complexes from >15,000 MS experiments), BioPlex 3.0 (Huttlin et al. 2021, 118,162 interactions in HEK293T), and the Complex Portal already cover a large fraction of the human complexome. The authors compare to PDB, the original interactome paper, and Complex Portal, but they explicitly skip CORUM and hu.MAP, both of which are central reference resources in this space. Without including these, the "60 complexes unique to DepCom" number is not really meaningful. This needs to be redone properly.
3. Validation rate is one out of 518. The JASS work is solid, but a single experimentally validated complex out of 518 gives the reader essentially no estimate of how often the rest of the predictions are correct. Even a smaller systematic effort, say IP-MS on five to ten predicted novel complexes in the same cell line, would do an enormous amount to establish how trustworthy the resource is. The authors already have the V5/IP-MS pipeline running. Right now the manuscript implicitly asks the reader to trust 517 predictions on the strength of one validation.
4. The functional and disease clustering is potentially circular. GO terms and STRING associations are themselves derived in large part from the published literature on protein function, including text mining channels in STRING, much of which is downstream of complex membership. Of course complexes cluster into "DNA repair" and "vesicle trafficking" if you cluster on GO and STRING. The same applies to Open Targets, which integrates GWAS Catalog, ClinVar, literature mining, and other sources. The clustering is fine as a navigation aid for the website, but it is not, as currently presented, an independent validation of anything. I would tone the discussion down accordingly.
5. AF3 limitations on this class of problem. AF3 itself acknowledges limitations (Abramson et al. 2024, including the December 2024 addendum), and subsequent benchmarking has flagged disordered regions, dynamic/large assemblies, and certain transmembrane systems as known weak points. The JASS complex is largely transmembrane, the WNK1-TSC22D2 example involves disorder-to-order transitions, and several flagship examples involve large multi-domain proteins. The authors acknowledge some of this in passing but should state explicitly which complexes were trimmed, how the trimming choices were made, and whether predictions were repeated with different seeds to check stability. Figure S4 is a good start, but for a resource paper a more systematic seed-stability analysis is warranted.
6. Statistics are thin in several places. On the Fisher exact test for Golgi/ER enrichment in V5-JTB IP-MS (Supplemental Table 1), an odds ratio of 2.77 is modest, and there is no comparison to a matched control IP. Is this more than expected by chance against an appropriate background? The IP-MS volcano plots show many significant proteins, but how was the background controlled? On the LLM section, no quantitative evaluation is presented at all and the assessment is admitted to be subjective.
7. The 4×ACTB speculation. The authors themselves note the AlphaBridge score declines from 0.9 (1×ACTB) to 0.78 (4×ACTB), yet they speculate about functional implications. This is exactly the kind of post-hoc rationalisation around weak evidence that should either be supported with experiment or removed. Either remove or qualify as speculative.
8. The LLM-assisted analysis. I am genuinely uncomfortable with releasing 76 LLM-generated complex annotations as part of a published resource when the authors openly state these have "not been systematically validated". Putting these summaries on a website with the imprimatur of a peer-reviewed paper will lead to them being cited and reused. At minimum, the website needs prominent warnings on every page where an LLM summary appears, the prompts must be fully reproducible (not just downloadable as JSON), and a small validation table, say 10 complexes scored by a domain expert for accuracy of each claim, should be included as a supplemental figure. As it stands this section reads like an enthusiastic add-on that has not been thought through with the same care as the rest of the work.
9. Cutoffs and cluster numbers need stability analysis. The cutoff for the 75th-percentile DepMap correlation (mean of random + 3 SD = 0.147) is reasonable but should be accompanied by an FDR or precision/recall estimate against a labelled reference set. The choice of 20 final clusters in functional clustering (because that gave a peak in silhouette score) and 14 for disease clustering should also be supported by stability analysis, e.g. resampling.
10. Internal numerical consistency. The bioRxiv preprint abstract refers to 354 high-confidence multi-protein complexes, while the body of the manuscript discusses 518 (224 dimers + 294 multimers). The relationship between these numbers should be stated explicitly. Likewise, the breakdown of "60 unique to DepCom" into 41 heterodimers + 19 multimeric should be reconcilable in the figures and tables. The number "9,764 unique seed proteins" should also be clarified to confirm it is the DepCom-internal seed set and not inherited from the Zhang et al. coverage or hu.MAP 2.0 (9,963 proteins). These are easy fixes but matter for a resource paper.
11. Mander's overlap coefficient. The VSV-G(ts045)-KDELR retrograde-transport assay is well established and the experiment is clean, but MOC has been increasingly criticised in the colocalisation literature (Adler & Parmryd 2010, 2021). Best practice is to also report Manders' M1/M2 coefficients or Pearson's correlation alongside MOC. Adding these would be straightforward and would strengthen Fig 4B.

Minor comments

1. Page 4: "candidate sets of potential multi-protein complex members". Pick one, they are either candidates or potential, not both.
2. Page 7: "Complex 294... mechanistic basis for CFL1 and WDR1 cooperation has only recently been described". Please update the reference list and language given how recent this is.
3. Page 7: JTB is described as "poorly characterised". This is a bit too strong. JTB has been studied in the context of TGF-β-induced mitochondrial regulation (Kanome et al. 2007), cytokinesis and chromosomal passenger complex association (Platica et al. 2011), the structural characterisation of its extracellular domain (Rousseau et al. 2012), and breast cancer biomarker work (Jayathirtha et al. 2022). A more accurate framing would be "incompletely characterised, with previously reported but functionally unresolved roles". The novelty here is the Golgi connection, which is genuine.
4. Page 8: the citation of Blomen et al. 2015 Science for "Golgi-related synthetic lethality" should be checked against the actual supplementary data of that paper to confirm the JTB attribution is correct.
5. Figure 1: as in many omics papers, please think of us colourblind readers. The pink-green DepMap correlation scale will be hard for some of us.
6. Figure 5A and 5B: 21 and 14 colour-coded clusters respectively in a single UMAP is too much. Consider splitting into separate panels by broad theme or providing an interactive version only.
7. Page 11: "manually evaluated the quality of outputs". By whom, blinded to which model produced which output? Methods are silent on this.
8. Some figures show "hairballs" with very limited informative content. Fig. 1B left panel and the AlphaBridge wheel plots in particular convey relatively little at the size shown.
9. The reference list looks a bit thin on prior systematic complexome efforts. BioPlex 3.0 (Huttlin et al. 2021 Cell), hu.MAP 2.0 (Drew et al. 2021 MSB) and CORUM 5.0 (Tsitsiridis et al. 2024 NAR) should all be cited and discussed.
10. The discussion section drifts into general comments about AI in science that don't add much. I would cut about a third of it and use the space for a more careful framing of the actual contribution.

Significance

General assessment:

The strongest aspect of this study is the JASS complex story. The IP-MS, the SYS1-KO rescue experiment, the VSV-G(ts045)-KDELR transport assay, and the orthogonal CRISPR screens with diphtheria and Pseudomonas exotoxins together build a convincing case for JTB as a regulator of Golgi-to-ER retrograde trafficking. This part of the paper is genuinely nice work and would stand on its own. The pipeline itself, combining structural predictions with functional dependency data and filtering with AlphaBridge, is sensible and timely. It is a reasonable demonstration of how confidence filtering should be done at this kind of scale.

The main limitations concern the resource framing. After reading the manuscript several times I am still trying to identify the central novel contribution beyond the JASS validation. The interactome predictions are taken from Zhang et al., DepMap is public, AF3 is public, AlphaBridge is the authors' own previously published tool, and GO/STRING/Open Targets/dbPTM are all public. The manuscript is essentially an integrative pipeline plus a website plus one experimentally followed-up complex. The framing oversells what is genuinely new. The authors' own comparison (Fig. S3) shows 60 complexes "unique to DepCom" out of 518, of which 41 are heterodimers and only 19 are multimeric. Nineteen genuinely novel multi-protein complexes is still a contribution but it is a long way from the 354/518 that the abstract and discussion implicitly emphasise. The validation rate (one of 518) and the missing comparisons to CORUM 5.0 and hu.MAP 2.0 are the two issues that most need addressing.

Advance:

The advance is incremental rather than conceptual. The idea of intersecting co-essentiality with structural predictions is sensible but not new in spirit, and similar hybrid approaches are now becoming more common in this space (see e.g. EndoMAP.v1, Gonzalez-Lozano et al. 2025 Nature, which the authors do cite). What is new here is the specific implementation, the AlphaBridge filtering layer, and the JASS finding. The technical advance lies in the AlphaBridge filtering step on top of AF3 at a reasonably large scale. The biological advance is the JASS complex and the demonstration that JTB plays a role in Golgi-to-ER retrograde transport, which is genuinely new and well supported.

Audience:

This work will be of interest mainly to specialised audiences in structural proteomics, computational biology of protein complexes, and the protein-protein interaction community. The JASS finding will be of interest to a broader readership in cell biology, particularly those working on Golgi trafficking, ARF/ARL family GTPases, and retrograde transport. The web resource will likely find users among researchers studying specific complexes who want a quick structural hypothesis. I do not think the work, in its current form, will reach broad audiences in the way the authors hope, but a more sober framing would actually help it land better in the specialist community where it belong.

My expertise:

Mass spectrometry-based proteomics, protein-protein interaction mapping, systems biology, structural biology. I have working knowledge but not deep expertise in: structural prediction confidence metrics (AF3, AlphaBridge implementation details), DepMap CRISPR co-essentiality analysis, and Golgi cell biology. I would defer to a computational structural biology or cell biology specialist on the AF3 confidence interpretation details and on the cell biology specifics of the JASS validation.

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Referee #2

Evidence, reproducibility and clarity

The study presents DepCom as a broad resource for discovering human multi-protein complexes by integrating predicted binary interactions, DepMap co-dependency, AF3 modelling, and AlphaBridge filtering. Overall, the computational strategy is well motivated, and the experimental validation of the JTB/SYS1/ARFRP1 complex provides a compelling example of how the resource can generate testable biological hypotheses.

Major comment: scope and interpretation of DepMap-derived functional evidence

The manuscript could benefit from more clearly defining the scope of the functional evidence used to nominate complexes. The central co-dependency signal is derived from DepMap 24Q2 CRISPR gene-effect profiles, which are primarily cancer cell-line fitness/proliferation data. This is an important limitation because the resulting correlations may preferentially capture complexes or pathways that influence viability in proliferating cancer cells, while missing complexes active in differentiated, tissue-specific, stimulus-dependent, or non-proliferative contexts. Conversely, some correlations may reflect shared cancer-lineage or fitness dependencies rather than direct participation in a stable complex. The authors are appropriately cautious in stating that DepCom is not a complete inventory of human protein complexes, but the title, framing, and resource description could still be read as implying a more general catalogue of functional protein complexes. The authors might consider adding a clearer introduction to DepMap and explicitly discuss how the cancer-cell-line origin of the data affects interpretation of the 518 predicted complexes. This could be addressed without new experiments, for example by adding text early in the Results section explaining what the CRISPR gene-effect scores measure, and by expanding the Discussion to clarify that DepCom represents structurally plausible complexes prioritized by co-dependency across cancer cell lines, rather than an unbiased or context-independent map of human protein complexes. The selection of highlighted examples would also benefit from clearer justification. The peroxisome, actin, WNK/TSC22D2, and Golgi/JASS examples are biologically interesting, but the rationale for choosing them is not always explicit. Were they selected because they were novel, high-confidence, disease-associated, experimentally tractable, or representative of different resource categories? Briefly stating the selection criteria would help readers understand whether these examples are illustrative case studies or representative outcomes of the pipeline.

Minor comments

1. Clarify post-clustering removal of large/problematic protein families and complexes.

In the Methods, the authors state that "clusters of histones and keratin clusters, as well as the mito-ribosome, complexes of the electron transport chain and the mediator complex" were removed because of their large sizes. This filtering step would benefit from additional detail. Please specify the criteria used to define these removed clusters, how many clusters/proteins were removed at this stage, and whether removal was based only on size or also on biological/manual curation. It would also be helpful to explain why these proteins or clusters were removed after clustering rather than excluded before graph construction and clustering, since highly connected or compositionally biased protein families could potentially influence neighboring cluster assignments. If available, a brief robustness check showing that pre-removal of these proteins gives similar candidate complexes would strengthen confidence in the clustering procedure. 2. Clarify the rationale for excluding complexes larger than 5000 residues.

The 5000-residue cutoff is understandable for AF3 computational cost, but the manuscript should briefly state how many candidate complexes were excluded by this cutoff and whether this preferentially removes known large assemblies. This would help readers understand the scope of complexes that DepCom is expected to miss. 3. Improve wording in the CAP1/CFL1/WDR1/ACTB example.

The sentence "Additionally, CAP1 works in concert with CFL1 to accelerate depolymerisation, though if a four-protein complex consisting of actin, WDR1, CAP1 and CFL1 is relevant is not clear" is difficult to parse. Possible revision might be something like: "Additionally, CAP1 works in concert with CFL1 to accelerate depolymerisation, although it remains unclear whether actin, WDR1, CAP1 and CFL1 form a stable four-protein complex in cells." This more clearly separates known biology from the speculative interpretation of the DepCom prediction. 4. Improve reproducibility details for AF3 predictions.

The Methods state that predictions were run using a local AF3 installation, but reproducibility would be improved by reporting relevant AF3 settings, number of seeds/models per complex, whether templates were used, how disordered regions were handled, and whether predictions were repeated for all complexes or only selected examples. This is especially important because the manuscript notes that multiple predictions can yield different subunit arrangements.-

Significance

General assessment:

This study presents a timely and useful resource for prioritizing candidate human protein complexes by integrating predicted binary protein-protein interactions, DepMap co-dependency profiles, AlphaFold3 structure prediction, and AlphaBridge confidence filtering. A major strength is the combination of orthogonal evidence types: physical interaction predictions define a tractable search space, functional co-dependency helps identify coherent protein groups, and structure-confidence metrics provide an additional filter on the resulting candidates. The experimental validation of the JTB/SYS1/ARFRP1 complex is also a strong aspect of the study, as it demonstrates that the resource can generate biologically meaningful and experimentally testable hypotheses.

The main limitation is that the resource should be interpreted as a prioritized, hypothesis-generating dataset rather than a comprehensive or context-independent catalogue of human protein complexes. As noted above, the DepMap-derived signal reflects cancer cell-line fitness/proliferation dependencies, and the final complex set is also shaped by the starting interactome, filtering choices, and computational constraints on complex size. These limitations do not undermine the utility of the resource, but they should be clearly framed for readers.

One aspect that could further increase the impact and usability of the study is the DepCom web resource. The searchable table of complexes is already useful, particularly for users who want to query by gene or protein name. However, the website also presents functional and disease-based clustering, and many users may want to search or filter complexes by biological process, GO term, pathway, disease association, or disease cluster. Adding GO-term and disease-association fields to the main table, and allowing users to search/filter by these annotations, would make the resource more discoverable and useful to researchers approaching the dataset from a biological process or disease area rather than from a specific gene.

Advance:

The advance is primarily technical and resource-oriented, with an accompanying functional biological demonstration. The study helps fill a gap between large-scale binary interaction prediction and the more difficult problem of nominating higher-order assemblies. By using functional dependency profiles to prioritize multi-protein combinations before structure prediction, the authors reduce an otherwise intractable search space and generate a set of structurally plausible candidate complexes. The JASS complex and the proposed role of JTB in Golgi-to-ER retrograde trafficking provide a compelling example of biological discovery enabled by the pipeline.

The broader DepCom resource, including predicted complex structures, AlphaBridge interface-confidence information, PTM-interface mapping, functional/disease clustering, and downloadable LLM prompts, should provide useful starting points for follow-up studies. These outputs are best viewed as hypothesis-generating rather than definitive biological annotation, but they represent a valuable extension of existing protein-interaction and structure-prediction resources.

Audience:

The study will likely interest a broad basic-research audience, especially researchers in protein complex biology, structural biology, functional genomics, systems biology, cancer dependency mapping, cell biology, and computational biology. It may also be useful to investigators studying specific pathways or poorly characterized proteins, since the resource provides candidate interaction partners and structural hypotheses that can guide experiments. The translational relevance is more indirect, mainly through disease-association clustering and potential target-discovery applications, but the immediate audience is likely to be basic and computational researchers.

My expertise is in computational protein databases, protein domain classification, structural/evolutionary analysis of proteins, and functional annotation resources, including experience with the ECOD database for evolutionary classification of protein domains. I am less able to evaluate the fine details the experimental cell-biology assays beyond their general interpretation and reporting.

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Referee #1

Evidence, reproducibility and clarity

Characterising protein complexes is a fundamental goal in modern molecular cell biology. Here, Uckelmann and colleagues have presented a solution to part of this problem. By combining functional clustering with alphafold modelling, they present a high throughput bioinformatic solution. The paper and figures are exceptionally clear and well presented. The conclusions are reasonable, and the data interesting. I am a cell biologist with expertise in molecular machinery of trafficking, so the focus of my review will be on the identification of a new complex, that is proposed to have a role in retrograde trafficking. On the whole I find this a interesting and convincing finding. However I have some comments and questions that I hope may help the authors. I will naturally focus my comments on the cell biology.

1.The authors do not co-IP ARF1. This does not surprise me as small GTPases often hydrolyse their GTP during lysis. 2.There have been a number of ARF1 bioID screens done- have the authors checked if their complex has turned up here? 3.I am a bit confused by some of the interpretation about KO and loss of JTB staining. They interpret: "The SYS1 acts as a Golgi recruitment factor for both ARFRP1 and JTB". The ARFRP1 has been published and is a cytosolic protein, so that makes sense. However, the JTB is not cytosolic by a membrane protein, so cannot be "recruited". Now maybe it is retained in the Golgi by this interaction, but if that is the case you would still expect signal on another organelle or the plasma membrane (and we see it isnt degraded in the lysosome due to the western blot). I am confused by the authors model here. 4.The authors validate their JTB antibody and confirm the fact that there are not reduced SYS1 levels in the JTBKO- this is very clear (albeit unquantified). What I do not see validated is the SYS1KO. I think this is quite important. 5.The colocalisation in panel 3D is weak and unclear to me. It is not quantified. It is not clear if there have been 3 repeats. 6.The imaging in figure 3 is not clear in places, and it stands out in a very clear manuscript. I cannot see the JTB in panel F. There are no scale bars. The dynamic range of the image is not utalised. I do not see the stain in the JTB in either of the sys1 KO, i do not see the SYS1-FLAG staining in the complement, and it is not quantified at all. It may all seem trivial, but (to me) this is an absolutely critical bit of biology data to support the informatics. 7.I am a bit unconvinced by the interpretation of it being a retrograde trafficking complex. This is for 2 key reasons- 1) the VSV-G is antrograde (despite unusually they interpret a "severe defect in retrograde transport"). 2) Even if it was only having an effect in the retrograde direction I would still remain a little open minded about it as you can easily mistake trafficking of a protein in one direction for another if an unknown protein (SNARE for example) has defective trafficking.

Significance

Characterising protein complexes is a fundamental goal in modern molecular cell biology. Here, Uckelmann and colleagues have presented a solution to part of this problem. By combining functional clustering with alphafold modelling, they present a high throughput bioinformatic solution. The paper and figures are exceptionally clear and well presented. The conclusions are reasonable, and the data interesting. I am a cell biologist with expertise in molecular machinery of trafficking, so the focus of my review will be on the identification of a new complex, that is proposed to have a role in retrograde trafficking. On the whole I find this a interesting and convincing finding.

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Reply to the reviewers

Reviewer #1

Summary: This manuscript has presented a high-throughput fluorescence recovery after photobleaching (HiT-FRAP) platform to screen genes affecting the dynamics of the nucleolar scaffold nucleophosmin (NPM1). The platform included the siRNA-based screening of 65 RNA helicases, 9 phylogenetically related helicase pairs, and 290 ribosomal proteins along with selected assembly factors. These factors were classified as those accelerating or decelerating NPM1 dynamics based on the t1/2 measurements. Combined with nucleolar morphological changes, the authors identified that depletion of early-stage (A-F) and later-stage (G-H) LSU assembly factors resulted in different nucleolar phenotypes, suggesting the pre-ribosome assembly can impact nucleolar morphology. Further exploring the potential mechanis m suggested that the NPM1's intrinsically disordered region (IDR) contributed to the nucleolar organization and dynamics.

Together, this well-designed study uncovered that the ribosome assembly, both the early and late ribosomal precursors can influence biophysical properties of the nucleolus. Below please find our concerns for the authors to consider to strengthen the major conclusions.

Major comments:

The main conclusion that NPM1's biophysical states directly impact its interaction strength with ribosome intermediates (and thereby nucleolar dynamics) should be further strengthened as listed below:

1). Given the nucleolus's complexity, an additional GC factor, or/and one more marker of other nucleolar regions, should be examined to substantiate the proposed impact of LSU-associated factors on nucleolar morphology (Figures 3, 4).

We thank the reviewer for this very important point. We have now included representative images for representative hits in major phenotypic clusters co-stained for SURF6, another GC marker, which shows similar localization patterns as NPM1 (Fig. S4B). For other nucleolar subcompartments, we have included images obtained from a cell line harboring endogenously tagged FBL-mNeonGreen (a marker for the DFC) for representative hits (Fig. S4A). We see a similar overall distribution of the DFC within the GC (i.e. DFCs distribute to fill the area of the disrupted GC), confirming our screen results. We look forward to further examining the changes in nucleolar subcompartment architecture in future work.

As additional support, we note that we probed NOG2, NOP53, and NOP2 in our IF results, all of which are GC-localized factors. We see a very similar distribution for these factors in our hits as for NPM1 (see Fig. S8D). In addition, FISH data for pre-rRNA precursors show similar morphological patterns as NPM1, further confirming our results (Fig. S7). We have noted this in text and have also included representative images in supplement.

2). Additional experiments are needed to support the proposed model that ribosomal intermediates, especially the pre-LSU complexes could determine nucleolar biophysical properties through the interaction with NPM1. Their direct interaction by biochemical assays should be provided. Also, when analyzing the interaction with other nucleolar factors, the authors should provide data that show NPM1 mutant expression levels were comparable to endogenous levels (Figures 4, 6).

We agree that directly probing NPM1's interactions with LSU precursors is critical to supporting our model, and we have addressed this through several complementary biochemical approaches. First, we performed immunoprecipitation of tagged NPM1 (NPM1-mScarlet, IP-ed using RFP-trap agarose) and assessed interaction with pre-LSU rRNA transcripts via Northern blot (Fig. 5D). We find that NPM1 interacts strongly with the 32S pre-rRNA. Second, we performed sucrose gradient sedimentation and find that NPM1 preferentially co-migrates with pre-60S complexes (Fig. 5B). Together with previous reports of NPM1-pre-LSU interactions, these data provide direct biochemical support for the proposed interaction.

To test whether interaction strength with pre-LSUs could regulate NPM1 dynamics, we next asked whether our NPM1 mutants that differ in their dynamics in turn interact differentially with pre-LSU complexes. Using co-IP Northern blot for ITS2 and sucrose co-sedimentation, we find that NPM1 mA3 pulls down more 32S and co-sediments more robustly with pre-60S complexes, while NPM1 mB2 shows reduced association (Fig. 5D, E; Fig. S10F, G). These data support that the strength of the NPM1-pre-LSU interaction is a determinant of NPM1 exchange dynamics, and, by extension, of nucleolar biophysical properties.

Exogenous mutant NPM1 is expressed at approximately 10% of endogenous levels (Fig. S10A). We address this in two ways. First, all interaction comparisons are made between WT and mutant exogenous constructs, not against endogenous NPM1, controlling for expression level differences. Second, we observe similar effects on interactions both in the presence of endogenous NPM1 and in null backgrounds, indicating that the differences we detect reflect NPM1 mutation, not expression level.

3). Northern Blotting should be done to dissect which pre-rRNA intermediates interact with NPM1 and contribute to the nucleolar dynamics (Figures 4B, D, F). These additional experiments should be feasible within a reasonable timeframe.

We agree with the reviewer and have performed northern blots for major hits in our different nucleolar phenotypes, and results reinforce what we see by FISH and qPCR (Fig. S6B). Briefly, depletion of the “RNA Exosome” hit SKIV2L2 results in smearing of pre-rRNA precursors that harbor both ITS1 and ITS2 and an accumulation of the 12S, in keeping with its role in end-processing of these transcripts. For “Other” hit PHF5A, we see an enrichment for 47S/45S/41S species, consistent with an early precursor stall. Notably, we do not see this phenotype for depletion of “Other” hit CNOT1, which suggests multiple processing defects may lead to a similar nucleolar phenotype. Treatment with PolI inhibitor CX5461 shows a depletion in ITS1 containing transcripts, and minimal impact on ITS2-containing transcripts, similar to FISH results. Lastly, depletion of “LSU” hits NOP53 and RPF2 leads to accumulation of the 32S and 12S species, in keeping with accumulation of abortive pre-LSUs.

In addition, the authors should provide the code and the hardware control procedures for HiT-FRAP to ensure reproducibility.

We thank the reviewer for this thoughtful suggestion. We have made our software available on GitHub (https://github.com/jess-sheu/colony_blob_bleacher) and archived on Zenodo

(https://doi.org/10.5281/zenodo.20275447).

According to the authors' statement, all the experiments are adequately replicated, and the statistical analysis is adequate.

Minor comments:

To enhance clarity and focus, consider the following:

1). Simplifying the HiT-FRAP screening section (Fig. 1-3) would emphasize the significant findings.

We have simplified text throughout to better highlight significant findings.

2). Expanding analysis and experimental validation could help to solidify the interdependency between rRNA / ribosome precursors and the NPM1- driven nucleolar dynamics (Fig. 4-5). Indeed, additional experiments suggested above in the major concerns should be supplemented here.

We have performed additional experiments to demonstrate the interdependency between ribosomal precursors and their interaction with NPM1 in shaping nucleolar dynamics, as described above.

Reviewer #1 (Significance (Required)):

This work has established a powerful toolkit, named HiT-FRAP, to identify factors involved in the organization and regulation of the membrane-less nucleolus, which will be useful for understanding the complexity not only the nucleolus, but likely other condensates in cells in the future. Using this platform and with the Granular Component (GC)-localized NPM1 as an indicator of nucleolar morphology, the authors found that the biophysical properties of the nucleolus are sensitive to the ordered assembly of ribosomes, in particular the LSU maturation steps at the GC. This finding is important as it suggests the interdependency between the dynamic rRNA processing and the functional assembly and morphology of the nucleolus. Further studies are warranted to analyze the dynamics of other nucleolar constituents, particularly those localized at other sub-nucleolar regions, to fully depict how exactly the nucleolar function is coordinated with its biophysical properties.

Reviewer #2

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

Summary: The nucleolus is a multiphase biomolecular condensate whose primary function is ribosome biogenesis. There are mounting evidences that the material state of condensates is important for their function. Here the authors have probed how the material property of the nucleolus responds to inhibitions of ribosome biogenesis.

They have assessed nucleolar dynamics (molecular diffusivity) of a nucleolar protein, NPM1, by fluorescence recovery after photobleaching (FRAP). NPM1 is a protein that labels the periphery of the nucleolus (the so-called granular component, GC). (The nucleolus has 3 main subcompartments: the internal fibrillar centers, the middle dense fibrillar components, and the GC).

One of the main findings of the work is that inhibition of late steps of ribosome biogenesis increases fluidity (faster recovery of NPM1), while inhibition of earlier (and inhibition of mRNA processing -but see below) rather increases rigidification (slower recovery). They then attempt to correlate what is interpreted as biophysical changes to pre-ribosomal intermediates and interaction with NPM1.

Practically, the authors have produced reporter cell lines (HeLa) expressing stably (CRISPR engineering) mono or bi-allelic fluorescent version of NPM1; they have developed a powerful platform to conduct high throughout FRAP (this is really good); they have calibrated their system, initially with basic perturbations (ATP depletion, proteasome inhibition, etc), and then they focused on a family of trans-acting factors: the helicases, investigating systematically their effect on NPM1 recovery. They then extended their initial candidate-based screen to additional factors (using STRING interactions). This is nice and useful. Later in the work, they include in their analysis additional (morphological) features of nucleoli to cluster functionally their hits, as was done earlier by others in similar works. Finally, using recently published structural data (CryoEM), they attempt to correlate groups in the cluster with particular pre-ribosomal species. This part is less advanced and weaker than the initial part of the paper (screens and FRAP measurements).

Major comments:

-A major comment is with the compositional analysis of precursor intermediates that should be better defined. The stage assignment of particles is not quite as good as the screening part of the paper. At the RNA level, the authors provided FISH, as histograms of quantifications (see e.g. Fig 4D, and Fig SS6E). It would be necessary to show images, and to perform biochemistry. At the protein level, the authors provide immunostaining, but it does not really prove the detected protein is part of a particle,..

We thank the reviewer for this important critique. We have taken several steps to address both the stage assignment and biochemical characterization concerns.

Regarding stage assignment: We have consolidated our LSU phenotypic clusters (previously LSU1 and LSU2) into a single "late pre-LSU" group based on their shared features and proximity in PCA space. We want to be clear that this consolidation is intended to more accurately represent what our data can support: the screen reliably identifies factors whose perturbation produces a coherent late LSU assembly phenotype, and we do not wish to overstate the resolution of state assignment from imaging data alone. Sub-cluster distinctions are retained in supplementary materials for transparency. We have revised language throughout to reflect this framing.

Regarding biochemical characterization of intermediates: We have now performed Northern blots on strong hits within our phenotypic groups (Fig. S6B). For LSU cluster hits, we observe accumulation of the 32S and 12S species, indicating a stall in ITS2 processing, which is directly consistent with our ITS2 FISH results and confirms that the RNA-level phenotypes reflect genuine pre-rRNA processing defects rather than indirect effects. For "Other" group factor PHF5A, we observe 47/45/41S accumulation consistent with an early processing stall. We have also added representative FISH images to Fig. S7 to allow direct visual assessment of RNA-level phenotypes.

Regarding protein-level particle assignment: We agree that IF alone cannot establish that assembly factors are incorporated into discrete pre-ribosomal particles rather than existing as free factors. To more directly test whether the LSU cluster phenotypes reflect accumulation of genuine pre-ribosomal particles rather than mislocalized free factors we used NOP53 knockdown as a representative LSU cluster perturbation and, similar to RPF2 knockdown, see an accumulation of ITS2 and NOG2 in the nucleolus by FISH and IF (Fig. 4E). We then performed nuclear sucrose gradient fractionation and found that NOG2 co-migrates with the LSU peak and does not enrich in soluble fractions (Fig. 4F-H), supporting the interpretation that late pre-LSU particles accumulate in the nucleolus upon disruption of LSU cluster genes. Importantly, we also observe a strong decrease in co-sedimentation of NPM1 with the LSU peak upon depletion of NOP53 (Fig. 4G,H). This result, together with the Northern blot and FISH data, provides biochemical and cell biological evidence that the nucleolar phenotypes we identified by HiT-FRAP are associated with accumulation of late LSU assembly intermediates.

-Another concern is to know if NPM: a GC component located periphery of the condensate and a late assembly factor is an appropriate marker for assessing the effects on nucleolar material state of all (including early and late) inhibitions.

Would factors involved in earlier ribosomal assembly steps, and localized more internally would not be better tools to evaluate change in material states caused by alterations in early steps?

We appreciate this important point and agree that NPM1 reports primarily on GC dynamics. However, we would argue this is a feature rather than a limitation for two reasons.

First, the GC is the terminal assembly compartment through which pre-ribosomal particles must transit before nuclear export. Perturbations to earlier assembly steps, including FC/DFC-localized processes, likely propagate into GC dynamics, because stalled or aberrant particles accumulate in or are excluded from the GC. NPM1 FRAP thus functions as a downstream integrator of upstream assembly status, not only a reporter of GC-proximal events. This interpretation is consistent with our observation that depletion of early factors (and, therefore, depletion of downstream intermediates) do produce detectable NPM1 phenotypes in our screen. Second, the pattern of our screen results supports rather than undermines this logic: the striking enrichment of late LSU factors and near-complete absence of SSU hits is precisely what one would predict if NPM1 reports selectively on pre-LSU flux through the GC. A sensor that reported indiscriminately on all condensate perturbations would not produce this specificity.

We do acknowledge, however, that NPM1 cannot report on material state changes that are compartmentally confined to the FC or DFC and do not propagate outward. Extending this approach to internal markers remains an important future direction. To clarify the scope of our readout, we have revised the text to specify that we are monitoring GC dynamics, and we have added representative images of fibrillarin localization in Supplemental Figure S4A to illustrate the relationship between DFC and GC compartments in our experimental system.

-About the engineered cell lines used for screening by FRAP (Fig 1S): NPM1-mNeonGreen (biallelic with reduced expression of NPM1) and mScarlet (heterozygous): There is a need to characterize pre-rRNA processing in both cell lines to show they are not affected for ribosome biogenesis. This is important information since the entire work is based on these cells.

We have performed a Northern blot across the cell lines used in this paper as compared to their parent cell line and see no substantial difference in rRNA processing. We have included this data as Supplemental Figure 1D.

The screening cells are HeLa cells implying they are not physiologically regulated for p53. Nucleolar surveillance is a key regulatory surveillance loop triggered by ribosome biogenesis inhibitions leading to p53 stabilisation. How could this affect this work? Should key findings be confirmed in diploid p53 positive cells?

We acknowledge that our choice of HeLa cells limits our ability to distinguish cell-type-specific responses from more universal mechanisms and have added an explicit discussion of cell choice in the main text. To begin exploring the impact of p53, we performed gene depletions for representative hits across phenotypic clusters in untransformed, diploid hTERT-RPE cells that were lentivirally-transduced with NPM1-mScarlet and assessed nucleolar morphological phenotypes at smaller scale (Figure S6C, Supplementary Text). At baseline, RPE cells show more and smaller nucleoli than HeLa cells, which may reflect a difference in basal nucleolar assembly and, potentially, ribosome biogenesis, in keeping with previous observations that transformed cells rely more heavily on ribosome biogenesis than non-transformed.

Upon gene depletion, we found that hits from the "RNA exosome" cluster shows a different phenotype than seen in HeLa cells, where we observe less size difference and a marked decrease in eccentricity, which may reflect a p53 or cell type specific response. Depletion of the “Other” cluster gene PHF5A results in a milder though qualitatively similar phenotype as seen in HeLa cells, with nucleolar rounding and an increase in NPM1 intensity. Depletion of “LSU”-associated hits in RPE cells very robustly replicated most of the nucleolar features we observed in HeLa, which suggest that these are likely generalizable responses to LSU disruption. We have included this data in Supplementary Figure 5C. We note that we did not directly test whether p53 is stabilized upon depletion of our hits in RPE cells, and whether p53 activation feeds back on condensate dynamics remains an open area for future work. However, the concordance of LSU-associated phenotypes across HeLa and RPE cells, which differ substantially in p53 status, transformation state, and baseline nucleolar architecture, supports the generalizability of our core findings.

-About factor depletion, e.g. helicases, it's important to consider direct versus indirect effects on ribosome biogenesis, the timeline of depletion should be well described in the paper. Apparently, most factors, including the helicases were depleted for 72 hours, this is very long considering most of them play important roles in essential processes for cell homeostasis implying severely reduced growth at the time of capture (and the possibility of indirect effects).

We thank the reviewer for this important point. To directly address depletion timeline, we performed time courses for strong hits and monitored nucleolar morphology at 24 and 48 hour intervals (now included in Fig. S3D). Morphological changes begin to emerge by 48 hours across phenotypic classes; for the RPF2 LSU phenotype specifically, nucleolar expansion and decreased NPM1 intensity are detectable as early as 24 hours, inconsistent with a general stress response and more consistent with a direct downstream consequence of LSU assembly disruption. Moreover, despite all targeted genes being essential for homeostasis, phenotypic profiles are cluster-specific and associated with multiple genes of coherent function, which suggests that observed impacts are downstream of specific pathway inhibition rather than a general cellular stress response.

-Another cause of concern is that some perturbations (factor depletion) affect very deeply nucleolar structure/morphology (eg uL2 depletion shown in Fig 2C); how easy/difficult was it to control/make sure that a correct area was obliterated in the FRAP experiment using the (remarkable) data-adaptive approach. For cases where the nucleolus was deeply affected how did you check that a significant nucleolar area had been selected for analysis? It would be good to describe this in the text.

We manually ensured our segmentation protocol accurately captured nucleoli, defined by higher intensity regions of NPM1, for all depletion cases during screen development. As this is the key factor in ensuring where the bleach point is, most bleaches, even in disrupted cases, bleached the nucleolar interior. To address this point, we have included figures in the supplement (Fig. S4D) that show bleaching time courses for select highly disrupted hits uL2 and eL39.

• Fig 6C, interaction of NPM1 constructs with pre-ribosomes: the authors have tested interaction with select nucleolar proteins (NOP53, NOP2, NOG2, and uL2), which is not the same as preribosomes.

It would be important to see the interactions with precursors (Fig S9C, now histograms) please show the actual data, this was tested by qPCR, please show classical northern blots as RTqPCR have shown their limits in such applications.

Indeed, we cannot distinguish between assembly factors/ribosomal proteins that are associated with NPM1 in their latent, non-pre-LSU bound state versus those that are part of a developing ribosome. We have addressed this gap in several ways. Firstly, we have performed IP-northern blots for tagged NPM1-mutants, as suggested, and find that the mA3 mutant co-IPs more 32S than WT, while the mB2 binds less (Fig. 5D). We also performed sucrose gradient analysis of pre-ribosomal complexes and find that the mA3 mutant co-sediments more with the pre-60S peak, while mB2 co-sediments less (Fig. 5E). These findings are consistent with in vitro findings in the field that B2 mediates interactions with rRNA, while A3 occludes B2 through intramolecular interactions. Collectively with our co-IP western data, we believe the evidence strongly suggests that NPM1 mutants interact differentially with pre-LSU complexes.

-Minor comments:

-The effects of mRNA processing disruption on nucleolar dynamics could be (is most likely) very indirect (the so-called "slow hits"). The respective time course of inhibitions is important to describe.

We direct the reviewer to our response above for other phenotypes. For our "slow hit" / "Other" cluster, we also used the splicing inhibitor PladB as an orthogonal approach. Strikingly, nucleolar rounding was detectable within less than one hour of treatment, well before any general cell health effects would be expected, while dynamics changes required approximately 24 hours — suggesting that morphological and biophysical responses are kinetically separable and that the early morphological response is directly downstream of splicing inhibition. We have included a representative rounding timecourse in Fig. S8E.

Reviewer #2 (Significance (Required)):

-General assessment: strengths and limitations

Strengths: -The automated platform for high throughput FRAP\

-The authors develop a potentially interesting model where they attempt to connect rigidification/fluidity of a condensate to its function in assembly of large ribonucleoprotein complexes. -The manuscript reads very well; it has been prepared with great care (figures). Some complicated concepts are explained very well (Introduction/Discussion). Limitations: -particle stage assignment based on FISH and immunostaining only. The authors have not demonstrated that the LSU1 cluster = state F and LSU2 cluster = states G/H

-Advance: -Technological advance, high throughput FRAP, a powerful platform to interrogate macromolecular diffusivity.

-Several nucleolar screens have been conducted in the past (but at steady-state, not using FRAP), in these works textural and morphological features were used together with dimensionality reduction techniques to define functional clusters of genes that impact the homeostasis of the nucleolus. Often these references are cited but it could be useful to expand a bit on some of the earlier findings to bring the new ones in perspective. Some clusters (typically, the transcriptional cluster that disrupts the nucleolus; and the late binder ribosomal proteins) have been well identified before.

-Audience: Cell biologists, scientists involved in ribosome biogenesis research, scientists with an interest in helicases. The growing condensate community.

-Describe your expertise: ribosome biogenesis, structure-function relationships in the nucleolus, technological development in microscopy.

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

Summary: The authors use high throughput FRAP (HiT-FRAP) in arrayed genetic screens of HeLa cells expressing nucleophosmin (NPM1)-fluorescent protein variants to monitor the biophysical properties of the nucleolus in response to genetic perturbations. HiT-FRAP uses a data adaptive imaging strategy to automatically identify and photobleach fluorescently labeled organelles in living cells and acquire movies for FRAP. Quantitative analysis of FRAP curves include t1/2 and mobile fraction. NPM1 was monitored since it is an important nucleolar scaffolding protein that is thought to interact with many pre-ribosome intermediates.

The authors depleted 65 RNA helicases (+ 9 pairs) with siRNA and found that 15 of them either increased or decreased t1/2. Knockdowns were confirmed with western blotting. RNA helicase knockdowns with faster NPM1 diffusion were associated with large subunit (LSU) assembly. Most RNA helicase knockdowns with slower NPM1 diffusion were associated with early rRNA processing via the small subunit (SSU) intermediate. The authors screened an additional 290 gene depletions of many ribosomal proteins and assembly factors. With this expanded set of perturbations, they categorized nucleoli based on four morphological features in addition to t1/2 and mobile fraction. Using principal component analysis (PCA), the authors identified clusters of genes with similar effects on NPM1 dynamics and nucleolar morphology. From this secondary screen, the majority exhibited slower NPM1 dynamics. The knockdowns associated with faster NPM1 dynamics were associated with LSU assembly, similar to the helicase experiments. The authors further analyzed several mutants of NPM1 to elucidate the likely interactions between the scaffolding protein and ribosome biogenesis factors. The accumulation of early ribosomal intermediates were associated with decreases in NPM1 dynamics, and accumulation of late intermediates led to increased NPM1 dynamics. The findings established a link between the biophysical properties of the nucleolus and the stages of ribosome biogenesis.

Major comments:

• The claims are supported by experimentation.
• No additional experiments requested.
• The experiments are adequately replicated, and statistical analysis is sufficient. • Methods are very detailed, which should facilitate reproducibility. Minor comments:

• Prior studies are referenced appropriately.

• A bit more coverage of background on the nucleolar scaffolding protein, nucleophosmin (NPM1) would be helpful in the introduction, perhaps in favor of the details on ribosome biogenesis o Paragraph 2 could be shorter or placed elsewhere

We thank the reviewer for this suggestion and have now included some background on NPM1 in the introduction and have shortened paragraph 2.

• Figures

o In Figures 2 - 5: explicitly state in the figure caption what dotted lines are encircling (entire cell?)

We have now included this in the figure captions (they encircle the nucleus).

o In Figures 2 - 5: explicitly state what the mp-inferno LUT intensity in the images is quantitating (amount of NPM1?)

We have now included this in the figure captions (NPM1/mScarlet intensity).

o Figure 7: more detail in the figure caption

We have now expanded our model figure caption.

• The paper is quite dense with a lot of nice work, discussing many different genetic perturbations. It feels a bit overwhelming, and I think the biological significance gets somewhat lost in the presentation of all the data. Perhaps some of the presentation of results can be moved to the supplement in favor of a "leaner" main text. Currently, there are only figures in the supplement, but I feel that some of the text that is not central to the key conclusions can be moved to the supplement. I found myself getting a bit bogged down and having to re-read several times to catch the takeaway messages. Some of the clarifying statements that are found in the discussion section can be moved to the results section. In short, some reorganization would help with readability. One suggestion is to move the Inhibition of rRNA transcription or the RNA exosome leads to nucleolar fragmentation and/or the Perturbation of mRNA processing pathways results in slowed NPM1 dynamics and accumulation of rRNA precursors in the nucleolus to the supplement.

We thank the reviewer for this helpful suggestion. Due to this and other reviewers, we have now simplified discussion of phenotypic groups, including combining the “LSU” phenotypes into a single group and discussing LSU1/2 in the supplementary text. In addition, while we have chosen to keep the “rRNA transcription/exosome” and “Other” descriptions in the main text, they have been condensed and included in one main section with the other ribosome biogenesis phenotypes to highlight this key takeaway. Remaining discussion of phenotypes is now in supplemental text, as suggested.

Reviewer #3 (Significance (Required)):

• General Assessment: The main claim of the paper is that nucleolar phenotype (measured by morphology and NPM1 diffusivity) is correlated with stages in ribosome assembly - i.e. the stage of ribosome assembly determines the biophysical properties of the nucleolus. A strength of the study is the wide range of genetic perturbations tested enabled by the high throughput FRAP. With FRAP, I do worry a bit about using t1/2 as the sole dynamic measurement, but it is not a deal breaker. The authors introduce morphology as another way to characterize the nucleoli. • The claims are well supported by extensive experiments and data. The experiments are well designed, and proper controls were conducted. To validate the method, the authors used perturbations of NPM1 dynamics from the literature including ATP depletion, blocking glycolysis and oxidative phosphorylation, inhibition with MG132, and treatment with sodium arsenite. They observed slower NPM1 diffusivity under all validation conditions. • Advance: The authors have introduced a high-throughput technique for extracting diffusivity with FRAP, yielding a lot of data, but I think the paper suffers a bit in trying to present so much data in the main text. The mechanistic biological insights are compelling but get a bit overshadowed. Improved organization can help the messages come across more clearly. • To my knowledge, there is not a similar study in the literature as the detailed mechanisms of ribosome biogenesis are not well studied. • Audience: The audience for this manuscript seems to be biophysical researchers, thought there may be broader interest due to the wide screening of genetic perturbations. • Expertise: I have evaluated this manuscript from the perspective of a single-molecule biophysicist that studies protein-protein interactions between ribosome biogenesis factors. I am not an expert in FRAP, but I use FCS.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors use high throughput FRAP (HiT-FRAP) in arrayed genetic screens of HeLa cells expressing nucleophosmin (NPM1)-fluorescent protein variants to monitor the biophysical properties of the nucleolus in response to genetic perturbations. HiT-FRAP uses a data adaptive imaging strategy to automatically identify and photobleach fluorescently labeled organelles in living cells and acquire movies for FRAP. Quantitative analysis of FRAP curves include t1/2 and mobile fraction. NPM1 was monitored since it is an important nucleolar scaffolding protein that is thought to interact with many pre-ribosome intermediates.

The authors depleted 65 RNA helicases (+ 9 pairs) with siRNA and found that 15 of them either increased or decreased t1/2. Knockdowns were confirmed with western blotting. RNA helicase knockdowns with faster NPM1 diffusion were associated with large subunit (LSU) assembly. Most RNA helicase knockdowns with slower NPM1 diffusion were associated with early rRNA processing via the small subunit (SSU) intermediate. The authors screened an additional 290 gene depletions of many ribosomal proteins and assembly factors. With this expanded set of perturbations, they categorized nucleoli based on four morphological features in addition to t1/2 and mobile fraction. Using principal component analysis (PCA), the authors identified clusters of genes with similar effects on NPM1 dynamics and nucleolar morphology. From this secondary screen, the majority exhibited slower NPM1 dynamics. The knockdowns associated with faster NPM1 dynamics were associated with LSU assembly, similar to the helicase experiments. The authors further analyzed several mutants of NPM1 to elucidate the likely interactions between the scaffolding protein and ribosome biogenesis factors. The accumulation of early ribosomal intermediates were associated with decreases in NPM1 dynamics, and accumulation of late intermediates led to increased NPM1 dynamics. The findings established a link between the biophysical properties of the nucleolus and the stages of ribosome biogenesis.

Major comments:

• The claims are supported by experimentation.
• No additional experiments requested.
• The experiments are adequately replicated, and statistical analysis is sufficient.
• Methods are very detailed, which should facilitate reproducibility.

Minor comments:

• Prior studies are referenced appropriately.
• A bit more coverage of background on the nucleolar scaffolding protein, nucleophosmin (NPM1) would be helpful in the introduction, perhaps in favor of the details on ribosome biogenesis
• Paragraph 2 could be shorter or placed elsewhere
• Figures
  • In Figures 2 - 5: explicitly state in the figure caption what dotted lines are encircling (entire cell?)
  • In Figures 2 - 5: explicitly state what the mp-inferno LUT intensity in the images is quantitating (amount of NPM1?)
  • Figure 7: more detail in the figure caption
• The paper is quite dense with a lot of nice work, discussing many different genetic perturbations. It feels a bit overwhelming, and I think the biological significance gets somewhat lost in the presentation of all the data. Perhaps some of the presentation of results can be moved to the supplement in favor of a "leaner" main text. Currently, there are only figures in the supplement, but I feel that some of the text that is not central to the key conclusions can be moved to the supplement. I found myself getting a bit bogged down and having to re-read several times to catch the takeaway messages. Some of the clarifying statements that are found in the discussion section can be moved to the results section. In short, some reorganization would help with readability. One suggestion is to move the Inhibition of rRNA transcription or the RNA exosome leads to nucleolar fragmentation and/or the Perturbation of mRNA processing pathways results in slowed NPM1 dynamics and accumulation of rRNA precursors in the nucleolus to the supplement.

Significance

• General Assessment: The main claim of the paper is that nucleolar phenotype (measured by morphology and NPM1 diffusivity) is correlated with stages in ribosome assembly - i.e. the stage of ribosome assembly determines the biophysical properties of the nucleolus. A strength of the study is the wide range of genetic perturbations tested enabled by the high throughput FRAP. With FRAP, I do worry a bit about using t1/2 as the sole dynamic measurement, but it is not a deal breaker. The authors introduce morphology as another way to characterize the nucleoli.
• The claims are well supported by extensive experiments and data. The experiments are well designed, and proper controls were conducted. To validate the method, the authors used perturbations of NPM1 dynamics from the literature including ATP depletion, blocking glycolysis and oxidative phosphorylation, inhibition with MG132, and treatment with sodium arsenite. They observed slower NPM1 diffusivity under all validation conditions.
• Advance: The authors have introduced a high-throughput technique for extracting diffusivity with FRAP, yielding a lot of data, but I think the paper suffers a bit in trying to present so much data in the main text. The mechanistic biological insights are compelling but get a bit overshadowed. Improved organization can help the messages come across more clearly.
• To my knowledge, there is not a similar study in the literature as the detailed mechanisms of ribosome biogenesis are not well studied.
• Audience: The audience for this manuscript seems to be biophysical researchers, thought there may be broader interest due to the wide screening of genetic perturbations.
• Expertise: I have evaluated this manuscript from the perspective of a single-molecule biophysicist that studies protein-protein interactions between ribosome biogenesis factors. I am not an expert in FRAP, but I use FCS.

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

The nucleolus is a multiphase biomolecular condensate whose primary function is ribosome biogenesis. There are mounting evidences that the material state of condensates is important for their function. Here the authors have probed how the material property of the nucleolus responds to inhibitions of ribosome biogenesis. They have assessed nucleolar dynamics (molecular diffusivity) of a nucleolar protein, NPM1, by fluorescence recovery after photobleaching (FRAP). NPM1 is a protein that labels the periphery of the nucleolus (the so-called granular component, GC). (The nucleolus has 3 main subcompartments: the internal fibrillar centers, the middle dense fibrillar components, and the GC).

One of the main findings of the work is that inhibition of late steps of ribosome biogenesis increases fluidity (faster recovery of NPM1), while inhibition of earlier (and inhibition of mRNA processing -but see below) rather increases rigidification (slower recovery). They then attempt to correlate what is interpreted as biophysical changes to pre-ribosomal intermediates and interaction with NPM1. Practically, the authors have produced reporter cell lines (HeLa) expressing stably (CRISPR engineering) mono or bi-allelic fluorescent version of NPM1; they have developed a powerful platform to conduct high throughout FRAP (this is really good); they have calibrated their system, initially with basic perturbations (ATP depletion, proteasome inhibition, etc), and then they focused on a family of trans-acting factors: the helicases, investigating systematically their effect on NPM1 recovery. They then extended their initial candidate-based screen to additional factors (using STRING interactions). This is nice and useful. Later in the work, they include in their analysis additional (morphological) features of nucleoli to cluster functionally their hits, as was done earlier by others in similar works. Finally, using recently published structural data (CryoEM), they attempt to correlate groups in the cluster with particular pre-ribosomal species. This part is less advanced and weaker than the initial part of the paper (screens and FRAP measurements).

Major comments:

• A major comment is with the compositional analysis of precursor intermediates that should be better defined. The stage assignment of particles is not quite as good as the screening part of the paper.

At the RNA level, the authors provided FISH, as histograms of quantifications (see e.g. Fig 4D, and Fig SS6E). It would be necessary to show images, and to perform biochemistry. At the protein level, the authors provide immunostaining, but it does not really prove the detected protein is part of a particle,.. - Another concern is to know if NPM: a GC component located periphery of the condensate and a late assembly factor is an appropriate marker for assessing the effects on nucleolar material state of all (including early and late) inhibitions. Would factors involved in earlier ribosomal assembly steps, and localized more internally would not be better tools to evaluate change in material states caused by alterations in early steps? - About the engineered cell lines used for screening by FRAP (Fig 1S): NPM1-mNeonGreen (biallelic with reduced expression of NPM1) and mScarlet (heterozygous): There is a need to characterize pre-rRNA processing in both cell lines to show they are not affected for ribosome biogenesis. This is important information since the entire work is based on these cells. The screening cells are HeLa cells implying they are not physiologically regulated for p53. Nucleolar surveillance is a key regulatory surveillance loop triggered by ribosome biogenesis inhibitions leading to p53 stabilisation. How could this affect this work? Should key findings be confirmed in diploid p53 positive cells? - About factor depletion, e.g. helicases, it's important to consider direct versus indirect effects on ribosome biogenesis, the timeline of depletion should be well described in the paper. Apparently, most factors, including the helicases were depleted for 72 hours, this is very long considering most of them play important roles in essential processes for cell homeostasis implying severely reduced growth at the time of capture (and the possibility of indirect effects). - Another cause of concern is that some perturbations (factor depletion) affect very deeply nucleolar structure/morphology (eg uL2 depletion shown in Fig 2C); how easy/difficult was it to control/make sure that a correct area was obliterated in the FRAP experiment using the (remarkable) data-adaptive approach. For cases where the nucleolus was deeply affected how did you check that a significant nucleolar area had been selected for analysis? It would be good to describe this in the text. - Fig 6C, interaction of NPM1 constructs with pre-ribosomes: the authors have tested interaction with select nucleolar proteins (NOP53, NOP2, NOG2, and uL2), which is not the same as preribosomes. It would be important to see the interactions with precursors (Fig S9C, now histograms) please show the actual data, this was tested by qPCR, please show classical northern blots as RTqPCR have shown their limits in such applications.

Minor comments:

• The effects of mRNA processing disruption on nucleolar dynamics could be (is most likely) very indirect (the so-called "slow hits"). The respective time course of inhibitions is important to describe.

Significance

General assessment: strengths and limitations

Strengths:

• The automated platform for high throughput FRAP
• The authors develop a potentially interesting model where they attempt to connect rigidification/fluidity of a condensate to its function in assembly of large ribonucleoprotein complexes.
• The manuscript reads very well; it has been prepared with great care (figures). Some complicated concepts are explained very well (Introduction/Discussion).

Limitations:

• particle stage assignment based on FISH and immunostaining only. The authors have not demonstrated that the LSU1 cluster = state F and LSU2 cluster = states G/H

Advance:

• Technological advance, high throughput FRAP, a powerful platform to interrogate macromolecular diffusivity.
• Several nucleolar screens have been conducted in the past (but at steady-state, not using FRAP), in these works textural and morphological features were used together with dimensionality reduction techniques to define functional clusters of genes that impact the homeostasis of the nucleolus. Often these references are cited but it could be useful to expand a bit on some of the earlier findings to bring the new ones in perspective. Some clusters (typically, the transcriptional cluster that disrupts the nucleolus; and the late binder ribosomal proteins) have been well identified before.

Audience: Cell biologists, scientists involved in ribosome biogenesis research, scientists with an interest in helicases. The growing condensate community.

Describe your expertise: ribosome biogenesis, structure-function relationships in the nucleolus, technological development in microscopy.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This manuscript has presented a high-throughput fluorescence recovery after photobleaching (HiT-FRAP) platform to screen genes affecting the dynamics of the nucleolar scaffold nucleophosmin (NPM1). The platform included the siRNA-based screening of 65 RNA helicases, 9 phylogenetically related helicase pairs, and 290 ribosomal proteins along with selected assembly factors. These factors were classified as those accelerating or decelerating NPM1 dynamics based on the t1/2 measurements. Combined with nucleolar morphological changes, the authors identified that depletion of early-stage (A-F) and later-stage (G-H) LSU assembly factors resulted in different nucleolar phenotypes, suggesting the pre-ribosome assembly can impact nucleolar morphology. Further exploring the potential mechanism suggested that the NPM1's intrinsically disordered region (IDR) contributed to the nucleolar organization and dynamics.

Together, this well-designed study uncovered that the ribosome assembly, both the early and late ribosomal precursors can influence biophysical properties of the nucleolus. Below please find our concerns for the authors to consider to strengthen the major conclusions.

Major comments:

The main conclusion that NPM1's biophysical states directly impact its interaction strength with ribosome intermediates (and thereby nucleolar dynamics) should be further strengthened as listed below:

1. Given the nucleolus's complexity, an additional GC factor, or/and one more marker of other nucleolar regions, should be examined to substantiate the proposed impact of LSU-associated factors on nucleolar morphology (Figures 3, 4).
2. Additional experiments are needed to support the proposed model that ribosomal intermediates, especially the pre-LSU complexes could determine nucleolar biophysical properties through the interaction with NPM1. Their direct interaction by biochemical assays should be provided. Also, when analyzing the interaction with other nucleolar factors, the authors should provide data that show NPM1 mutant expression levels were comparable to endogenous levels (Figures 4, 6).
3. Northern Blotting should be done to dissect which pre-rRNA intermediates interact with NPM1 and contribute to the nucleolar dynamics (Figures 4B, D, F). These additional experiments should be feasible within a reasonable timeframe. In addition, the authors should provide the code and the hardware control procedures for HiT-FRAP to ensure reproducibility. According to the authors' statement, all the experiments are adequately replicated, and the statistical analysis is adequate.

Minor comments:

To enhance clarity and focus, consider the following:

1. Simplifying the HiT-FRAP screening section (Fig. 1-3) would emphasize the significant findings.
2. Expanding analysis and experimental validation could help to solidify the interdependency between rRNA / ribosome precursors and the NPM1- driven nucleolar dynamics (Fig. 4-5). Indeed, additional experiments suggested above in the major concerns should be supplemented here.

Significance

This work has established a powerful toolkit, named HiT-FRAP, to identify factors involved in the organization and regulation of the membrane-less nucleolus, which will be useful for understanding the complexity not only the nucleolus, but likely other condensates in cells in the future. Using this platform and with the Granular Component (GC)-localized NPM1 as an indicator of nucleolar morphology, the authors found that the biophysical properties of the nucleolus are sensitive to the ordered assembly of ribosomes, in particular the LSU maturation steps at the GC. This finding is important as it suggests the interdependency between the dynamic rRNA processing and the functional assembly and morphology of the nucleolus. Further studies are warranted to analyze the dynamics of other nucleolar constituents, particularly those localized at other sub-nucleolar regions, to fully depict how exactly the nucleolar function is coordinated with its biophysical properties.

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Referee #4

Evidence, reproducibility and clarity

RNAi is remarkably efficient in planaria, yet no mechanism for the amplification of the RNAi signal has thus far been observed. In this manuscript, the authors analyse the mechanisms of RNAi spread in planaria. Starting from some basic observations on the identity of the Dicer and Argonaute proteins required for RNAi, the authors performed a set of elegant experiments to conclude that cycling stem cells likely take up dsRNA and excrete Ago-siRNA complexes, which are then taken up by other cells to mediate RNAi. In addition, the authors provide compelling evidence that RNAi is indeed independent of an amplification mechanism.

Overall, I found the experiments and results compelling and the manuscript a pleasure to read. I have only a few suggestions for consideration, none of which are essential to support the main conclusions:

• What does the arrest of stem cell proliferation do to the expression of RNAi genes (with and without dsRNA stimulation)?
• Page 9: top panel. Is there a control that the dsRNA generated by RNaseIII is functional? I.e. that the defect is indeed due to an uptake effect and not the quality of the siRNA preparation itself? (In our hands silencing of siRNA prepared with bacterial RNaseIII has not been efficient at all). As a side note: no method is provided for the RNaseIII treatment.
• Have the authors analyzed which of the Argonautes are present in the preparations generated with Q-sepharose?

Data presentation:

• For all figure legends: please make sure to state animals, number of repeats, define boxplots and what the individual data points represent. Please provide statistics where quantitative statements are made.

Minor points:

• First paragraph results: The statement that Ago1 and 3 were "closer to the nematode-specific WAGOs" does not seem correct, (horizontal distance to the miRNA-AGOs is still lower than the the WAGOs). I suggest removing the statement.
• Use of checkmarks: please define when a checkmark vs cross was indicated? E.g., does a checkmark indicate that 100% of the animals showed efficient RNAi, or a majority of animals?
• Many of the legends contain conclusions. While this may be a matter of taste/style, I would suggest to introduce conclusions only sparingly, if at all, in the legends
• Some of the font sizes are rather small on print size (e.g. Fig 1A, S4i). In Fig 1A the black font on dark blue background is hard to distinguish.

Textual suggestion:

• Abstract "that rely on dsRNA intermediates, such as viruses" > ".. such as those from viruses..."
• Materials and Methods: The lowerscript numbers for the ion show as squares in my pdf.

Significance

Strength/weaknesses:

I found the experimental support robust and well supported and I did not find weaknesses that jeopardize the conclusions.

Significance:

One of the most intriguing features of RNAi is the systemic spread of a silencing signal across an organism's body. This has received significant attention in C. elegans and plants, but for other organisms, this is much less well explored. Planaria have a very efficient RNAi response, which the authors propose is due to uptake of an initial dsRNA by stem cell and excretion of an Argonaute-siRNA complex, which is then taken up by distal cells in an endocytic mechanism. I find this an intriguing mechanism that to differ from mechanisms for RNAi spread observed in other organisms.

The work will be of interest to those interested in small RNA pathways (and RNA biology in general) and has practical implications for scientists working on planaria. The fact that small RNAs spread in an Argonaute-siRNA complex in an organism should also be of interest for cell biologists.

My field of expertise: Small RNA pathways and antiviral defense in insects. No experience working with planaria.

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Referee #3

Evidence, reproducibility and clarity

In RNA interference (RNAi), double-stranded RNA (dsRNA) is processed into small interfering RNAs (siRNAs), which can function locally or act as mobile RNA species that spread between cells. In organisms such as nematodes and plants, the underlying mechanisms and key factors involved in this process, including transporters such as SID-1, have been well characterized. While systemic RNAi has also been reported in other animals, the underlying mechanisms remain largely unclear. In this context, the authors focus on planarians as one such model to investigate these processes. In the planarian S. mediterranea, gene knockdown by dsRNA injection is commonly employed, and the RNAi effect is known to spread rapidly throughout the organism. However, given the absence of RNA-dependent RNA polymerase (RdRP), the mechanism by which RNAi signals are efficiently propagated remains unclear. In this study, the authors provide several important insights into this question.

First, the authors carefully evaluated the duration of the RNAi effect. In addition, they systematically examined the involvement of known RNAi-related factors and demonstrated that this process depends on ago1 and ago3. Second, interestingly, the authors find that initiation of systemic RNAi depends on neoblasts. Third, Argonaute-siRNA complexes play a crucial role in systemic RNAi. This differs markedly from the nematode system, in which dsRNA itself is transported, highlighting an intriguing mechanistic distinction. Finally, the authors suggest that distinct Argonaute proteins may function at different stages of RNAi propagation. Ago1 + Ago3 play essential roles in the initial phase of systemic RNAi in neoblast, Ago3 but not Ago1 silences the target in the differentiated cells. While the phenomenon described here is highly interesting, the underlying mechanism remains to be fully elucidated. In particular, how different Argonaute proteins functionally coordinate with each other, especially with respect to the transfer of siRNAs between Argonaute complexes, is still unclear and represents an important direction for future studies.

The study is supported by well-designed control experiments, and the results are consistent with and support the authors' conclusions.

I have no major concerns about this manuscript. The study is well conducted, and I only have minor comments that could further improve the manuscript.

(Minor) While the authors have examined the effects of irradiation on the donor, it would be interesting to test the reciprocal experiment in which the recipient is irradiated. In particular, assessing whether the addition of donor lysate to irradiated recipients can recapitulate the observed RNAi propagation would further strengthen the proposed model.

(Minor) The purity of the AGO complexes obtained via the TraPR anion-exchange procedure is not entirely clear. The authors may consider providing additional evidence of purity (e.g., visualization of small RNAs with T4-PNK), which would strengthen the conclusions.

(Minor) Figure 4H is not referred to in the main text. The authors may consider incorporating a description of this panel into the Results section for clarity.

Significance

Overall, given the substantial amount of data and the overall high quality of the present study, further mechanistic dissection would likely be beyond the scope of the current manuscript. I look forward to future work from the authors addressing these mechanistic questions in more detail. RNAi has been widely used in stem cell research in planarians. In light of the findings presented in this study, however, previous studies that combine UV irradiation and RNAi may warrant careful re-evaluation. In this regard, the present work has important implications and is likely to have a broad impact on the field.

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Referee #2

Evidence, reproducibility and clarity

In this paper, the authors set out to understand how dsRNA elicits a system-wide RNAi effect using planarians as a model system. This is an important question, because it gets at evolution of these processes in different animal models and because knowing more about how RNAi works can allow scientists to tweak their approach for a better knock down efficiency. Importantly, though the system-wide mechanism of RNAi is fairly well understood in C. elegans and in some plants, it isn't clear how conserved these mechanisms are. Some aspects of this paper are quite convincing, including identification of the responsible Argonaute and Dicer proteins. Further, the identification of potential Sid-1 homologs that may allow for import of dsRNA is new. However, the role for Ago-3 was recently reported in Sasidharan, et al (Science Advances, 2026), which is not cited in this manuscript. Perhaps more importantly, several key aspects of the argument set up in this paper are not adequately supported and there are key gaps in the mechanism proposed that prevent its publication in this form. Major and minor suggestions follow:

Major issues:

1. The argument that siRNAs must be generated in stem cells that are cycling is not well supported.

a. The authors only use one approach to reduce stem cell numbers, lethal irradiation. In addition to causing loss of stem cells, lethal irradiation causes wide-spread DNA damage and organismal/cellular stress responses. By 6 days after lethal irradiation, other progenitor cells are lost as well. Epidermal progenitors are known to be very abundant and to play signaling and/or metabolic roles in planarian physiology, so their loss may also be impactful. The authors should consider other orthogonal approaches to eliminate stem cells and to rule out other potential mechanisms.

b. The authors use camptothecin in planarians and claim that it reduces cell divisions of stem cells. To my knowledge, this drug has not been shown to work in planarians before. The concentration used is also higher than in published studies. The authors should show whether stem cells are lost after this drug treatment (through levels of stem cell markers or stem cell counting) and should clarify the timing of the treatment relative to the RNAi, which is not clear from the figure legend or methods section. The authors should also discuss possible alternative interpretations of this piece of data (e.g. potential off-target effects). Without more information, it is hard to interpret the data relative to the irradiation results. The authors also do not provide any insight into how or why dividing/cycling stem cells would be important for the systemic RNAi mechanism they propose.

c. ago-1, ago-3, and dcr-2 were shown to be enriched in stem cells (Fig. 3C), but these genes are also expressed in differentiated cells in single-cell sequencing data. Therefore, it isn't intuitive that non-stem cells would lack the capacity to generate siRNAs.

d. Is there a way to directly test the hypothesis that stem cells are only generated in stem cells, potentially by blocking transport in some way and then visualizing new siRNAs with a miRNA/siRNA version of ISH OR FACS and sequencing? If the Ago-1/3-siRNA complexes are indeed transported by EVs as per Sasidharan, et al then the ESCRT(RNAi) approach might be useful in blocking movement of siRNAs? Or, could the authors show that dsRNAs are preferentially taken up by stem cells using the type of experiment shown in Fig. S5H? 2. It isn't clear from the manuscript how the authors believe that Ago-1/3-siRNA complexes exit and enter cells. The diagram in Fig. 5F describes the complex as moving between cells either through vesicles or extracellularly. How do the authors propose that Ago-siRNA complexes pass through the plasma membrane given that they are not known to go through the secretory pathway? Or once endocytosed, how do they exit the vesicle? Uncertainty on these points makes the molecular mechanism proposed here seem poorly supported by the data provided in the paper. 3. One key result in the paper is the transplant of "AGO complexes" that are purified from lysate. The authors writing about this experiment implies that they are transplanting a fairly pure material representing these RNPs and no others. However, the approach described is unlikely to result in purification of highly specific protein complexes. At a minimum, gels that illustrate protein/complex purity should be provided. Preferably, though, mass spectrometry and sequencing would be provided to detail siRNAs and proteins in this sample. 4. The Sasidharan, et al (Science Advances, 2026) paper should be cited and also the findings of this paper should be put in the context of that work.

Minor changes:

1. In several experiments, quantitative assessment of impacts (e.g. eye size or ovo/opsin transcript levels) rather than subjective eye scoring would be preferable for rigor and for statistical analysis of changes rather than check/X (e.g. 4F-H).
2. F1 and F2 terminology for regenerates is probably not accurate since F in those terms stands for "filial" and is used to denote offspring.
3. The images in Figure 2 (A, C) are quite hard to see on the printed page. Using white for fluorescence might improve contrast and visibility.
4. The element of time seems to be very important for transmission of the RNAi effect in sexual offspring. Instead of the claim that hatchlings from RNAi crosses have no effect (Fig. 2H), the detail provided in the results section seems to indicate that there is a time-limited effect. These findings should be clarified with progeny sorted by time of egg laying and with a better sense of time between RNAi injection and hatch. Further, even in animals that do regenerate eyes, it would be nice to see a quantification of transcript as a clearer readout of whether some knockdown persists.
5. This is more of a curiosity question, but it would be interesting to know how the differences in Ago1/2/3 protein structure might relate to their function, particularly in terms of the PAZ and MID domains.

Significance

This paper provides some new insight into mechanisms underlying systemic RNAi in planarians. Some of the results are quite preliminary and the overall interpretation of data is not yet well founded. However, there are some highlights, including the potential identification of dsRNA transporters that will be interesting to those in the planarian field.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors characterized the molecular mechanism of systemic RNAi in planarian Schmidtea mediterranea (Sme) through loss-of-function genetic perturbations. They genetically identified key protein factors involved in the siRNA pathway and assessed the systemic RNAi efficacy at the molecular level. Notably, they find that the proliferating stem cells (neoblasts) are specifically required for systemic RNAi in Sme. They further propose that the requirement of neoblasts in systemic RNAi is mediated by spreading of the RISC RNP to differentiated cells.

Major Comments

1. The authors show that in Sme systemic RNAi strictly relies on the presence of neoblasts, which is one of the most interesting finding. It is important to understand the mechanism, specifically whether neoblasts are generally required for dsRNA processing or for conferring mRNA slicing activity. Although the authors claimed in Figure 5 that neoblasts are required for siRNA biogenesis, the results provided do not directly support this claim. An alternative scenario is that dsRNA can still be processed into siRNA in the absence of neoblasts, but the resulting siRNA subsequently fails to function without the neoblast AGOs or other signals. To directly confirm that neoblasts are required for dsRNA processing, one additional experiment should be performed in which irradiated worms are injected with dsRNA, followed by small RNA cloning and sequencing to detect whether processed siRNAs are present.
2. An alternative mechanism to interpret the role of neoblasts is that, instead of processing dsRNA and/or spreading RISC RNP, the neoblasts may function as regulatory cells that provide signals licensing the dsRNA processing and target slicing in differentiated cells. Under this scenario, the requirement for sid-1 and vha-16 could instead be interpreted as necessitate the dsRNA transfer from the initial uptake tissues (parenchyma for be injection or intestine for feeding) to the target tissues. To rule out this possibility, isolated neoblasts from naive donors could be transplanted into irradiated recipient worms who have been injected with dsRNA, and whether such transplantation can restore the systemic RNAi in the recipient animals could then be tested phenotypically. One caveat is that any positive result may be due to the proliferation of the donor neoblasts in the recipient. This can be addressed by performing the same transplantation but using neoblasts isolated from camptothecin-treated worms, which would limit the proliferative contribution.
3. In Figure 5E, the authors show that recipient ago-3 is required for systemic RNAi, and they suggest in the Discussion a plausible model in which recipient AGO-3 is required for nuclear RNAi for transcriptional target repression. However, this result appears inconsistent with the results in Figure 1C-D, where ago-3 KD did not abolish systemic RNAi. This contradiction should be acknowledged in text and further investigated. One possible interpretation is that the presence of the neoblast ago-3 from the donor lysate may have an antimorphic effect and interferes with the recipient AGO(s) (presumably ago-1 in this case) during target silencing , implying that homogeneity of AGO(s), or at least homogeneity of ago-1, is required for such systemic RNAi. Although the underlying mechanism remains difficult to interpret, such hypothesis could be tested by injecting lysate from ago-3 KD donor into ago-3 KD recipient. If AGO homogeneity is indeed required, such transfer treatment should no longer abolish systemic RNAi in the recipient in Figure 5D. Additionally, the target genes used for the systemic RNAi in Figure 1C/D and Figure 5E are different. To exclude the possibility that this discrepancy is target-specific, either six1/2 should be tested in the whole worm RNAi assay in Figure 1 or opsin should be used in the transfer assay in Figure 5.
4. The authors claim in Figure 4 that the systemic RNAi is mediated by secreted RISC. This claim is not unexpected, because naked siRNA generally suffers poor half-life in vivo and therefore must be stabilized by bounding to AGO to evade the endogenous ribonucleases. Nevertheless, the alternative hypothesis that the transferred RNAi is mediated by the spread of naked RNA, though unlikely, should be experimentally excluded. Specifically, the isolated RNA and lysate with protease in Figure 4F (which failed to induce RNAi in the host worm) should be tested to confirm whether they contain siRNAs. This can be done by cloning and sequencing the sRNA in the lysate.
5. The authors assigned ago-1 and ago-3 to the siRNA pathway and ago-2 to the miRNA pathway. This is an important conclusion for subsequent sRNA studies in planarians. However, the evidence provided in the current manuscript is insufficient to exclude ago-2 from the siRNA pathway, especially given that DDH catalytic triad is present in AGO-2. The observed redundancy between ago-1 and ago-3 to maintain functional RNAi can only support the involvement of these two AGO genes in the siRNA pathway but does not exclude AGO-2. To more rigorously test whether ago-2 should be excluded from the siRNA pathway, double RNAi of ago-2 and ago-1, as well as of ago-2 and ago-3, should be performed, and ago-2 should only be excluded from the siRNA-pathway if such double KD do not further reduce the RNAi efficacy compared with individual KD.
6. The results shown in Figure 1F, where exposure to exogenous dsRNA can enhance the endogenous transcription of ago-1 and ago-3 in Sme, are particularly interesting. The authors should discuss whether this phenomenon is related to nuclear RNAi. In addition, it has been reported that exposure to exogenous dsRNA can increase the AGO/DICER protein levels without increasing the mRNA level (PMID32194567), and this should be compared with the present findings. Importantly, the result also suggests a potential strategy to improve the Sme RNAi efficiency. Accordingly, it would be valuable to test whether the increased ago-1/3 transcript levels caused by introducing exogenous dsRNA can lead to higher RNAi efficacy, both in terms of target silencing depth and the duration of RNAi effectiveness.
7. Figure 2I-J provides remarkable evidence that the systemic RNAi in Sme is independent of RdRP. This result should be highlighted in the final paragraphs of the Introduction and mentioned in the Abstract.

Minor Comments:

1. The authors show that ago-1 + ago-3 KD only slightly perturbed the miRNA levels. However, this observation can be interpreted in at least two ways: (a) these two AGO genes are not involved in the miRNA pathway; or (b) these two genes are expressed at low abundance (which was mentioned later in the paper), such that their KD only mildly perturb their associated miRNAs, especially if these miRNAs are also associated with AGO-2. Scenario (a) seems less likely to be true because ago-2 is enriched in neoblasts (Figure 3C), whereas many conserved miRNAs have been reported to be enriched in Xins in Sme (Sasidharan et al 2013). This issue should be therefore discussed. In addition, the gene expression levels of the three ago genes from previously published bulk RNAseq datasets should be included in the figure.
2. The illustration in Figure 1A is not fully accurate. In the miRNA pathway, target repression also includes mRNA degradation (which is conventionally referred to as mRNA decay or mRNA destabilization), which is in fact the dominant mode of miRNA-mediated repression. Therefore, "mRNA decay" should be added in addition to "translational inhibition". In the siRNA pathway, mRNA degradation is not directly mediated by RISC itself, but by the downstream exonucleases (i.e., XRN-1); therefore, the term "mRNA slicing" should be used instead for the siRNA part. Additionally, it has been shown that C. elegans RDE-1 is also associated with miRNAs (PMID 36790166), so the functional assignment in the model should be adjusted accordingly.
3. In Figure S1C, the authors claimed that ago-1 and ago-3 exhibit more divergent PAZ and MID domains according to the AF modeling. However, this divergence may simply reflect the lower sequence conservation of AGO-1 and AGO-3 relative to AGO-2, which is shown in the phylogeny in Figure S1A. To address this caveat, Robetta modeling should be performed for both the full-length proteins in the comparative modeling mode due to the length of AGO proteins, or de novo modeling of the PAZ and MID domain. Structural the alignment in reference to solved AGO structures such as 4W5Q or 6N4O should be shown. If the MID/PAZ domains divergency remains evident, it should be quantified using backbone RMSD relative to known AGO structures.
4. In Figure S1C, a second structural view should also be included to better illustrate the AGO architecture. The duplex channel within the PIWI-MID lobe should be clearly visible in one of the views. The L2 domain, or at least helix-7, should be labeled. If possible, the relative position of helix-7 to the guide RNA should also be shown. All the predicted structural models should be included in the supplemental files.
5. The authors suggest that the spread of functional RISC from neoblasts depends on EVs. The evidence involving vha-16 is convincing, but to directly validate the presence of EVs that cargo RISC, CsCl ultracentrifugation would be informative. Although this experiment is beyond the scope of the current manuscript, the need for direct EV validation should be discussed.
6. In Figure 2G, the authors show that although zfp-1 restores the homeostatic mRNA level at week 5, its downstream target prog-1 and agat-3 fail to recover. It remains unclear whether this is due to the delay of newly translated zfp-1 to activate the downstream targets, or due to translational suppression of zfp-1. Therefore, the mRNA levels of prog-1 and agat-3 should be further monitored beyond week 5.
7. In Figure 3, the authors use co-expression by in situ hybridization to demonstrate the expression of ago in neoblasts. To provide the whole-animal context, co-expression of smedwi-1 and ago genes should also be confirmed using the current Sme scRNAseq datasets.
8. The authors proposed in the Discussion that AGO-1 may sponge unwound RNA duplex and this facilitates the dsRNA transfer. This interpretation seems unlikely, because the ago-1 single KD, which would abolish such dsRNA transfer, did not show phenotypes in terms of systemic RNAi defect. Also, such scenario suggests that loss-of-function of ago-1 may be antimorphic since the sponged dsRNA were released, and thus co-KD of ago-1 and ago-3 should result in more efficient RNAi. These concern should be discussed.
9. The Discussion states that AGO-1 is required in the donor, but this is inconsistent with the results in Figure 5D, where ago-1 KD in the donor did not abolish RNAi in the recipients. This inconsistency between results and text should be corrected.
10. In Figure S5I, the authors show that short dsRNA generated by RNase III digestion failed to induce systemic RNAi in sid-1 loss-of-function condition. However, the alternative explanation is that RNase III digestion produced short dsRNAs that may result in siRNA with suboptimal length for AGO loading or functioning. This caveat should be mentioned, and the length profile of the RNase III digestion products should be shown by high density urea gel electrophoresis or HPLC.
11. In all the transfer assays, one concern is the lysate may contain viable neoblasts, so that any observed results could be attributed to the proliferation of the donor-derived neoblasts rather than the transfer of RNAi materials. Therefore, a cell viability test using Calcein AM or other equivalent assay should be conducted to confirm the absence of live cells in the lysate preparation protocol.
12. In the second paragraph of the introduction, when comparing the siRNA and miRNA pathways, the difference in base-pairing configuration with the target site should be introduced with appropriate reference.
13. In the last paragraph of the introduction, the claim that the results may have implications for the design of effective RNAi-based therapies is too vague. Given that the current therapeutic siRNA delivery methods are already robust in clinical applications, the authors should more specifically explain how their findings in Sme might inform therapeutic development.
14. In the last sentence of the second last paragraph of the introduction and Figure S5I, "RNAse" should be corrected to "RNase".
15. In the first Results subsection, the second last paragraph, first sentence, one left parenthesis is missing.
16. Throughout the Discussion, the term "AGO-RNA". If the authors intend to express a distinction from RISC, how this terminology differs from RISC should be justified. Otherwise, RISC would be more appropriate.
17. Statistical significance should be shown in Figure 2E, 2G, 3A, 3C, S2A, S2D, S2G, S3D, S5D, S5G, S5J.
18. Molecular weight should be labeled in Figure S5L.
19. In Figure 2J, where the y-axis indicates % prevalence, the down-facing bars (antisense reads) should also be labeled as positive values on the y-axis. Displaying them as negative percentages (-20%) is incorrect.
20. The small RNA cloning procedure should be described in the Methods. Basic information of sRNA sequencing, including read numbers, biotype distribution, proportion mapping to the triggering dsRNA, should be included too.
21. The methods used to measure RNA and protein concentrations should be included in the Methods section.
22. The irradiation protocol, including dosage, should be included in the Methods.
23. In the Methods section, subscripts of chemical formulas are rendered as squares throughout the text. This formatting issue should be corrected.
24. In the Results section, first subsection, second paragraph and first sentence. The cited data should be Suppl Figure S2D, not the current S2A-C.
25. The manuscript uses inconsistent formatting for supplemental figures (for example, "Suppl Figure S1B,C" versus "Suppl Figure 2A-C"). The formatting should be standardized.

Significance

Planarians have long been appreciated as a robust model organisms for studying gene function in animal regeneration, and one major advantage of this system is its highly efficient systemic RNAi. However, the molecular basis of the RNAi machinery has not been thoroughly investigated, and detailed RNAi efficacy hasn't been evaluated. This study therefore provides important value by characterizing the molecular components underlying systemic RNAi in Sme, which contributes to both fundamental understanding and to potential optimization of RNAi-based experiments in Sme.

In addition, the manuscript reports that stem cells are required for systemic RNAi in differentiated cells in Sme, a finding that has not been described in other organisms. Although the underlying mechanism remains unresolved, this observation offers potentially important implications for both RNA biology and stem cell biology.

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Reply to the reviewers

Reviewer #1

Major comments: 1) The study focused on regulatory activity in a lung-derived cellular setting and was well executed. However, the degree that non-coding variation in lung elements, particularly alveolar basal epithelial cells, modeled by A549 cells, contributes genetic risk for COVID19 severity is unclear. Especially as non-coding variants in other contexts such as immune cells have been shown to be enriched for disease risk. To strengthen the choice for the A549 cellular context, the authors can assess enrichment for COVID19 severity heritability using stratified LD-score regression (PMID: 26414678) using A549/lung epithelium chromatin data (ATAC-seq, CHIP-seq) to check for enrichment polygenic signal or if the lung associated-risk is focused on a restricted set of genome-wide significant signals.

The reviewer is correct that most analysis of non-coding variants to date has been in immune cells, as is the case for many GWAS studies. However, severe COVID-19 affects many systems, especially the lung alveolar epithelium, and so there is a pressing need for functional genomic studies that go beyond immune cells. We chose A549 due to its lung origin, experimental tractability, and availability of published datasets. While enrichment such as S-LDSC suggested by the reviewer would be a good indication to screen for cell types with enrichment in e.g. open chromatin, many of our STARR-seq hits were found in closed chromatin and so would have been missed by such an analysis. To further emphasize the importance of type II alveolar epithelial cells in severe COVID-19 progression, we added the following to the manuscript: * "Cell death and the innate immune response of type II alveolar epithelial cells, which also function as progenitors for type I epithelial cells, are the main driver of alveolar damage and acute respiratory distress syndrome in coronavirus infection (Bridges et al 2022 PMID 34404754; Qian et al 2013 PMID: 23418343)."*

2) It would strengthen the manuscript to compare the results to prior analyses where overlap exists (eg PMID:36763080). Particularly it would be informative to address if nominated variants for signals have different variants operating in different cell types. Also, one prominent variant, rs17713054, that had previously been nominated to operate in lung through in silico predictions and CRISPR perturbations (PMID:34737427) appears to be non-significant in this STARR-seq analysis. Was a different variant nominated at this locus? Could the authors expand on methodological differences that could explain this difference?

rs17713054 (chr3:45,818,159:G>A) was nominated by Downes et al (2021) based on in silico predictions. While the authors found rs17713054 resides in open chromatin and is a chromatin accessibility (ca)QTL, the variant did not validate in CRISPR perturbations. Deletion of the putative enhancer encompassing rs17713054 across 4 cell lines led to no detectible changes in expression of the predicted target gene LZFTL1. The lack of H3K27ac at the putative enhancer led the authors to conclude that this enhancer is not active in any of the lung epithelial cell lines tested, consistent with our STARR-seq results which suggest that rs17713054 is inactive in A549 cells.

We nominated 6 amVars at the LZFTL1 locus (Table 1) and propose there are multiple functional variants with small effect sizes operating at this locus which together significantly contribute to risk. We have included an additional supplemental figure panel (Fig. S2H) showing a genome browser view of these variants. As suggested by the reviewer, we also compared our results to Jagoda et al. That study only reported allele-specific change and not baseline activity, it is thus possible that very weak signal (below our thresholds) can show up as allele-specific. This appears to be the case for at least one variant (rs35454877) which we call as inactive but nevertheless has a significant allele-specific activity (mpralm padj

3) Given a subset of the prioritized variants originate from the credible set, were the amVars enriched in terms of posterior inclusion probability than the tested set? This technical information could be valuable for interpreting fine-mapping efforts.

We did not observe an enrichment of posterior inclusion probabilities (PIPs) for the amVars or active variants compared to inactive variants. One reason could be that we primarily find variants in weak enhancers with moderate effect sizes which may be too subtle to be attributed a high PIP by GWAS due to insufficient statistical power. It is also possible that variants with a high PIP are active in other cell types. Fine-mapped variant sets already contain variants likely to be functional, so observing no difference between already statistically likely functional variants is perhaps not surprising. Another study testing melanoma risk variants similarly observed no statistically significant differences in PIPs between MPRA functional and non-functional variants (Long et al 2022 PMID: 36423637). We have included a supplemental plot of the PIP scores (Fig. S2G) for inactive, active and amVars and added this analysis in the first results section (see revised manuscript lines 181-186).

4). Similarly, for the eQTL comparisons, what proportion of the amVar/eQTL pairs are directionally consistent (e.g. increased activity/increased expression)?

For the 29 amVars, there are a total of 4689 combined eQTLs across all GTEx tissues. When filtering for lung, there are 180 eQTLs across the 29 amVars, whereby only 17/29 amVars have eQTLs in lung. For 16 of these 17 amVars, there is at least 1 eQTL in lung that is directionally concordant - listed in Table 1. Notably, however, almost all variants which have lung eQTLs with concordant direction also have lung eQTLs with discordant direction, suggesting the effects may be more complicated. When considering all lung eQTLs in GTEx v11, amVars were surprisingly enriched for discordant direction of effect (see figure below, left). However, we noticed this signal was driven entirely by the variants in the H2 haplotype block (as proposed by the reviewer in question 5), which includes many genes with varying effects which may be unrelated to our amVars. When excluding chr17, no enrichment was seen (see figure below, right). There was also no significant correlation between the effect size magnitude of eQTL and STARR-seq. Therefore, globally comparing amVars and eQTLs was not informative per se. We emphasize that we have few amVars (29), which makes subtle correlations/enrichments less likely to be detectable. Siraj et al. (2026) (PMID: 41741648), testing a much larger variant set than ours and in multiple cell lines, observed weak correlation between MPRA allelic effects and eQTL normalized effect size (Spearman;s p = 0.35), although these libraries were selected to include only fine-mapped eQTLs in high PIP, in comparison to our libraries which also include a large number of additional variants in LD. Overall, this suggests eQTL effect size is not a strong predictor for variant effects observed by MPRAs. We have included a discussion about this (see revised manuscript lines 186-190).

5) Several of the variants implicated by STARR-seq, including several of the pairs with non-additive activity were associated with the MAPT locus. This locus has a common 900kb inversion in Europeans (PMID: 15654335), were these variants linked to the same H1/H2 haplotype?

Indeed, all five prioritised variant pairs, as well as 5 amVars and 2 further variant pairs showing STARR-seq activity at this locus (Table 1, Table 2), are linked to the same (H2) haplotype. More specifically, all variants show high LD with the H2 haplotype-tagging SNP rs8070723‐G in European ancestry (r2 > 0.73) and are not linked to one of the H1 haplotype-tagging SNPs (rs242557-A, r2

6) Were the variants with non-additive effects analyzed for transcription factor motifs?

We looked for both motifs (FIMO and motifbreakR) and predictions of contribution scores using Malinois and AlphaGenome in the non-additive combinations, without finding any evidence for synergistic binding/activity. For example, see below the non-additive example in Fig. 3C (rs77819001_rs76667867), where the total activity prediction by Malinois is low (0.10-0.14), and there is no evidence of non-additive contribution scores as expected from the STARR-seq results. Because of the few examples, we cannot determine whether this is due to a systematic inability of the models to predict non-additivity, and therefore we chose not to present them. For transparency, we added the following sentence to the results: "For prioritized, non-additive variants pairs neither model identified an impact on transcription factor motifs that could explain the observed non-additivity. However, the few examples preclude drawing any general conclusions regarding the ability of these models to detect non-additivity."

Minor comments: 1) The sentence in the methods, Variant selection and design section, "the 95% credible set from the second GenOMICC releases containing causal variants to 95% statistical probability," is somewhat unclear. Given that the next sentence describes the 99% credible set, the authors should use more consistent terminology.

For the 3rd release we used the 99% credible set of variants to increase comprehensiveness of our library, meaning the list of variants contains causal variants to 99% statistical probability. In contrast, for the first and second release we used the 95% credible set as is the standard for fine-mapped variants. We clarified the phrasing in the methods as follows: "Fine-mapped severe COVID-19 risk variants encompassing causal variants to 95% statistical probability (95% credible set) from the first and second GenOMICC release2 and a more comprehensive 99% credible set of variants from the third GenOMICC release2 were included in the STARR-seq library."

2) Some text in supplemental figures (Fig S6) is too small to be legible. Please either remove or adjust the figure size.

We removed the variant IDs from figure panels S6A and S6B to aid readability.

Reviewer #2

Major comments: 1). The major conclusion is well supported by the main data presented; but additional clarification and extension in the discussion part may be helpful to determine the potential impacts and application of such conclusions especially related splicing isoform changes regulated by potential functional variants. "OPTIONAL" CRISPR editing for a couple of selected genes/variants will be helpful to confirm effects of these novel pathways.

We thank the reviewer for the positive appraisal.

Regarding splicing isoform changes, rs2297480 lies within the promoter-proximal region of two alternative FDPS isoforms which lack the penultimate exon encoding part of the catalytic domain. Therefore, we propose the variant could increase expression of a non-enzymatically functional FDPS isoform, which may compete with the functional isoform for substrate binding, thereby decreasing overall FDPS enzymatic activity. There are other examples of such "promoter usage" QTLs. We have rephrased this section and included references to studies supporting such a situation at other loci *"While speculative, global analyses have found examples where enhancer/promoter variants are proposed to lead to isoform expression changes (so called promoter usage QTLs), which may have disease implications (PMID 36037215, 30618377)" *

While CRISPR editing could be interesting, it would require extensive additional resources and is outside of the scope of the current manuscript. As a significant proportion of our amVars are not within accessible chromatin nor overlapping active chromatin modifications, we expect these to be functional in a different cell type rather than A549. Identifying a suitable cell line for CRISPR editing would therefore be non-trivial. Furthermore, the small effect size of our hits suggests seeing clear effects of single variants on transcription may be hard, as genes can be controlled by multiple enhancers simultaneously.

Minor comments: 1, please be specific about the proportion here in the text "Similarly, the proportion of active candidate sequences overlapping predicted ENCODE CREs in A549 cells was increased compared to inactive sequences (Fig. S2F)."

We added the specific proportions to the text: "Similarly, the proportion of active candidate sequences (39.3%) overlapping predicted ENCODE CREs in A549 cells was increased compared to inactive sequences (23.2%) (Fig. S2E)."

2, Out of 29 variants showing allele-specific effects, how many of them are close to the known TSS of candidate genes. Is IFNA is the only gene nearby these 29 variants?

rs7041102/rs7040981 reside ~4.5-5.5kb from the TSSs of IFNA10 and IFNA16. More gene-proximal variants include rs2297490, residing within in the first intron of the reference FDPS isoform and in the promoter-proximal region of three further FDPS isoforms (discussed above). In addition, rs145951274 resides in the first intron of HCG27 and rs3130925 in the first intron of the reference MICB isoform and within the promoter region of an alternative MICB isoform. We have added information on the distance to the closest TSS for all 29 amVars in Table 1 and indicated whether the variant is intronic.

3, out of 166 variants, what are genes with TSS closer to the 166 variants. It will be helpful to have a table or list of these genes since their promoter close to the significant variants

Of 166 active variants, 20 are within 1kb of the nearest TSS. Of those, 16 occur in the 1kb upstream or 100bp downstream of the TSS, the other 4 variants are within 1kb downstream. We have added this information as a new column to Supplementary Table 3 now showing the distance to the nearest TSS for all single variants tested, and we have modified figure S2F (previously S2E) which now shows the comparison of TSS proximity for inactive, active, and amVars.

4, Do these 16 combinations of variants pairs have genetic interaction in the population levels, i.e. epistasis?

This is an intriguing point, but challenging to test and beyond the scope of this work. 12/16 variant pairs are in very high or perfect LD (Table 2) and therefore either both risk variants or neither will co-occur in the population. We therefore cannot test if two variants have epistatic (beyond additive) effects in the population, nor can we directly link individual variants to a biological phenotype and therefore test for epistatic effects on phenotypes. We are limited to testing for beyond additive, i.e. epistatic, regulatory effects in the context of the STARR-seq assay, which we show in Fig 3B.

5, It needs more clarification why the risk allele of rs2297480 at the FDPS locus is associated with increased enhancer activity and decreased levels or activity of FDPS?

We have addressed this point under major comment 1 in the context of enhancer/promoter-driven isoform switches as plausible disease mechanism.

To clarify, the rs2297480 risk allele showed increased enhancer activity by STARR-seq. The variant lies within the promoter-proximal region of two alternative FDPS isoforms which lack the penultimate exon encoding part of the catalytic domain. Therefore, we propose the variant could increase expression of a non-enzymatically functional FDPS isoform, thereby decreasing overall FDPS enzymatic activity as the enzymatically inert isoform may compete with the functional isoform for substrate binding. We emphasize that this possible mechanism at FDPS is speculative.

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Referee #2

Evidence, reproducibility and clarity

Summary

This Manuscript by Dr. Weykopf and Friman et al applied STARR-Seq method to screen and identify function variants that determine the severity of COVID-19 patients in lung epithelial cell lines followed by functional validation. Both additive and non additive effects of various regulatory variants were evaluated. Furthermore machine learning models were applied to interpret allele specific variant effects. This is a pioneering work to identify functional variants on GWAS loci associated with severe COVID-19 with solid methods and modeling. sufficient literatures were cited and discussed. The major limitations were well discussed.

Significance

Major comments

The major conclusion is well supported by the main data presented; but additional clarification and extension in the discussion part may be helpful to determine the potential impacts and application of such conclusions especially related splicing isoform changes regulated by potential functional variants. "OPTIONAL" CRISPR editing for a couple of selected genes/variants will be helpful to confirm effects of these novel pathways. .

Minor comments

1. please be specific about the proportion here in the text "Similarly, the proportion of active candidate sequences 153 overlapping predicted ENCODE CREs in A549 cells was increased compared to 154 inactive sequences (Fig. S2F)."
2. Out of 29 variants showing allele-specific effects, how many of them are close to the known TSS of candidate genes. Is IFNA is the only gene nearby these 29 variants?
3. out of 166 variants, what are genes with TSS closer to the 166 variants. It will be helpful to have a table or list of these genes since their promoter close to the signficant variants
4. Do these 16 combinations of variants pairs have genetic interaction in the population levels, i.e. epistasis?
5. It needs more clarification why the risk allele of rs2297480 at the FDPS locus is associated with increased enhancer activity and decreased levels or activity of FDPS?

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Referee #1

Evidence, reproducibility and clarity

Summary:

To investigate the contribution of non-coding GWAS variants linked to COVID19 severity across individuals, Weykopf and colleagues assayed allelic differences in reporter activity using STARR-seq in the A549 lung epithelial cancer cell line. The authors prioritize 4,894 COVID19 severity associated variants from several GWAS for functional screening. Of these, 166 of the variants designed elements displayed significant enhancer activity, and 29 of these also displayed allele-modulated activity. These results were further contextualized through comparisons with lung-cell relevant chromatin marks. Additionally, a subset of variants in close proximity were analyzed for non-additive effects in the reporter assay. In addition, results were compared results to predictions using deep modeling approaches such as AlphaGenome and Malinois. This approach allows for a systematic characterization of these variants and expands on previous work focused on narrower sets of variants. While well written and results are presented clearly, several additions could help with placing results in context.

Major comments:

• The study focused on regulatory activity in a lung-derived cellular setting and was well executed. However, the degree that non-coding variation in lung elements, particularly alveolar basal epithelial cells, modeled by A549 cells, contributes genetic risk for COVID19 severity is unclear. Especially as non-coding variants in other contexts such as immune cells have been shown to be enriched for disease risk. To strengthen the choice for the A549 cellular context, the authors can assess enrichment for COVID19 severity heritability using stratified LD-score regression (PMID: 26414678) using A549/lung epithelium chromatin data (ATAC-seq, CHIP-seq) to check for enrichment polygenic signal or if the lung associated-risk is focused on a restricted set of genome-wide significant signals.
• It would strengthen the manuscript to compare the results to prior analyses where overlap exists (eg PMID:36763080). Particularly it would be informative to address if nominated variants for signals have different variants operating in different cell types. Also, one prominent variant, rs17713054, that had previously been nominated to operate in lung through in silico predictions and CRISPR perturbations (PMID:34737427) appears to be non-significant in this STARR-seq analysis. Was a different variant nominated at this locus? Could the authors expand on methodological differences that could explain this difference?
• Given a subset of the prioritized variants originate from the credible set, were the amVars enriched in terms of posterior inclusion probability than the tested set? This technical information could be valuable for interpreting fine-mapping efforts. Similarly, for the eQTL comparisons, what proportion of the amVar/eQTL pairs are directionally consistent (e.g. increased activity/increased expression)?
• Several of the variants implicated by STARR-seq, including several of the pairs with non-additive activity were associated with the MAPT locus. This locus has a common 900kb inversion in Europeans (PMID: 15654335), were these variants linked to the same H1/H2 haplotype?
• Were the variants with non-additive effects analyzed for transcription factor motifs?

Minor comments:

• The sentence in the methods, Variant selection and design section, "the 95% credible set from the second GenOMICC releases containing causal variants to 95% statistical probability," is somewhat unclear. Given that the next sentence describes the 99% credible set, the authors should use more consistent terminology.
• Some text in supplemental figures (Fig S6) is too small to be legible. Please either remove or adjust the figure size.

Significance

The authors performed a systematic evaluation of COVID19 risk variants in a lung relevant cell line. This study expands the number of variants tested as well as explores them in the lung cellular context. As this study did not filter tested variants allowing for comprehensive integration with chromatin annotations and computational predictions. This provides nominates a short list of lung relevant variants for further investigation. This paper will be of interest to genetics community interested in basic research in COVID19 severity.

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Reply to the reviewers

__ __We thank all reviewers for the valuable feedback and critical insight on our study. We acknowledge the concern that the manuscript, in its initial form, appeared descriptive and did not provide the mechanistic insight inferred from the current data. In the revised manuscript, we will (i) more clearly delineate what mechanistic inferences can be drawn from the existing data, (ii) expand our discussion of the caspase-independent mechanisms, and (iii) incorporate additional experiments/analyses aimed at identifying downstream effectors that mediate the observed phenotypes. In this revision plan, we have included six new figures addressing some of the major issues raised by reviewers.

1. Specifically, to address questions about mechanistic insight, we generated stable ACSL1:HaloTag expressing hESCs. Currently presented as Figure 1A for reviewers____. __ACSL1 is a critical enzyme that catalyzes the first step of fatty acid oxidation at the outer mitochondrial membrane. Our previous analysis and work from the Opferman lab demonstrated that ACSL1 contains a BH3-like domain. Thus, we examined the effects of MCL-1 inhibition on the mitochondrial localization of this enzyme. Our findings pinpoint that MCL-1 inhibition is causing the displacement of ACSL1 from the mitochondria (__Figures 1B-C for reviewers). Our interpretations of the effects of MCL-1 inhibition are 2-fold: 1) as we show in our data, MCL-1 inhibition causes disruption of the mitochondrial cristae, altering the microenvironment for fatty acid oxidation, and 2) as seen in cancer cells, the MCL-1 inhibitor may also displace ACSL1 from the mitochondria. In the new version of the manuscript, we will focus on these 2 mechanisms as mechanistic outcomes of MCL-1 inhibition.
2. We have included data of cells treated with Perhexilin (CPT1/2 inhibitor), and Etomoxir (CPT1a inhibitor) (Figure 2 for reviewers). This experiment determines whether direct perturbation the FAO pathway mimics the effects of the MCL-1i.
3. We have assayed the effects of MCL-1 inhibition on oxygen consumption rates in NPCs. Currently presented as Figure 3 for reviewers.
4. We will perform MCL-1:MICOS proximity ligation assays and/or immunoprecipitation assays to determine whether MCL-1 inhibitors disrupt the association of MCL-1 with MICOS. Preliminary data suggesting an association (albeit, very weak) are shown in Figure 4 for reviewers. __Reviewer #1____ (Evidence, reproducibility and clarity (Required)): __

Summary: This study claims that beyond its canonical anti-apoptotic function, MCL-1 has essential non-apoptotic roles in human neurodevelopment. Pharmacologic inhibition of MCL-1 in human neural stem cells disrupts mitochondrial inner membrane architecture by destabilizing cristae and the OPA1-MICOS complex, leading to swollen mitochondria with disorganized cristae. These structural defects impair fatty acid oxidation and lipid droplet homeostasis, linking cristae integrity to metabolic competence. Independently of apoptosis or proliferation, MCL-1 inhibition selectively depletes intermediate neural progenitors, indicating a direct role in lineage progression. Overall, the work positions MCL-1 as a key regulator of mitochondrial structure-metabolism coupling that instructs neural progenitor identity and human neurogenesis.

Overall: The study does a good job of using (in most assays) caspase inhibition (e.g., QVD treatment) to block apoptotic responses induced by MCL-1 inhibition. As a result, many of the phenotypes caused by inhibition are likely to be independent of caspase activation. As a result, this manuscript would be of interest to researchers that study the topics of the BCL-2 family and cell death signaling, mitochondrial bioenergetics and dynamics, neurodevelopment, and cellular metabolism. However, as currently presented the manuscript is only descriptive and lacks mechanistic insight.

We thank Reviewer 1 for the insightful evaluation of our work. We are encouraged that the reviewer finds the study relevant to investigators in the fields of BCL-2 family biology, mitochondrial dynamics and bioenergetics, neurodevelopment, and cellular metabolism. We also thank the reviewer for pointing out the need to increase the mechanistic insight of our findings. As mentioned above, in the revised manuscript, we are proposing to address this.

Major Concerns:

1) The authors only use a single MCL-1 inhibitor and never use other non-targeting BH3-mimetics (such as venetoclax) as negative controls. This seems like a missed opportunity to demonstrate that the phenotypes observed are MCL-1 dependent.

This is an excellent point. We will include venetoclax (ABT-199) to examine their effect on intermediate progenitors (TBR2 +) and early born neurons (BIII tubulin +).

2) There is no mechanism proposed in this study other than reliance upon QVD as not affecting the phenotypes. As submitted, the manuscript only can speculate that these phenotypes are due to non-apoptotic roles of MCL-1 inhibition. The authors have missed an opportunity to explore MCL-1's non-apoptotic functions directly.

Mechanistically, we propose MCL-1 is acting in 2 ways: 1) as we show in our data, MCL-1 inhibition causes disruption of the mitochondrial cristae, altering the microenvironment for fatty acid oxidation, and 2) as seen in cancer cells, MCL-1 inhibitors may also displace ACSL1 from the mitochondria.

In the past few weeks, since receiving the initial reviews, we have focused on testing the 2nd possibility, since the accumulation of lipids was also seen in cancer cells (see PMID: 38503284). We have successfully generated stable ACSL1:HaloTag expressing hESCs (Figure 1A for reviewers). Our findings included here, ACSL1 is displaced from the mitochondria by MCL-1 inhibition in NPCs (Figures 1B-C for reviewers).

Other concerns exist that weaken the impact of the study.

1. Figure 1 should include the fact that QVD inhibition (shown in Sup Fig 2) does not obviate the phenotype induced by pharmacological inhibition of MCL-1 on mitochondrial morphology. We would like to clarify that QVD does prevent the phenotypes induced by MCL-1 inhibition on mitochondrial morphology. In Fig1B, we report an increase in volume and surface area at 24h and 48h along with a decrease in mitochondrial content at 48h when NPCs were treated with MCL-1i only. However, NPCs co-treated with QVD in Supp Fig 2B did not exhibit any significant morphological phenotypes on average or at min/max values. Reviewer 1 may be referring to Fig 1B’s corresponding min/max values presented in Supp Fig 2A where we reported an increase in __max __volume.

Figure #

Volume

Surface Area

Fig 1B (MCL-1i only, avg values)

Increase (avg vol)

increase (avg)

Supp Fig 2B (MCL-1i+QVD)

no change

no change

Supp Fig 2A (MCL-1i only, max/min values)

increase (max vol)

no change (max)

For clarity, we will move Supplementary Fig 2A into Supplementary Fig 1.

Figure 2 would benefit from evidence that caspase inhibition does not repress the phenotype on mitochondrial cristae morphology (volume and area). Furthermore, the FIB-SEM data are very hard to appreciate as the size precludes visualization of individual mitochondria.

While we included the visualization of the segmented mitochondria and cristae (Figure 2C), as well as snapshots through the z-stack for segmented cristae only (Figure 2E) and segmented mitochondria separately (Supp Figure 3A) in the original manuscript, we are also now attaching the FIB-SEM 3D reconstruction videos (New Supplementary Videos 1-2 for reviewers) (1. Mito and cristae, 2. Cristae only, 3. Mito only) for ease of visualization purposes.

Figure 3 reports that MIC60 and OPA1 appear to be downregulated in response to MCL-1 inhibition, but these appear to be more significant only when QVD is added. Why would the phenotype be obscured in the non-QVD setting (Fig. 2B&C). How does MCL-1 inhibition lead to changes in MIC60/MICOS/OPA1? This seems quite preliminary at this point.

In Figures 3B and 3C, we report decreased protein levels of short-form OPA1 and MIC10 only, not MIC60. We argue that our data with QVD shows that the cell death function of MCL-1 (i.e., inhibiting cell death effectors from initiating the caspase cascade) is not the main trigger of the phenotypes we report (cristae dysregulation and fatty acid oxidation disruption), however, cells without a functional cristae and/or defects in FAO, may not be able to survive long-term. Thus, QVD treatment preserves these cells that may not survive the dismantling of such an essential structure. To confirm this, we have performed immunofluorescence of cleaved caspase 3 (Figure 5 for reviewers). These results show that indeed MCL-1 inhibition at the time points of our study doesn’t result in increased activation of Caspase-3. We reported similar results of MCL-1 inhibition in oligodendrocyte precursor cells (Gil and Hanna et al., Glia, 2025, PMID: 41420072)

The loss of MIC60 and OPA1 should repress electron transport chain function, are such impacts observed in the cultured cells? This could be shown by assessing oxygen consumption, etc. Such data would enhance the authors' conclusion that MCL-1 inhibition leads to defects in mitochondrial physiology*. *

We completely agree with this comment by Reviewer 1. In our revision, we will include an assessment of mitochondrial oxygen consumption rate, using the Seahorse analyzer (mitochondrial stress test), of NPCs treated with MCL-1i. Preliminary data (n=3) are currently presented as Figure 3 for reviewers. Interestingly, these data show a more nuanced cellular response. Consistent with our conclusion that MCL-1 inhibition does not cause apoptotic cell death, MCL-1i did not affect mitochondrial respiration at baseline. The specific deficits appear in spare respiratory capacity and maximal respiration, meaning cells can sustain routine mitochondrial function but lose the ability to respond to increased energetic demand. This suggests MCL-1 loss creates a mitochondrial reserve deficiency rather than a generalized bioenergetic failure. The results with caspase inhibitors show a near-zero OCR across both 24h and 48h timepoints, and significant reductions in maximal respiration, spare respiratory capacity, and non-mitochondrial OCR. Remarkably, these conditions are not detrimental to newborn neurons, as shown in Figure 7. This is very interesting because it suggests that, under severe bioenergetic failure, neural stem cells (PAX6+) can differentiate into newborn neurons in a TBR2-independent manner. More relevant to this study, our results unequivocally demonstrate that TBR2-positive cells depend on the non-apoptotic function of MCL-1

In Figure 4, the differences between transcripts (qPCR data) and protein (immunoblot) data are often confusing and not well explained. Why do the authors propose that mRNA expression is decreasing whereas the protein expression is increasing? Example CPT1. Furthermore, it is unclear what these data mean functionally? Is this reflective of enhanced lipid oxidation or simply a response to inhibition of fatty acid oxidation? Clarification of the impact of these findings is necessary.

We agree with Reviewer 1 that the results could be hard to interpret. However, the effects of MCL-1 inhibitors on the transcription of fatty acid oxidation genes have been widely cited by the work of Opferman and Walensky (PMID: 36198266). We speculate that the effects on transcription are triggered by mitochondrial signaling. The mechanistic insight into this phenomenon would be an interesting next step.

In the case of CPT1, we addressed this comment and found that the difference is due to differential expression of isoforms The RT-qPCR shown in Figure 4, is on CPT1c, whereas the western blot is on CPT1a. Unfortunately, after trying several products, we determined that there are no good antibodies for CPT1c. Thus, since we can’t compare gene and protein expression, we will include CPT1a RT-qPCR data to complement the western blot.

The increase in lipid droplet number induced by MCL-1 inhibition has been previously documented, but it is unclear whether this increase is related to an inability to oxidize lipid (defective fatty acid oxidation) that leads to increases in the cellular abundance or whether this indicates that MCL-1 inhibition leads to enhanced storage. Do other inhibitors of fatty acid oxidation lead to similar increases in lipid droplet size and abundance? Does QVD inhibition affect this phenotype?

This is a great point raised by Reviewer 1, and one we have also wondered about. We conducted an experiment using C16 BODIPY to address this point (Figure 6 for Reviewers). We observed no changes in C16 lipid droplet accumulation in count, volume, or surface area when cells were treated with MCL-1 inhibitor for 24 hours total with or without a starvation period in the last 6 hours of treatment. However, we observed significant pan-lipid droplet accumulation in the same conditions. This contrast suggests that FAO of exogenous LC-fatty acids is not reliant on MCL-1. This finding does not discount from the requirement of MCL-1 for other FAO processes especially given the major limitation of how much C16 BODIPY (fluorescent palmitate) can be administered to the cells (10µM) which was 10-fold less than what we exogenously supplied to the cells for the pan-BODIPY experiment (100µM, see Figure 5). It is entirely possible that this small dose was not enough to detect any lipid droplet accumulation.

We have now also included experiments using etomoxir and perhexiline to assess their effects on TBR2/PAX6 (Figure 2 for reviewers). The results indicate that inhibiting the FAO pathway does not fully mimic the effects of MCL-1i on TBR2. However, we show that MCL-1i displaces ACSL1 from the mitochondria, a step that is upstream of CPT1/2. We suggest a model in which the coordinated non-apoptotic function of MCL-1 at the outer mitochondrial membrane promotes ACSL1 activity and, in the inner mitochondrial membrane, regulates mitochondrial cristae morphology. While our data point to this model, we are limited by the tools to investigate it further, but it will be a great direction for future experiments.

For Figure 6, while these data may be very meaningful, as presented they are very hard to appreciate. Insets that show the neuronal populations would help to convey the point that the differentiation is impacted. Also, are there other methods that could confirm these observations (qPCR to show changes in differentiation).

We agree with Reviewer 1. In the new version of the manuscript, we will include panels that zoom into the cell populations we quantified. The current panels will go to a new Supplemental figure. We will also add the TUBB3 to the qPCR panel in the new version.

Figure 7 is also very hard to appreciate. What is the reader to see? Can these be quantified? It seems that QVD may be rescuing in this figure, does this suggest that MCL-1 inhibition might be inducing death. All of this needs to be quantified.

We will provide quantification of BIII tubulin branching, and it will be included next to the images provided.

BCL-XL has also been implicated in affecting mitochondrial electron transport chain function (See PMID: 19255249, 21926988, 21987637). Can BCL-XL inhibitors affect any of the phenotypes associated here?

We will include experiments to test the effect of BCL-2 and BCL-XL inhibitors on TBR2 cells to address this comment.

Please be carefully avoid using the term "MCL-1 loss", when talking about pharmacological inhibition. Only genetic ablation (e.g. knockout, silencing, etc.) should be termed loss.

We have now removed the reference to MCL-1 loss in line 199.

__*Reviewer #1 (Significance (Required)):

The study advances in human cells the impacts of MCL-1 inhibition. They replicate many impacts previously observed in mouse systems and refine analyses to impacts on MICOS complex, lipid droplet storage, and neuronal differentiation. While these findings are important and would be well received by a wide audience, the study fails to provide almost any mechanistic insight into how these phenotypes are being induced. The only common theme is that blocking caspase activation in many assays fails to block the phenotype.

*__

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

Summary: This manuscript by Hanna et al. investigates non-apoptotic roles of MCL-1 in human neural stem cells and connects MCL-1 inhibition to mitochondrial cristae formation and beta-oxidation. Connecting these roles to brain development, the authors also show a reduction in the number of progenitor cells upon MCL-1 inhibition, independently of caspase activity. Throughout their work, the authors make use of an impressive array of imaging techniques. While the methods used offer sufficient evidence to connect MCL-1 inhibition to cristae architecture, the mechanistic underpinnings of this effect remain unexplored. *__

We thank Reviewer 2 for the thoughtful and positive assessment of our manuscript. We appreciate the reviewer’s recognition that our study reveals non-apoptotic roles of MCL-1 in human neural stem cells. We are also grateful for the acknowledgment of the imaging approaches employed, which allowed us to connect MCL-1 function to cristae architecture with multiple complementary techniques. We acknowledge the reviewer’s point that the mechanistic basis by which MCL-1 influences cristae structure remains insufficiently defined. In the revised manuscript, we will clarify the limitations of the current data, expand our discussion of potential mechanisms, and incorporate additional analyses to identify downstream effectors that mediate these structural and metabolic changes.

Major comments:

- In Fig. 1B, the very same representative images are shown for both conditions (DMSO and S63845) at 48 hours.

We deeply appreciate Reviewer 2 for catching this unintentional duplication that occurred during figure preparation. We have now corrected this issue.

- For Western Blot analysis, it looks like the authors only quantified the band density of their proteins of interest without considering varying levels of control protein (Actin) levels. Normalizing the protein levels to actin would account for any differences in loaded protein amounts (although a Ponceau staining might be preferable still to exclude this). This is especially relevant for Fig. 4E, where actin levels visibly differ between the conditions.

All WB quantifications were normalized to Actin (this detail is now added to the y-axis of all band density graphs and figure legends). In addition, we will transform the data to a logarithmic scale to “normalize” for gel-to-gel variability.

- The authors offer evidence that MCL-1 inhibition impedes proteolytic cleavage of OPA1-L into the OPA-1-S isoforms, yet do not explore the mechanism behind this. Since OPA1 is cleaved by both OMA1 and YME1L, determination of the levels of these proteases could help shed some light on the mechanism leading to cristae reorganization.

We will follow up on Reviewer 2's comment with a WB analysis of OMA1 and YMEL in cells treated with an MCL-1 inhibitor.

- Generally speaking, while the authors show all those effects (cristae defects, FAO dysfunction) upon MCL-1 inhibition, it would be interesting to see whether any of those effects can be rescued by blocking FA import e.g. through carnitine palmitoyl- transferase 1a (CPT1a) inhibition with etomoxir to understand if they are downstream of altered Fa supply. This could affect cristae morphology through altered Cardiolipin biogenesis.

This is an excellent point, which was also raised by reviewer 1. We have now included experiments using etomoxir and perhexiline to assess their effects on TBR2/PAX6 (Figure 2 for Reviewers). As mentioned above, the results indicate that inhibiting the FAO pathway does not fully mimic the effects of MCL-1i on TBR2. However, we show that MCL-1i displaces ACSL1 from the mitochondria, a step that is upstream of CPT1 and 2. We suggest a model in which the coordinated non-apoptotic function of MCL-1 at the outer mitochondrial membrane promotes ACSL1 activity and, in the inner mitochondrial membrane, regulates mitochondrial cristae morphology. While our data point to this model, we are limited by the tools to investigate it further, but it will be a great direction for future experiments. The suggestion of Reviewer 2 that the effects on FAO could impact cardiolipin biogenesis is a very exciting possibility. However, difficult to test with the tools available.

- In line 262 the authors discuss that mitochondria lose metabolic function upon MCL-1 inhibition. This claim would require additional experiments. While the authors look at lipid droplet accumulation and FAO enzymes, there are many more aspects to mitochondrial metabolic function that should be investigated. While measuring the oxygen consumption rate via Seahorse might require additional resources (optional), measurements of ATP production, ROS generation or determination of the mitochondrial membrane potential should be feasible.

We fully agree with Reviewer 2's comment, which was also raised by Reviewer 1. In our revision, we will include an assessment of the mitochondrial oxygen consumption rate of NPCs treated with MCL-1i, measured using the Seahorse analyzer (mitochondrial stress test). These data are presented as Figure 3 for reviewers. Interestingly, these data show a more nuanced cellular response. While MCL-1i does not globally collapse mitochondrial respiration at baseline, the specific deficits appear in spare respiratory capacity and maximal respiration, meaning cells can sustain routine mitochondrial function but lose the ability to respond to increased energetic demand. This suggests MCL-1 loss creates a mitochondrial reserve deficiency rather than a generalized bioenergetic failure. The results with caspase inhibitors show a near-zero OCR across both 24h and 48h timepoints, and significant reductions in maximal respiration, spare respiratory capacity, and non-mitochondrial OCR. These conditions are detrimental for TBR2-positive NPCs (Figure 6) , but not for newborn neurons (Figure 7).

- While the authors "propose a model in which MCL-1 associates with MICOS", they do not offer direct scientific to support this hypothesis. Co-immunoprecipitation experiments or e.g. proximity ligation assays would better support the proposed model.

We agree with this statement. Preliminary, we have performed proximity ligation assays and immunoprecipitation analyses to test for this interaction (see below and ____Figure 4 for reviewers), and the results indicate an interaction, albeit very weak. In the revised version of the manuscript, we will attempt to repeat these experiments with MCL-1i.

- While Fig. 7 shows representative images, quantification e.g. for the truncation of neuronal processes is missing.

We will provide quantification of BIII tubulin branching, which will be included alongside the images provided.

- In lines 219f. the authors state that they "observed a significant downregulation of PAX6 and EOMES at 24 hours that was not rescued by QVD co-treatment". While there is still a trend towards a downregulation, there is no statistical significance anymore. In fact, PAX6 levels almost mirror those of SOX2 which is not described as "downregulated" by the authors. In order to be more consistent, I would suggest rephrasing this part, or at least reword it to be less absolute.

In the new version, we will clarify that while QVD rescued TBR2 and PAX6 transcript levels at 24h, it did not rescue them at 48h. We will also mention the downregulation of SOX2 at 48h that persists with co-treatment.

- Brinkmann et al. (2025) also investigated cristae structure upon MCL-1 deletion in vivo and found no effect when MCL-1 was replaced with other Bcl-2 family members. It would be interesting to combine MCL-1 inhibition with overexpression of MCL-1 versus BCL-XL to reconsolidate some of the discrepant findings.

While this is a great suggestion for future studies, there are some complications. Specifically, it is likely that the inhibitor may also target the overexpressed MCL-1 and thus, a mutant form is needed.

To address this, we generated a Flag-tagged MCL-1 construct with a mutated BH3 domain, previously described by Kotschy et al. Nature 2016. We validated the construct in HeLa cells, but unfortunately the mutant protein appears to be significantly less stable than the WT construct, complicating analysis of this experiment.

Minor comments:

- In Supp. Fig. 1C the MCL-1 protein is shown both to run above 37kDa (upper panel) and below 37 kDa (lower panel). Could the authors please comment on why this is the case?

The observed variation is caused by drift in the gel during electrophoresis. In Fig 1C, the protein ladder is on the edge of the gel, whereas in Fig 1E, the protein ladder is in the middle of the gel, and the last sample is on the edge and also exhibits edge drift.

- In line 64 of the introduction the authors mention clinical trials yet do not give a citation for these trials making it hard to judge whether the content of these trials is actually related to the brain.

This information is anecdotal, based on an Amgen press release.

- MCL-1 as well as ACSL-1 are sometimes written without the hyphen both in the text and figures.

We will carefully check the manuscript before submission.

- Lines 92-94 and 106-108 essentially highlight the same existing knowledge gap. Maybe the content of these two paragraphs could be combined in order to avoid repetition.

We thank Reviewer 2 for this suggestion. We will do this in the new version of the manuscript.

- In Fig. 1A, the authors provide a schematic for their experimental design. While the figure legend is very thorough, some of this information (like the days of collection) could also be included in the figure itself. The same is true for schematics in the following figures.

We agree with this and will incorporate the suggestion in the new version.

- Fig. 2A includes a typo (analyze) but would maybe also be more suitable for the supplement figures or could even be combined with Fig. 1A as not much new content is added.

We already incorporated these changes in the new version of the manuscript.

- Regarding statistical analysis, could the authors please comment on why they did not consider one-sample t-tests suitable for the cases where control values were set at 1 (e.g. Fig. 4B, C for the relative expression).

This is a valid suggestion. We will rerun RT-qPCR data using a one-sample t-test.

- In lines 247f. the authors state that "inhibition of MCL-1 leads to [...] and disassembly of the MICOS complex as well as OPA1". This sounds like OPA1 is still cleaved upon MCL-1, which is not at all what the authors showed and further discuss. Rewording of the sentence would help in avoiding any misunderstandings.

We agree with this comment and have now reworded the paragraph: “Inhibition of MCL-1 leads to structural collapse of the cristae likely due to the possible disassembly of the MICOS complex, as suggested by decreased MIC10 levels, and interruption of OPA1 cleavage, as suggested by decreased short-form OPA1, two scaffolds required for cristae maintenance.”

- In lines 210f. the authors state that "quantitative imaging increased the average and maximum volume of lipid droplets". While there is definitely a trend towards an increase for the maximum volume, the increase is in fact not statistically significant. This should be reflected in the wording.

We have reworded this to “Quantitative imaging revealed a significant increase in average lipid droplet volume and a trending increase in maximum volume of lipid droplets.”

- In Fig. 6 the overlap between TBR2 and PAX6 is hard to judge when printed out. Including a zoom-in may make it easier to judge.

We agree with Reviewer 2. In the new version of the manuscript, we will include panels that zoom into the cell populations we quantified. The current panels will go to a new Supplemental figure. We will also add the TUBB3 to the qPCR panel in the new version.

- In Fig. 7 the color-coding is listed in the figure legend but is missing from the figure itself. If the authors could include this, as they did for the other figures, it would further improve this figure.

We agree. We have specified the channel color in the new figure.

- Line 238 should reference Fig. 7A, as Fig 7B does not exist.

Thanks for catching this. It is already corrected

- In the figure legends the authors state that biological replicates were used. Were technical replicates also performed?

Yes, technical replicates were performed for RT-qPCR.

Reviewer #2 (Significance (Required)):____ Significance

The authors make use of a wide array of imaging techniques to further elucidate non-apoptotic roles of MCL-1. The study has the potential to offer new insights into mitochondrial biology on the level of basic research rather than translational. While the methods used offer sufficient evidence to connect MCL-1 inhibition to cristae architecture, the mechanistic underpinnings of this effect remain unexplored. Nevertheless, the study offers additional knowledge on the role of MCL-1 in human neural stem cells, whereas previous research mostly focused on cardiomyocytes or cancer cells.

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

Summary: ____ In this study, Gama et al. describe a non-canonical role for the anti-apoptotic protein Myeloid Cell Leukemia-1 (MCL-1) in mitochondrial cristae organization and suggest a role of MCL-1 in regulating metabolism and neuronal differentiation. Using fluorescence microscopy imaging and electron microscopy, the authors show changes to mitochondrial morphology upon treatment with MCL-1 inhibitor S63845. MCL-1 inhibition results in altered protein and transcript levels of some key proteins involved in mitochondrial cristae organization and fatty acid metabolism. While some of the findings are interesting and indeed point towards a non-canonical role of MCL-1, several key conclusions of the authors are not sufficiently supported by the data shown in the manuscript.

We thank Reviewer 3 for the careful evaluation of our manuscript. We appreciate the reviewer’s recognition that our study identifies a potential non-canonical role for MCL-1 in mitochondrial cristae organization, metabolism, and neuronal differentiation. As with Reviews 1 and 2, we are encouraged that the reviewer finds these observations interesting and suggestive of previously unappreciated functions for MCL-1. We agree that stronger evidence is required to firmly link MCL-1 inhibition to specific changes in MICOS organization and metabolic regulation. In the revised manuscript, we will (i) more clearly distinguish between observations and mechanistic inferences, (ii) temper conclusions where appropriate, and (iii) incorporate additional analyses and controls to better substantiate the proposed model.

Major comments:

1. The authors try to disentangle the apoptotic and non-apoptotic role of MCL-1 through addition of a caspase inhibitor. However, I am not convinced that phenotypes found under the addition of caspase inhibitor are necessarily caused by non-canonical functions independent of apoptosis. It could also be that the observed changes happen upstream of caspase activation. In addition, many of the described finding, such as CPT1 expression changes, only happen in the presence of the caspase inhibitor. If one follows the logic of the authors, changes associated by non-canonical MCL-1 functions should happen under MCL-1 inhibition and caspase inhibition, but not with MCL-1 inhibition only____. __ The reviewer is right that we expected non-canonical functions to happen under MCL-1 inhibition and caspase inhibition. Our data with QVD shows that the cell death function of MCL-1 (i.e., inhibiting cell death effectors from initiating the caspase cascade) is not the main trigger of the phenotypes we report (cristae dysregulation and fatty acid oxidation disruption), however, cells without a functional cristae and/or defects in FAO, may not be able to survive long-term. Thus, QVD treatment preserves these cells that may not survive the dismantling of such an essential structure. To confirm this, we performed immunofluorescence of cleaved caspase 3 (__Figure 5 for reviewers). These results show that, indeed, MCL-1 inhibition at the time points of our study doesn’t result in increased Caspase-3 activation. We reported similar results of MCL-1 inhibition in oligodendrocyte precursor cells (Gil and Hanna et al., Glia, 2025, PMID: 41420072).

The authors show no data on the viability of the cells in response to the MCL-1 inhibitor. To exclude secondary effects of the inhibitor, at least some of the results should be validated with an MCL-1 knock down.

We will include this experiment in our revised manuscript. To check the effects of MCL-1 knockdown on TBR2 positive cells, we tested 5 different ASOs for MCL-1. Knockdown efficiency with ASOs was very low (on average In Figure 1, the authors show immunofluorescence data of mitochondria and nucleus staining and conclude that MCL-1 inhibition alters mitochondrial morphology. Based on the images shown in Fig. 1, I do not think that individual mitochondria can be segmentd to measure their volume and length. In addition, some metrics such as mitochondrial content are not explained in the text or methods.

We can achieve mitochondrial segmentation with a SoRa Spinning Disk Confocal Microscope, which has a lateral (XY) resolution of approximately 120 nm to 150 nm and an axial (Z) resolution of approximately 300 nm–320 nm. All images are first denoised prior to sharpening using the Richardson-Lucy deconvolution algorithm. Additionally, the FIB-SEM data are consistent with the IF data (both show increase in mitochondrial volume and surface area).

We agree with Reviewer 3 that we need to explain some metrics in the revised version. We will specify the meaning of mitochondrial content (count of all mitochondria in FOV, not normalized to Hoechst).

In Fig. 2 B-D, the authors show TEM and FIB-SEM imaging to demonstrate alterations in the cristae architecture upon treatment with MCL-1 inhibitor. However, based on the images shown, it looks that cristae area and density is reduced under S63845 treatment in TEM images, while the FIB-SEM data come to the opposite conclusion. In addition, the quantification of cristae volume quantified as cristae volume in percentage is unclear to me.

We apologize for the confusion. No conclusions about the cristae area and density were made using the TEM data, because TEM data represent a single snapshot section of a mitochondrion without a discernible orientation. Cristae from TEM were described as “aberrant” and preliminarily revealed changes in cristae and were followed up with FIB-SEM, 3D reconstruction of intact mitochondria, and quantification of volume.

In the new version of the manuscript, we will specify that the cristae volume is normalized to the volume of its respective mitochondria (i.e., how much of the mitochondrial volume is attributed to cristae).

The change in CPT1/2 protein levels (Fig. 4) is interesting but does not directly proof that fatty acid oxidation is altered, as concluded by the authors. For this, the authors would need to directly measure fatty acid oxidation for example using Seahorse or metabolic tracing experiments. Also, to prove that the MCL-1 inhibition affects neural differentiation through fatty acid oxidation, a rescue experiment should be performed through CPT1 overexpression.

We agreed that this is an important point. We have optimized the fatty acid oxidation test using Seahorse and will make sure to include it in the revised version of the manuscript.

In Figure 6, the authors show decreased intermediate progenitor cells after MCL-1 inhibition by immunofluorescence staining. I am not convinced that this can be concluded from the data shown, since the concentration of intermediate progenitor cells is very close to the noise levels. Since the MCL-1 treated cells look much less sparse, I don't think the percentages can be compared (total counts are between 2-20). Although this data might give some indication that differentiation could be impaired, the measured effect could be very well due to lower viability of the cells. The authors need to control for this or come up with a different method for measuring differentiation.

The number of TBR2 is low, but we disagree with the reviewer’s assessment of noise levels. We focused on cells expressing only TBR2 and rigorously examined this population of cells. The percentages are compared to account for the lower density of the MCL-1i-treated cultures, as the IPC counts are normalized to the Hoechst total cell count within the FOV. Moreover, the immunofluorescence images are complemented with RT-qPCR, which shows significant downregulation of EOMES (gene encoding TBR2).

Figure 7 is missing quantification

We will include this quantification in the revised version of the manuscript.

Reviewer #3 (Significance (Required)):

General assessment____: The manuscript reports an interesting finding, which suggest a non-canonical role of MCL-1 in mitochondrial remodeling, regulation of fatty acid oxidation and neuronal fate. While this finding would be highly interesting and relevant, the presented data do not sufficiently support this conclusion. Further experiments would have to be performed to proof causality. ____ Advance: Should the authors manage to proof their hypothesis by additional experiments, this would indeed advance the field on mitochondrial remodeling and its effect on neuronal differentiation by

identifying a novel molecular player. ____ Audience: mitochondrial biology, cell biology, developmental neuroscience Own expertise: mitochondrial biology, cell biology, advanced imaging techniques

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this study, Gama et al. describe a non-canonical role for the anti-apoptotic protein Myeloid Cell Leukemia-1 (MCL1) in mitochondrial cristae organization and suggest a role of MCL1 in regulating metabolism and neuronal differentiation. Using fluorescence microscopy imaging and electron microscopy, the authors show changes to mitochondrial morphology upon treatment with MCL1 inhibitor S63845. MCL1 inhibition results in altered protein and transcript levels of some key proteins involved in mitochondrial cristae organization and fatty acid metabolism. While some of the findings are interesting and indeed point towards a non-canonical role of MCL1, several key conclusions of the authors are not sufficiently supported by the data shown in the manuscript.

Major comments:

1. The authors try to disentangle the apoptotic and non-apoptotic role of MCL1 through addition of a caspase inhibitor. However, I am not convinced that phenotypes found under the addition of caspase inhibitor are necessarily caused by non-canonical functions independent of apoptosis. It could also be that the observed changes happen upstream of caspase activation. In addition, many of the described finding, such as CPT1 expression changes, only happen in the presence of the caspase inhibitor. If one follows the logic of the authors, changes associated by non-canonical MCL1 functions should happen under MCL1 inhibition and caspase inhibition, but not with MCL1 inhibition only.
2. The authors show no data on the viability of the cells in response to the MCL1 inhibitor. To exclude secondary effects of the inhibitor, at least some of the results should be validated with an MCL1 knock down.
3. In Figure 1, the authors show immunofluorescence data of mitochondria and nucleus staining and conclude that MCL1 inhibition alters mitochondrial morphology. Based on the images shown in Fig. 1, I do not think that individual mitochondria can be segmentd to measure their volume and length. In addition, some metrics such as mitochondrial content are not explained in the text or methods.
4. In Fig. 2 B-D, the authors show TEM and FIB-SEM imaging to demonstrate alterations in the cristae architecture upon treatment with MCL1 inhibitor. However, based on the images shown, it looks that cristae area and density is reduced under S63845 treatment in TEM images, while the FIB-SEM data come to the opposite conclusion. In addition, the quantification of cristae volume quantified as cristae volume in percentage is unclear to me.
5. The change in CPT1/2 protein levels (Fig. 4) is interesting but does not directly proof that fatty acid oxidation is altered, as concluded by the authors. For this, the authors would need to directly measure fatty acid oxidation for example using Seahorse or metabolic tracing experiments. Also, to prove that the MCL1 inhibition affects neural differentiation through fatty acid oxidation, a rescue experiment should be performed through CPT1 overexpression.
6. In Figure 6, the authors show decreased intermediate progenitor cells after MCL1 inhibition by immunofluorescence staining. I am not convinced that this can be concluded from the data shown, since the concentration of intermediate progenitor cells is very close to the noise levels. Since the MCL1 treated cells look much less sparse, I don't think the percentages can be compared (total counts are between 2-20). Although this data might give some indication that differentiation could be impaired, the measured effect could be very well due to lower viability of the cells. The authors need to control for this or come up with a different method for measuring differentiation.
7. Figure 7 is missing quantification

Significance

General assessment: The manuscript reports an interesting finding, which suggest a non-canonical role of MCL1 in mitochondrial remodeling, regulation of fatty acid oxidation and neuronal fate. While this finding would be highly interesting and relevant, the presented data do not sufficiently support this conclusion. Further experiments would have to be performed to proof causality.

Advance: Should the authors manage to proof their hypothesis by additional experiments, this would indeed advance the field on mitochondrial remodeling and its effect on neuronal differentiation by identifying a novel molecular player.

Audience: mitochondrial biology, cell biology, developmental neuroscience

Own expertise: mitochondrial biology, cell biology, advanced imaging techniques

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Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript by Hanna et al. investigates non-apoptotic roles of MCL-1 in human neural stem cells and connects MCL-1 inhibition to mitochondrial cristae formation and beta-oxidation. Connecting these roles to brain development, the authors also show a reduction in the number of progenitor cells upon MCL-1 inhibition, independently of caspase activity. Throughout their work, the authors make use of an impressive array of imaging techniques.While the methods used offer sufficient evidence to connect MCL-1 inhibition to cristae architecture, the mechanistic underpinnings of this effect remain unexplored.

Major comments:

• In Fig. 1B, the very same representative images are shown for both conditions (DMSO and S63845) at 48 hours.
• For Western Blot analysis, it looks like the authors only quantified the band density of their proteins of interest without considering varying levels of control protein (Actin) levels. Normalizing the protein levels to actin would account for any differences in loaded protein amounts (although a Ponceau staining might be preferable still to exclude this). This is especially relevant for Fig. 4E, where actin levels visibly differ between the conditions.
• The authors offer evidence that MCL-1 inhibition impedes proteolytic cleavage of OPA1-L into the OPA-1-S isoforms, yet do not explore the mechanism behind this. Since OPA1 is cleaved by both OMA1 and YME1L, determination of the levels of these proteases could help shed some light on the mechanism leading to cristae reorganization.
• Generally speaking, while the authors show all those effects (cristae defects, FAO dysfunction) upon MCL-1 inhibition, it would be interesting to see whether any of those effects can be rescued by blocking FA import e.g. through carnitine palmitoyl- transferase 1a (CPT1a) inhibition with etomoxir to understand if they are downstream of altered Fa supply. This could affect cristae morphology through altered Cardiolipin biogenesis.
• In line 262 the authors discuss that mitochondria lose metabolic function upon MCL-1 inhibition. This claim would require additional experiments. While the authors look at lipid droplet accumulation and FAO enzymes, there are many more aspects to mitochondrial metabolic function that should be investigated. While measuring the oxygen consumption rate via Seahorse might require additional resources (optional), measurements of ATP production, ROS generation or determination of the mitochondrial membrane potential should be feasible.
• While the authors "propose a model in which MCL-1 associates with MICOS", they do not offer direct scientific to support this hypothesis. Co-immunoprecipitation experiments or e.g. proximity ligation assays would better support the proposed model.
• While Fig. 7 shows representative images, quantification e.g. for the truncation of neuronal processes is missing.
• In lines 219f. the authors state that they "observed a significant downregulation of PAX6 and EOMES at 24 hours that was not rescued by QVD co-treatment". While there is still a trend towards a downregulation, there is no statistical significance anymore. In fact, PAX6 levels almost mirror those of SOX2 which is not described as "downregulated" by the authors. In order to be more consistent, I would suggest rephrasing this part, or at least reword it to be less absolute.
• Brinkmann et al. (2025) also investigated cristae structure upon MCL-1 deletion in vivo and found no effect when MCL-1 was replaced with other Bcl-2 family members. It would be interesting to combine MCL-1 inhibition with overexpression of MCL-1 versus BCL-XL to reconsolidate some of the discrepant findings.

Minor comments:

• In Supp. Fig. 1C the MCL-1 protein is shown both to run above 37kDa (upper panel) and below 37 kDa (lower panel). Could the authors please comment on why this is the case?
• In line 64 of the introduction the authors mention clinical trials yet do not give a citation for these trials making it hard to judge whether the content of these trials is actually related to the brain.
• MCL-1 as well as ACSL-1 are sometimes written without the hyphen both in the text and figures.
• Lines 92-94 and 106-108 essentially highlight the same existing knowledge gap. Maybe the content of these two paragraphs could be combined in order to avoid repetition.
• In Fig. 1A, the authors provide a schematic for their experimental design. While the figure legend is very thorough, some of this information (like the days of collection) could also be included in the figure itself. The same is true for schematics in the following figures.
• Fig. 2A includes a typo (analyze) but would maybe also be more suitable for the supplement figures or could even be combined with Fig. 1A as not much new content is added.
• Regarding statistical analysis, could the authors please comment on why they did not consider one-sample t-tests suitable for the cases where control values were set at 1 (e.g. Fig. 4B, C for the relative expression).
• In lines 247f. the authors state that "inhibition of MCL-1 leads to [...] and disassembly of the MICOS complex as well as OPA1". This sounds like OPA1 is still cleaved upon MCL-1, which is not at all what the authors showed and further discuss. Rewording of the sentence would help in avoiding any misunderstandings.
• In lines 210f. the authors state that "quantitative imaging increased the average and maximum volume of lipid droplets". While there is definitely a trend towards an increase for the maximum volume, the increase is in fact not statistically significant. This should be reflected in the wording.
• In Fig. 6 the overlap between TBR2 and PAX6 is hard to judge when printed out. Including a zoom-in may make it easier to judge.
• In Fig. 7 the color-coding is listed in the figure legend but is missing from the figure itself. If the authors could include this, as they did for the other figures, it would further improve this figure.
• Line 238 should reference Fig. 7A, as Fig 7B does not exist.
• In the figure legends the authors state that biological replicates were used. Were technical replicates also performed?

Significance

The authors make use of a wide array of imaging techniques to further elucidate non-apoptotic roles of MCL-1. The study has the potential to offer new insights into mitochondrial biology on the level of basic research rather than translational. While the methods used offer sufficient evidence to connect MCL-1 inhibition to cristae architecture, the mechanistic underpinnings of this effect remain unexplored. Nevertheless, the study offers additional knowledge on the role of MCL-1 in human neural stem cells, whereas previous research mostly focused on cardiomyocytes or cancer cells.

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Referee #1

Evidence, reproducibility and clarity

Summary: This study claims that beyond its canonical anti-apoptotic function, MCL-1 has essential non-apoptotic roles in human neurodevelopment. Pharmacologic inhibition of MCL-1 in human neural stem cells disrupts mitochondrial inner membrane architecture by destabilizing cristae and the OPA1-MICOS complex, leading to swollen mitochondria with disorganized cristae. These structural defects impair fatty acid oxidation and lipid droplet homeostasis, linking cristae integrity to metabolic competence. Independently of apoptosis or proliferation, MCL-1 inhibition selectively depletes intermediate neural progenitors, indicating a direct role in lineage progression. Overall, the work positions MCL-1 as a key regulator of mitochondrial structure-metabolism coupling that instructs neural progenitor identity and human neurogenesis.

Overall: The study does a good job of using (in most assays) caspase inhibition (e.g., QVD treatment) to block apoptotic responses induced by MCL-1 inhibition. As a result, many of the phenotypes caused by inhibition are likely to be independent of caspase activation. As a result, this manuscript would be of interest to researchers that study the topics of the BCL-2 family and cell death signaling, mitochondrial bioenergetics and dynamics, neurodevelopment, and cellular metabolism. However, as currently presented the manuscript is only descriptive and lacks mechanistic insight.

Major Concerns:

1) The authors only use a single MCL-1 inhibitor and never use other non-targeting BH3-mimetics (such as venetoclax) as negative controls. This seems like a missed opportunity to demonstrate that the phenotypes observed are MCL-1 dependent.

2) There is no mechanism proposed in this study other than reliance upon QVD as not affecting the phenotypes. As submitted, the manuscript only can speculate that these phenotypes are due to non-apoptotic roles of MCL-1 inhibition. The authors have missed an opportunity to explore MCL-1's non-apoptotic functions directly.

Other concerns exist that weaken the impact of the study.

1. Figure 1 should include the fact that QVD inhibition (shown in Sup Fig 2) does not obviate the phenotype induced by pharmacological inhibition of MCL-1 on mitochondrial morphology.
2. Figure 2 would benefit from evidence that caspase inhibition does not repress the phenotype on mitochondrial cristae morphology (volume and area). Furthermore, the FIB-SEM data are very hard to appreciate as the size precludes visualization of individual mitochondria.
3. Figure 3 reports that MIC60 and OPA1 appear to be downregulated in response to MCL-1 inhibition, but these appear to be more significant only when QVD is added. Why would the phenotype be obscured in the non-QVD setting (Fig. 2B&C). How does MCL-1 inhibition lead to changes in MIC60/MICOS/OPA1? This seems quite preliminary at this point.
4. The loss of MIC60 and OPA1 should repress electron transport chain function, are such impacts observed in the cultured cells? This could be shown by assessing oxygen consumption, etc. Such data would enhance the authors' conclusion that MCL-1 inhibition leads to defects in mitochondrial physiology.
5. In Figure 4, the differences between transcripts (qPCR data) and protein (immunoblot) data are often confusing and not well explained. Why do the authors propose that mRNA expression is decreasing whereas the protein expression is increasing? Example CPT1. Furthermore, it is unclear what these data mean functionally? Is this reflective of enhanced lipid oxidation or simply a response to inhibition of fatty acid oxidation? Clarification of the impact of these findings is necessary.
6. The increase in lipid droplet number induced by MCL-1 inhibition has been previously documented, but it is unclear whether this increase is related to an inability to oxidize lipid (defective fatty acid oxidation) that leads to increases in the cellular abundance or whether this indicates that MCL-1 inhibition leads to enhanced storage. Do other inhibitors of fatty acid oxidation lead to similar increases in lipid droplet size and abundance? Does QVD inhibition affect this phenotype?
7. For Figure 6, while these data may be very meaningful, as presented they are very hard to appreciate. Insets that show the neuronal populations would help to convey the point that the differentiation is impacted. Also, are there other methods that could confirm these observations (qPCR to show changes in differentiation).
8. Figure 7 is also very hard to appreciate. What is the reader to see? Can these be quantified? It seems that QVD may be rescuing in this figure, does this suggest that MCL-1 inhibition might be inducing death. All of this needs to be quantified.
9. BCL-XL has also been implicated in affecting mitochondrial electron transport chain function (See PMID: 19255249, 21926988, 21987637). Can BCL-XL inhibitors affect any of the phenotypes associated here?
10. Please be carefully avoid using the term "MCL-1 loss", when talking about pharmacological inhibition. Only genetic ablation (e.g. knockout, silencing, etc.) should be termed loss.

Significance

The study advances in human cells the impacts of MCL-1 inhibition. They replicate many impacts previously observed in mouse systems and refine analyses to impacts on MICOS complex, lipid droplet storage, and neuronal differentiation. While these findings are important and would be well received by a wide audience, the study fails to provide almost any mechanistic insight into how these phenotypes are being induced. The only common theme is that blocking caspase activation in many assays fails to block the phenotype.

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Reply to the reviewers

Reviewer 1

Point

Summary

Response

1.1

Overall, the study lacks well-controlled experiments comparing hypoxia induced by DMOG with hypoxia induced by 1% O₂ for assessing ERα occupancy throughout.

To assess whether DMOG-induced changes in ERα occupancy reflect bona fide hypoxia, we measured ERα binding by ChIP-qPCR under 1% oxygen over 48 hours, compared to normoxic (21% oxygen) cells and input controls in matched cells at the GREB1 and TFF1 loci. Our findings demonstrate that 1% oxygen treatment recapitulates the ERα binding changes observed with DMOG, at the time points of our RNA-seq experiments.

We have included these results in __Figure 1F __of the preliminary revision of the manuscript.

1.2

Lack of evidence for other co-transcription factors impact under hypoxia HIF's in Fig1.

We thank the reviewer for this comment. We have clarified that motif enrichment analysis is included to characterise the sequence context of ERα binding sites and to confirm enrichment of known ER-associated motifs (e.g. EREs), rather than to infer functional involvement of additional transcription factors under hypoxia. Corresponding interpretative statements have been removed from the Results and restricted to the Discussion.

1.3

Lack of evidence for DMOG induce HIF protein expression in MCF7 cells.

To confirm DMOG induces HIF-protein expression we have analysed HIF1α and HIF2α protein levels by western blot. We have included these in __Supplementary Figure S1A __within the preliminary revision to address this concern.

1.4

Figure 1: ATAC-seq was performed under 1% O₂, whereas ChIP-seq was conducted with DMOG treatment, making these conditions not directly comparable.

We acknowledge that the ERα ChIP-seq (DMOG) and ATAC-seq datasets were generated under different conditions and are therefore not directly comparable. To address this, we have performed ChIP-qPCR under bona fide hypoxia (1% oxygen) at canonical ERα target loci (TFF1 and GREB1), demonstrating that the directionality of ERα binding changes observed with DMOG is recapitulated under physiological hypoxia. These data provide a direct comparison of ERα occupancy across conditions and support the use of DMOG as a proxy for hypoxia in our ChIP-seq experiments.

If requested, we are willing to perform ATAC-seq at 16 h under 1% oxygen. However, because the original dataset was generated under 0.1% oxygen, and canonical ERα-bound sites show minimal accessibility changes under severe hypoxia, we anticipate limited additional insight from repeating this experiment.

1.5a

Figure S1: ERα ChIP lacks estradiol (E2) treatment in MCF7 cells with or without DMOG.

The statement that the ERα ChIP samples lack estrogen treatment is incorrect. Estradiol was not an experimental variable and cells were intentionally maintained under estrogen-rich conditions to preserve tumour-relevant ERα activity.

We have now clarified within the preliminary revision by stating that cells were routinely cultured in “estrogen-rich Dulbecco’s Modified Eagle Medium” in the methods section, and clarified the use of estrogen-rich conditions in the Figure S1 legend.

1.5b

The single-gene examples of DMOG effects shown in Fig. S1A are not significant.

The peak illustrated in Figure S1A (now Figure S1D) __is intended to provide a visual confirmation of peak calling and enrichment patterns underlying the genome-wide redistribution observed in __Figure 1. The peak was called by the MACS2 pipeline (code available from https://doi.org/10.5281/zenodo.17221105) with a log10(q-value) = 268.5, which passes the MACS2 cut-off q

1.6a

Fig. S2 lacks 1% O₂ conditions,

We wish to clarify that Figure S2 (now Figure S4) serves as quality control specifically for the DMOG-treated ChIP-seq dataset presented in Figure 1C. The purpose of the plot is to visualize unfiltered motif enrichment to confirm that the identified peaks represent bona fide ERα binding events within the DMOG condition. Motif enrichment under a 1% oxygen environment would not provide this validation. In all cases the ERE is the most significantly enriched motif.

With respect to ERα binding under 1% oxygen, we have now assessed this via targeted ChIP-qPCR validation (Figure 1F).

1.6b

Fig. S3 lacks DMOG-induced HIF factor assessments.

The DMOG-induced changes in HIF1α and HIF2α expression are shown in the__ Figure S1__ of this revision proposal and have been incorporated into the manuscript as part of the changes described in response 1.3.

1.7a

Figure S4: Estradiol (E2) treatment is missing from the controls, and the figure labeling is of poor quality.

We have substantially improved the labelling of Figure S4, now__ Figure S6.__

Additionally, we have clarified that all samples were cultured in estrogen-rich media and treated with either vehicle control or 100 nM fulvestrant; thus estrogen is present in all conditions including the controls.

1.7b

Hypoxic conditions for assessing ER status and appropriate controls are also lacking.

We agree that monitoring ERα stability under hypoxic conditions is essential.

We provided a western blot assessment of ERα protein levels at 0, 8 and 48 hours of treatment with 1% oxygen or DMOG, compared to normoxic controls, included as Supplementary Figures S1B, C in the preliminary revision.

These demonstrate the cells remain positive for ERα protein expression at 0, 8 and 48h.

1.8

Figure S5: The description of fulvestrant treatments under hypoxic conditions is unclear.

We thank the reviewer for this comment. To clarify the experimental design, we now signpost the reader in the figure legend of Figure S5 (now S7) to the schematic diagram provided in Figure 3B, and provide a summary stating the experiment employed a factorial design combining a 96-hour fulvestrant treatment with exposure to 1% oxygen for the final 48 hours.**

1.9

Supplemental legends: These require major revision; they are of poor quality and lack statistical details and references to biological replicates.

We have extensively revised all supplementary figure legends to ensure clarity and precision.

1.10

Overall comparisons throughout the manuscript are weak; the figures appear sloppy and lack sufficient effort in presentation.

Following this comment, we carefully reviewed the presentation of all figures throughout the manuscript. We improved the organisation and labelling of the Supplementary Figures to facilitate clearer comparison of the data. In particular, full western blots are now clearly annotated and supplementary legends have been expanded to provide sufficient context for each figure to be interpreted independently.

1.11

i) In general, the manuscript in its present form does not greatly contribute from published work as the ERα cistrone is well documented work studied for its role in regulating gene expression, particularly in ERα-positive breast cancer.

ii) Additionally, a lack of a thorough comparison between DMOG and or 1 %oxygen induce hypoxia in the MCF7 ER+ model, diminished initial interest in the manuscript.

iii) The lack of considering estradiol exposure under hypoxic conditions with either 1%oxygen and or DMOG also limits relevance to patients with ER+ BrCa.

iv) The ERα epigenomic profile has been extensively studied including work under hypoxic conditions.

i) We respectfully disagree that the manuscript does not extend prior work. Despite extensive characterisation of ERα, its role in shaping hypoxia-driven transcription in ER+ breast cancer has not been defined. Here, we identify an ERα-dependent hypoxic response (EDHR), demonstrating a reciprocal interaction between hypoxia and ERα activity.

ii) In revision, we address concerns regarding DMOG by validating ERα binding under 1% oxygen using ChIP-qPCR thereby confirming our result in bona fide hypoxia. Additionally, all RNA-seq and functional assays, including ENaC targeting, were performed under 1% oxygen in the original manuscript.

iii) All experiments were conducted under estrogen-complete conditions, now explicitly clarified, reflecting tumour-relevant ERα activity.

iv) Together, these data establish a reciprocal interaction between ERα and hypoxia and uncover a targetable vulnerability in hypoxic ER+ breast cancer, linking transcriptional regulation to therapeutic opportunity.

Reviewer 2

No.

Summary

Response

General Comments

2.1

ENAC is proposed as a therapeutic vulnerability based on amiloride sensitivity assays. Additional experiments are required, such as western blot validation of ENaC regulation under hypoxia and loss-of-function approaches to assess its contribution to the phenotype.

We agree that further validation of ENaC involvement would strengthen this observation. We will assess ENaC protein levels under 1% hypoxia ± fulvestrant by western blot and perform siRNA-mediated depletion of ENaC subunits to test their contribution to the hypoxia-specific amiloride-sensitive phenotype by viability assay (see also response 3.3).

2.2

Fulvestrant is used to dissect ERa dependency. However, as a SERD, it may alter chromatin and transcription independently of a simple loss of ERα. Addition control would strengthen interpretation.

The experimental design already controls for potential fulvestrant-specific transcriptional effects, as all four conditions (± hypoxia, ± fulvestrant) were included. EDHR genes were defined based on induction under hypoxia, loss of this induction following ERα degradation, and absence of residual hypoxic induction in the presence of fulvestrant. Consistent with this, SCNN1B and SCNN1G do not show significant fulvestrant-responsive changes under normoxia (Figure 5C,D).

We also note that fulvestrant has been shown to induce minimal global chromatin remodelling (Guan et al., 2019), supporting its use to assess ERα dependency without broadly confounding chromatin accessibility; this reference is now included in the manuscript.

2.3

The molecular mechanism by which ERα modulates the hypoxic transcriptome, specifically how ERα and HIF pathways converge at ENAC loci should be more studied.

We further examined the potential convergence of ERα and hypoxic signalling at the ENaC loci (included as __Figure 5E __in the revision proposal) showing genome browser views of the SCNN1G and SCNN1B loci, highlighting hypoxia-induced HIF1α binding and ERα association at these sites.

To further support this, we will perform RT-qPCR validation of SCNN1G and SCNN1B expression following treatment ± IOX5 and ± fulvestrant. IOX5 is a selective PHD inhibitor that stabilises HIF proteins, enabling us to assess the contribution of HIF signalling independently of other oxygen-dependent effects associated with hypoxia.

2.4

In addition, to assess the relevance of this work for luminal breast cancer and ERα expression, specific validation in TNBC should be performed

To assess the clinical relevance of SCNN1B and SCNN1G in ER-positive and ER-negative subgroups, we performed Cox proportional hazards analyses in TCGA and METABRIC cohorts individually, including ER status and stratifying by ER-positive and ER-negative cases (Figure 6C). These analyses support the association of SCNN1G with poorer relapse-free survival specifically in ER-positive patients.

2.5

The authors should provide RT-qPCR validation of the key EDHR genes, especially since this signature is later used for downstream analyses.

We agree that independent validation would strengthen these findings. We will perform RT-qPCR validation of key EDHR genes (including SCNN1B and SCNN1G) under ± hypoxia and ± fulvestrant conditions to confirm ERα-dependent hypoxic induction.

Limitations

2.6

Reprogramming of the ERα cistrome under cellular stress is well documented. The study extends these ideas but does not clearly demonstrate a new mechanistic paradigm, particularly because the EDHR is defined primarily through omics approaches without strong mechanistic validation. In addition, we have to keep in mind that the study uses DMOG to model hypoxia-driven chromatin changes, but DMOG inhibits many 2-oxoglutarate-dependent dioxygenases non-selectively.

This makes it difficult to attribute ERα cistrome reprogramming specifically to hypoxia, rather than to broad off-target effects. The transcriptomic dataset is more convincing by need the validation suggested previously.

While ERα cistrome reprogramming has been described, our study demonstrates a reciprocal interaction in which ERα not only responds to hypoxia but actively shapes hypoxia-driven transcription, defining an ERα-dependent hypoxic response (EDHR).

We acknowledge the limitations of DMOG and have addressed this by validating key ERα binding events under bona fide hypoxia (1% oxygen) using ChIP–qPCR, confirming our findings under physiological conditions (response 1.1).

To further strengthen mechanistic insight, we will assess the requirement for HIF stabilisation using the selective PHD inhibitor IOX5, combined with RT-qPCR analysis of SCNN1G and SCNN1B ± IOX5 ± fulvestrant (response 2.3 and 2.5). In addition, we will validate the functional relevance of ENaC through protein-level analysis and siRNA-mediated depletion, as described in__ response 2.1.__

Together, these additions address concerns regarding DMOG specificity and provide further support for a functional interaction between ERα and hypoxic signalling.

Audience

2.7

Given its reliance on omics datasets and preliminary functional assays, the paper will likely appeal to a specialized audience in transcriptional regulation, hypoxia signalling, and ER+ breast cancer biology. However, the limited mechanistic depth and uncertain translational relevance due to the lack of in vivo validation, may reduce its impact for broader oncology or therapeutic-development audiences. Without stronger validation, the findings may be perceived as niche and mainly of interest to researchers focused on ERα chromatin dynamics rather than to the wider cancer research community.

The study incorporates multiple layers of human relevance, including spatial transcriptomic analyses demonstrating enrichment of EDHR within hypoxic tumour regions and survival analyses linking EDHR and ENaC expression to clinical outcome.

In revision, we address the reviewer’s concerns through targeted validation (ChIP-qPCR in hypoxia, western blotting, and RT–qPCR). Together, these additions strengthen the mechanistic and translational relevance of the study.

Reviewer 3

No.

Summary

Response

Major comments

3.1

The DMOG ChIP-seq provides a valuable first look at ERα redistribution. Since DMOG inhibits both HIF hydroxylases and oxygen-dependent demethylases, the driver of the observed changes remains ambiguous. It would help to include either ERα ChIP-seq under bona fide hypoxia or a selective PHD inhibitor condition (for example IOX5, as you discuss) to separate HIF stabilisation from broad demethylase inhibition. If ChIP-seq is not feasible, a brief ATAC validation at a small panel of gained and lost loci would still increase confidence.

We acknowledge that mimetics of hypoxia can introduce off-target effects. To address this, we have validated our ERα ChIP-seq findings using ChIP-qPCR at representative loci (TFF1 and GREB1), demonstrating consistent changes in ERα binding under bona fide hypoxia (1% oxygen) (now included in Figure 1F).

As acknowledged by the reviewer, ChIP-seq under these conditions is likely not feasible due to cell number constraints. We are willing to undertake ATAC-seq if required (as stated in response 1.1); however, we do not feel it would directly address ERα occupancy at these loci. We therefore consider our targeted ChIP-qPCR to be the most appropriate approach to validate ERα redistribution under hypoxia.

3.2a

The factorial RNA-seq is well designed and the attenuation analyses are clear. The EDHR selection is stringent and reproducible across two ER+ lines.

To support the claim of ERα dependence mechanistically, a small number of targeted perturbations would go far. For example,

i) confirm EDHR induction for SCNN1B and SCNN1G in hypoxia with and without fulvestrant by RT-qPCR

We agree that targeted validation would strengthen the mechanistic support for ERα dependence. We will perform RT-qPCR validation of SCNN1B and SCNN1G under hypoxia ± fulvestrant to confirm ERα-dependent hypoxic induction (see also response 2.5).

3.2b

ii) test whether short-term ERα knockdown reproduces the effect.

ERα dependency is already assessed through fulvestrant-mediated degradation within the factorial design, which provides a well-established and direct approach to evaluate ERα function. As EDHR genes are defined by loss of hypoxic induction following ERα degradation, this constitutes a robust assessment of ERα-dependent effects.

We will therefore focus on orthogonal validation through RT-qPCR (response__ 2.5__), together with additional mechanistic and functional analyses using IOX5 and ENaC perturbation (responses 2.1 and 2.3), rather than introducing an ERα knockdown approach, although we would consider this if required.

3.2c

iii) A complementary test with a HIF-1α or HIF-2α knockdown at one time point would help position EDHR relative to HIF.

This request aligns with point 2.3, which addresses the convergence of ERα and HIF signalling. While HIF knockdown under hypoxia would assess necessity, we will instead assess the contribution of HIF signalling using the selective PHD inhibitor IOX5, as this allows us to isolate HIF stabilisation from broader hypoxia-associated effects and avoids additional perturbation associated with transfection-based approaches. We will perform RT-qPCR analysis of SCNN1B and SCNN1G following treatment ± IOX5 ± fulvestrant to determine whether HIF stabilisation is sufficient to support ERα-dependent induction of EDHR genes.

3.3

The amiloride result is intriguing and consistent with a hypoxia-specific dependency. Because amiloride is pleiotropic, it would strengthen the conclusion to add one genetic and one pharmacological specificity control. A brief SCNN1B or SCNN1G knockdown in hypoxia should phenocopy the viability effect if ENaC contributes. In parallel, testing benzamil at sub-micromolar doses would provide a more ENaC-selective pharmacological readout. These can be performed in MCF7 and, resources permitting, in T47D.

To address the reviewer’s concern regarding pleiotropic effects, we propose (aligning with our__ response to 2.1__) to apply siRNA-mediated knockdown of SCNN1B and SCNN1G under hypoxia to determine whether this reproduces our observed viability effect, thereby providing direct evidence for ENaC involvement.

We agree that additional pharmacological validation could further support specificity, and would consider inclusion of a more ENaC-selective inhibitor if required.

3.4

The RFS associations for

SCNN1B and SCNN1G are compelling. It would be helpful to report whether the associations persist in a multivariable model that at least includes ER status, grade and nodal status where available, or to state clearly when this is not possible across merged datasets. Even a sensitivity analysis in TCGA with ER+ cases only would contextualise the hazard ratios.

We have analysed TCGA and METABRIC cohorts individually using Cox proportional hazards models, as this functionality is not available for merged datasets in KMplot. ER status was included in the models, and analyses were additionally stratified by ER-positive and ER-negative subgroups. The number of relapse events per subgroup is approximately 40; therefore, additional covariates such as grade and nodal status were not included given the limited number of events per model.

Within ER-positive patients, high SCNN1G expression is associated with poorer relapse-free survival (TCGA HR 1.45, p = 0.0027), while SCNN1B shows a similar trend that does not reach statistical significance. These analyses are presented in Figure 6C and in the results section of the preliminary revision, and support the findings from the Kaplan–Meier analysis.

3.5

The spatial association of EDHR with EMT hotspots is a nice piece of the story. A short clarification of how spot-level cell type composition was handled will help readers interpret proximity results. If cell type deconvolution scores are available in the source dataset, adding a sentence on whether EDHR enrichment tracks tumour epithelial content would be useful.

Spatial cell type composition and spot annotations were used as provided in the SpottedPy dataset, based on Cell2location-derived deconvolution scores and STARCH tumour annotations, without additional re-estimation.

To address the reviewer’s suggestion, we examined the relationship between EDHR enrichment and epithelial content and observed no significant correlation at the neighbourhood level.

These points have now been clarified in the manuscript.

3.6

Data processing for ChIP-seq and RNA-seq is documented and accessions are provided. The RNA-seq includes n=3 per condition, which is appropriate, and the correlation and LFC analyses are clearly presented. For the amiloride assay, the two-way ANOVA with interaction is appropriate; please add the exact n and whether experiments were independently repeated, and include the underlying values in a source table for transparency. These are small presentational edits rather than new experiments.

In the preliminary revision we have added a statement to the amiloride assay figure (Figure 6D) clarifying that n = 3 independent biological replicates were performed per condition. In addition, we now provide the underlying numerical values for this assay in Table S11.

3.7

A small, hypothesis-driven mechanistic link from EDHR to ENaC function would substantially elevate impact without becoming a long project. For example, testing whether hypoxia increases amiloride-sensitive Na⁺ current in MCF7 and whether fulvestrant abrogates that increase would directly connect the transcriptional and functional observations. If available, patch-clamp or a simple SBFI-based Na⁺ imaging readout could suffice.

We agree that directly linking EDHR to ENaC channel activity would further strengthen the mechanistic connection. We will prioritise genetic validation of ENaC function through siRNA-mediated depletion (response 2.1), which directly tests the requirement for ENaC in the hypoxia-specific viability phenotype.

We are willing to explore the feasibility of measuring the amiloride-sensitive Na+ currents under normoxia and acute hypoxia (via perfusion of cells with bathing solution bubbled with nitrogen during recording) ± fulvestrant to further connect hypoxic regulation to channel activity.

Minor Comments

3.8

Please show representative ERα ChIP-seq browser snapshots for at least one gained, one conserved and one lost locus alongside input for both conditions.

We have now included representative ERα ChIP-seq browser snapshots for gained, conserved, and lost loci, together with input controls for both conditions, in Figure S3 of the revised manuscript.

3.9

In Figure 1D, the ATAC-seq comparison uses 0.1% O₂ for 48 h while the RNA-seq uses 1% O₂. Briefly justify the choice and discuss any expected differences.

We thank the reviewer for this point. The ATAC-seq dataset was generated under 0.1% oxygen in the original study, whereas RNA-seq experiments in this work were performed at 1% oxygen to reflect tumour-relevant hypoxic conditions. The more severe hypoxia used for ATAC-seq would be expected to maximise detection of chromatin accessibility changes. Despite this, chromatin accessibility changes were limited, with ERα binding occurring predominantly at pre-accessible regions. This has now been clarified in the manuscript.

3.10

In the Methods for spatial analyses, specify the thresholds for hotspot calling and how the neighbourhood radius was chosen.

The neighbourhood parameter was set to 8, corresponding to the immediate neighbouring spots in Visium data, consistent with package guidance. We have clarified this in the manuscript text.

3.11

For the EDHR heatmap, consider marking the 14 consensus genes and indicating which belong to the ENaC module to aid readability.

We have marked the 14 EDHR consensus genes and indicated the ENaC module in the revised heatmap to aid readability.

3.12

Please report exact sample sizes and replicate numbers in all figure legends and provide a single table with all statistical tests, n, and p values.

We have reported exact sample sizes and replicate numbers in all relevant figure legends and included Table S11 summarising all statistical tests, sample sizes (n), and p values.

3.13

A schematic summarising the experimental timelines for ChIP-seq, RNA-seq and viability would help orient readers.

We have added timelines for these experiments as requested.

3.14

Minor copyedits: consistent formatting of O₂, gene symbols and reagent catalogue numbers.

We have standardised oxygen notation throughout the manuscript to use “oxygen” in the main text and “O2” where appropriate (e.g. figures).

Reagent catalogue numbers have now been standardised for consistency of presentation in the revised manuscript.

Gene and protein nomenclature were already formatted according to accepted conventions and were verified for consistency.

3.15

The manuscript is well referenced. Where you contrast your findings with long-term CoCl₂ hypoxia, a sentence on why acute DMOG and short-term 1% O₂ may reveal different ERα behaviours would help position the novelty.

We thank the reviewer for this suggestion. We have expanded the manuscript to clarify that acute hypoxia (1% oxygen) and DMOG treatment capture early, dynamic hypoxic responses, in contrast to chronic CoCl2 exposure, which reflects longer-term adaptation. This distinction is relevant to tumour biology, where hypoxia is often transient due to unstable vascularisation. The following statement has been added to the manuscript:

“In addition to such chronic hypoxic adaptation, tumour hypoxia can also be dynamic, with cells experiencing acute or transient hypoxic exposure due to unstable vascularisation; an established contributor to tumour progression (Liu et al, 2022a; Koh & Powis, 2012). Thus, in contexts where both signalling pathways remain active, the dependence of the hypoxic response on ERα in ER+ cells has not been previously characterised.”

Primary Limitations

3.16

DMOG vs hypoxia in the cistrome experiment,

To address concerns regarding the use of DMOG, we have validated key ERα binding events from the ChIP-seq dataset by ChIP–qPCR at the TFF1 and GREB1 loci under bona fide hypoxia (1% oxygen) in biological triplicate__ (Figure 1F)__. These data demonstrate consistent changes in ERα binding under hypoxia, supporting that the DMOG-induced redistribution reflects hypoxia-driven changes.

3.17

the absence of direct HIF or cofactor perturbations

We acknowledge the absence of direct HIF perturbation. To address this, we will assess the contribution of HIF signalling through stabilisation approaches, including RT-qPCR analysis of SCNN1B and SCNN1G ± IOX5 ± fulvestrant (response 3.2), to determine whether HIF activation is sufficient to support ERα-dependent induction.

3.18

and the pleiotropy of amiloride.

To address the potential pleiotropy of amiloride, we will perform siRNA-mediated knockdown of SCNN1G and SCNN1B to provide independent validation of ENaC-dependent effects (response 3.3).

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Referee #3

Evidence, reproducibility and clarity

Summary

This study explores how hypoxia reshapes ERα signalling in ER-positive breast cancer and whether this cross-talk exposes targetable vulnerabilities. The authors first map ERα binding in MCF7 cells after dioxygenase inhibition with DMOG and observe a genome-wide redistribution with enrichment of ERE, FOXA1 and AP-1 motifs at gained sites while chromatin accessibility at these loci appears unchanged in public ATAC-seq after hypoxia. They then perform RNA-seq in MCF7 and T47D using a factorial design that combines fulvestrant-mediated ERα degradation with 1% O₂ to define an ERα-dependent hypoxia response (EDHR). A 14-gene consensus EDHR signature includes ENaC regulatory subunits SCNN1B and SCNN1G, whose higher expression is associated with poorer RFS in ER+ cohorts. Functionally, amiloride increases viability in normoxia but reduces viability under hypoxia in MCF7 across a dose range. Spatial transcriptomics from ER+ tumours shows EDHR expression enriched at the margins of hypoxia and estrogen-hallmark regions and adjacent to EMT hotspots. Raw data and code availability are stated for the central datasets and accessions are provided. Together the results argue that ERα helps organise a distinct hypoxic programme and suggest a context-specific sensitivity to ENaC inhibition.

Major comments

The paper addresses a timely question with a clear narrative arc and brings together ChIP-seq, RNA-seq, pharmacology, survival analysis and spatial transcriptomics. The EDHR concept is interesting and the ENaC angle is original. The work is already strong and with a few targeted additions and clarifications it can be made more persuasive without becoming a new project.

1) The DMOG ChIP-seq provides a valuable first look at ERα redistribution. Since DMOG inhibits both HIF hydroxylases and oxygen-dependent demethylases, the driver of the observed changes remains ambiguous. It would help to include either ERα ChIP-seq under bona fide hypoxia or a selective PHD inhibitor condition (for example IOX5, as you discuss) to separate HIF stabilisation from broad demethylase inhibition. If ChIP-seq is not feasible, a brief ATAC validation at a small panel of gained and lost loci would still increase confidence. Estimated time: 6-8 weeks for a focused follow up with two conditions and biological duplicates/triplicates.

2) The factorial RNA-seq is well designed and the attenuation analyses are clear. The EDHR selection is stringent and reproducible across two ER+ lines. To support the claim of ERα dependence mechanistically, a small number of targeted perturbations would go far. For example, confirm EDHR induction for SCNN1B and SCNN1G in hypoxia with and without fulvestrant by RT-qPCR and test whether short-term ERα knockdown reproduces the effect. A complementary test with a HIF-1α or HIF-2α knockdown at one time point would help position EDHR relative to HIF. Estimated time: 3-4 weeks for qPCR and siRNA validations.

3) The amiloride result is intriguing and consistent with a hypoxia-specific dependency. Because amiloride is pleiotropic, it would strengthen the conclusion to add one genetic and one pharmacological specificity control. A brief SCNN1B or SCNN1G knockdown in hypoxia should phenocopy the viability effect if ENaC contributes. In parallel, testing benzamil at sub-micromolar doses would provide a more ENaC-selective pharmacological readout. These can be performed in MCF7 and, resources permitting, in T47D. Estimated time: 4-6 weeks.

4) The RFS associations for SCNN1B and SCNN1G are compelling. It would be helpful to report whether the associations persist in a multivariable model that at least includes ER status, grade and nodal status where available, or to state clearly when this is not possible across merged datasets. Even a sensitivity analysis in TCGA with ER+ cases only would contextualise the hazard ratios. Estimated time: 1-2 weeks.

5) The spatial association of EDHR with EMT hotspots is a nice piece of the story. A short clarification of how spot-level cell type composition was handled will help readers interpret proximity results. If cell type deconvolution scores are available in the source dataset, adding a sentence on whether EDHR enrichment tracks tumour epithelial content would be useful. Estimated time: 1 week.

Reproducibility and statistics

Data processing for ChIP-seq and RNA-seq is documented and accessions are provided. The RNA-seq includes n=3 per condition, which is appropriate, and the correlation and LFC analyses are clearly presented. For the amiloride assay, the two-way ANOVA with interaction is appropriate; please add the exact n and whether experiments were independently repeated, and include the underlying values in a source table for transparency. These are small presentational edits rather than new experiments.

Optional

A small, hypothesis-driven mechanistic link from EDHR to ENaC function would substantially elevate impact without becoming a long project. For example, testing whether hypoxia increases amiloride-sensitive Na⁺ current in MCF7 and whether fulvestrant abrogates that increase would directly connect the transcriptional and functional observations. If available, patch-clamp or a simple SBFI-based Na⁺ imaging readout could suffice. Estimated time: 6-8 weeks.

Minor comments

1. Please show representative ERα ChIP-seq browser snapshots for at least one gained, one conserved and one lost locus alongside input for both conditions.
2. In Figure 1D, the ATAC-seq comparison uses 0.1% O₂ for 48 h while the RNA-seq uses 1% O₂. Briefly justify the choice and discuss any expected differences.
3. In the Methods for spatial analyses, specify the thresholds for hotspot calling and how the neighbourhood radius was chosen.
4. For the EDHR heatmap, consider marking the 14 consensus genes and indicating which belong to the ENaC module to aid readability.
5. Please report exact sample sizes and replicate numbers in all figure legends and provide a single table with all statistical tests, n, and p values.
6. A schematic summarising the experimental timelines for ChIP-seq, RNA-seq and viability would help orient readers.
7. Minor copyedits: consistent formatting of O₂, gene symbols and reagent catalogue numbers.

Prior studies

The manuscript is well referenced. Where you contrast your findings with long-term CoCl₂ hypoxia, a sentence on why acute DMOG and short-term 1% O₂ may reveal different ERα behaviours would help position the novelty.

Significance

General assessment

The strongest aspects are the carefully designed factorial RNA-seq that cleanly separates ERα and hypoxia effects, the discovery of a concise EDHR signature reproducible across two ER+ lines, and the integration with spatial transcriptomics that places EDHR near EMT-rich tumour regions. The ENaC connection is new and potentially actionable, and the context-dependent amiloride response is a practical lead. Limitations are primarily mechanistic: DMOG vs hypoxia in the cistrome experiment, the absence of direct HIF or cofactor perturbations, and the pleiotropy of amiloride.

Advance

To my knowledge, this is the first description of a distinct ERα-dependent hypoxic programme in ER+ breast cancer that includes ENaC regulatory subunits and links to an EMT-adjacent spatial niche. The conceptual advance is the positioning of ERα as a coordinator of a subset of hypoxia-induced genes rather than as a parallel pathway, together with an initial functional readout that suggests a therapeutic angle through ENaC modulation. With the targeted additions outlined above, the study would move from strong association to a more mechanistic and translationally relevant model.

Audience

The work will interest a specialised audience in nuclear receptor biology, hypoxia signalling, tumour microenvironment, and ion transport in cancer. It has potential relevance for basic researchers studying ERα cistrome dynamics, for groups using spatial transcriptomics to define micro-niches, and for translational researchers exploring metabolic and ionic vulnerabilities in ER+ disease.

Expertise disclosure

Keywords: nuclear receptors,, chromatin profiling, transcriptomics, spatial transcriptomics, breast cancer biology.

I am not a domain expert in ion channel electrophysiology; my comments on ENaC pharmacology focus on specificity and study design rather than detailed channel biophysics.

Tone

I find the paper well conceived and already compelling. The suggested experiments are focused, realistic in scope, and primarily aim to turn several strong associations into concise mechanistic statements that would further increase confidence and impact.

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Referee #2

Evidence, reproducibility and clarity

ERα drives most luminal breast cancers. However, how hypoxia reshapes ERα activity and how ERα itself might influence the hypoxic response remain unclear. Understanding this interaction is crucial, as hypoxia is strongly linked to endocrine resistance and poor outcomes. In this study, authors investigated how hypoxia modifies ERα signalling in ER+ breast cancer and whether ERα contributes to the transcriptional response to low oxygen. Using MCF7 and T47D cells, they combined genome-wide profiling of the ERα cistrome under DMOG, hypoxic transcriptomics with or without ERα degradation, and spatial transcriptomics in tumours. This revealed an ERα-dependent hypoxic response (EDHR), prominently involving regulation of epithelial sodium channel (ENaC) subunits, whose expression requires both hypoxia and active ERα signalling. Functionally, ENaC inhibition with amiloride reduced cell viability under hypoxia. Together, these findings uncover a previously unrecognised ERα-dependent layer of the hypoxic transcriptome and identify ENaC as a potential therapeutic vulnerability in hypoxic ER+ breast cancer. Although the study is interesting, the manuscript lacks several essential functional and experimental validations. ENAC is proposed as a therapeutic vulnerability based on amiloride sensitivity assays. Additional experiments are required, such as western blot validation of ENaC regulation under hypoxia and loss-of-function approaches to assess its contribution to the phenotype. Fulvestrant is used to dissect ERa dependency. However, as a SERD, it may alter chromatin and transcription independently of a simple loss of ERα. Addition control would strengthen interpretation. The molecular mechanism by which ERα modulates the hypoxic transcriptome, specifically how ERα and HIF pathways converge at ENAC loci should be more studied. In addition, to assess the relevance of this work for luminal breast cancer and ERα expression, specific validation in TNBC should be performed Finally, the authors should provide RT-qPCR validation of the key EDHR genes, especially since this signature is later used for downstream analyses.

Significance

General assessment strengths:

This study uncovers a previously unrecognised ERα-dependent hypoxic response in breast cancer, revealing that ERα actively shapes the hypoxic transcriptome rather than functioning as an isolated pathway. To me, the main strength of this work is the identification of ENaC as a novel hypoxia-specific therapeutic vulnerability in ER+ breast cancer, suggesting that ion-channel regulation may play a broader and underappreciated role in endocrine resistance.

Limitation:

Reprogramming of the ERα cistrome under cellular stress is well documented. The study extends these ideas but does not clearly demonstrate a new mechanistic paradigm, particularly because the EDHR is defined primarily through omics approaches without strong mechanistic validation. In addition, we have to keep in mind that the study uses DMOG to model hypoxia-driven chromatin changes, but DMOG inhibits many 2-oxoglutarate-dependent dioxygenases non-selectively. This makes it difficult to attribute ERα cistrome reprogramming specifically to hypoxia, rather than to broad off-target effects. The transcriptomic dataset is more convincing by need the validation suggested previously.

Audience:

Given its reliance on omics datasets and preliminary functional assays, the paper will likely appeal to a specialized audience in transcriptional regulation, hypoxia signalling, and ER+ breast cancer biology. However, the limited mechanistic depth and uncertain translational relevance due to the lack of in vivo validation, may reduce its impact for broader oncology or therapeutic-development audiences. Without stronger validation, the findings may be perceived as niche and mainly of interest to researchers focused on ERα chromatin dynamics rather than to the wider cancer research community.

Expertise:

My evaluation is based on my background in breast cancer, ERα signaling and breast tumorigenesis. However, I have limited expertise in spacial transcriptomic analyses and advanced CHiP-seq bioinformatic analyses, which may affect my assessment of some computational analyses.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Malcom et al. present evidence that, under hypoxic conditions, hypoxia-inducible factors (HIFs) alter the estrogen receptor alpha (ERα) epigenomic landscape in a model of estrogen receptor-positive (ER+) breast cancer (BrCa). The response of ER+ BrCa to estradiol (E2) in MCF7 (ER+) cells, as well as ERα signaling in both primary and metastatic breast cancer, has been well studied, and the epigenomic landscape of ERα+ BrCa is well documented. The differentially expressed genes (DEGs) identified under treatment with the hypoxia mimetic dimethyloxalylglycine (DMOG) revealed a subset of ERα-dependent hypoxic response (EDHR) genes. The outcome was a reprogramming of the basal ERα cistrome, coinciding with sites enriched for estrogen response elements (EREs) and co-transcription factor binding motifs for ERα, including FOXA1 and AP-1. This was demonstrated by ERα ChIP-seq (i.e. DMOG) and ATAC-seq (i.e. 1% O2) performed under different hypoxic conditions. The transcripts identified following DMOG treatment were leveraged and compared to publicly available RNA-seq datasets from various breast cancer subtypes exposed to 1% hypoxic oxygen. Although the comparison methods varied, the results suggested that BrCa cell lines under 1% hypoxic oxygen conditions showed strong similarity to MCF7 cells treated with DMOG. Genes upregulated in response to DMOG correlated with poorer survival outcomes. To demonstrate the requirement for ERα in this model, MCF7 cells were treated with the selective estrogen receptor degrader (SERD) fulvestrant-the only FDA-approved SERD for ER+ BrCa-showing a dampening of the HIF response among EDHR genes. This suggests that ERα is necessary for the expression of DEGs under hypoxic conditions induced by DMOG. Finally, the sodium channel protein ENaC subunits (i.e., SCNN1B and SCNN1G) were further characterized as candidate EDHR genes. Analyses of publicly available datasets indicated that high mRNA expression levels of these subunits were associated with worse survival outcomes, supporting the clinical relevance of EDHR genes SCNN1B and SCNN1G. To further validate clinical relevance, utilize the Spatial Transcriptome in a small subset of ER+ BrCa.

Major:

1. Overall, the study lacks well-controlled experiments comparing hypoxia induced by DMOG with hypoxia induced by 1% O₂ for assessing ERα occupancy throughout.
2. Lack of evidence for other co-transcription factors impact under hypoxia HIF's in Fig1.
3. Lack of evidence for DMOG induce HIF protein expression in MCF7 cells.
4. Figure 1: ATAC-seq was performed under 1% O₂, whereas ChIP-seq was conducted with DMOG treatment, making these conditions not directly comparable.
5. Figure S1: ERα ChIP lacks estradiol (E2) treatment in MCF7 cells with or without DMOG. The single-gene examples of DMOG effects shown in Fig. S1A are not significant.
6. Figures S2 and S3: Fig. S2 lacks 1% O₂ conditions, and Fig. S3 lacks DMOG-induced HIF factor assessments.
7. Figure S4: Estradiol (E2) treatment is missing from the controls, and the figure labeling is of poor quality. Hypoxic conditions for assessing ER status and appropriate controls are also lacking.
8. Figure S5: The description of fulvestrant treatments under hypoxic conditions is unclear.
9. Supplemental legends: These require major revision; they are of poor quality and lack statistical details and references to biological replicates.

Minor:

1. Overall comparisons throughout the manuscript are weak; the figures appear sloppy and lack sufficient effort in presentation.

Significance

In general, the manuscript in its present form does not greatly contribute from published work as the ERα cistrone is well documented work studied for its role in regulating gene expression, particularly in ERα-positive breast cancer. Additionally, a lack of a through comparison between DMOG and or 1 %O2 induce hypoxia in the MCF7 ER+ model, diminished initial interest in the manuscript. The lack of considering estradiol exposure under hypoxic conditions with either 1%O2 and or DMOG also limits relevance to patients with ER+ BrCa. The ERα epigenomic profile has been extensively studied including work under hypoxic conditions.

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Reply to the reviewers

We sincerely appreciate the constructive and insightful comments on our manuscript.

Both reviewers raised important concerns regarding our use of the term lysosome-related organelle. We fully acknowledge this criticism and will revise the terminology throughout the manuscript with greater care, referring to these structures as Rab32/Rab38-positive vacuoles where appropriate, and discussing their possible relationship to lysosome-related organelles in the Discussion.

We believe that the remaining comments can be adequately addressed through additional experiments, including CLEM and three-dimensional reconstruction analyses. We therefore submit this revision plan and hope that it will be viewed favorably.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript employs overexpression and knockdown experiments in an immortalized hepatocyte cell line to probe roles for RAB32 and RAB38 in lipid metabolism by lysosomes or lysosome-related organelles (LROs). Using these approaches, the authors show that both RAB32 and RAB38 colocalize with LAMP1 on late endosomes/ lysosomes, that the appearance of enlarged, round lysosomal structures that they refer to as LROs scales with both RAB32 and RAB38 expression, and they provide some evidence to suggest that material from lipid droplets (LD) are taken up into these large rounded compartments in a manner that requires RAB32 or RAB38. Additional experiments are interpreted to suggest that macroautophagy is not required for this uptake but that PtdIns3-kinase, PtdIns5-kinase, and ESCRT complexes are required. Analyses of Rab32/Rab38 knockout mice shows an accumulation of white fat, and in liver an accumulation of what the author interpret to be lipofuscin. The authors conclude that lipid droplets are consumed by LROs in an autophagy-independent manner.

Major Comments:

While the topic of the paper is interesting, the conclusions of the paper are not supported by the data shown. No evidence is presented in this paper that the structures analyzed are actual LROs rather than lysosomes, other than their content of RAB32 and RAB38 - which are not limited in expression to LROs. The fact that lipid accumulates in the white fat and not the livers of double knockout mice and that hepatocytes express very little RAB32 and no RAB38 renders the model cell system studied here artifactual; the paper should start with the in vivo analysis and then progress with an appropriate cell type using a line that mimics the behaviour of the endogenous cells. Moreover, the only experiments documenting partial overlap of lipid droplet (LD) material - interpreted as uptake of LDs - into these structures is in cells that massively overexpress LAMP1-mRFP, RAB32, and/or RAB38; in untransduced cells, only a handful of LAMP1-containing structures are enlarged and there is no evidence that they overlap with LD material. Moreover, the only evidence that colocalization is independent of autophagy is that it is blocked by overexpression of a single dominant-negative autophagy component, ATG4B. Finally, the data quantification throughout the paper lacks sufficient power to support the conclusions. Thus, the none of the major conclusions from this paper are well supported, and the physiological significance of the observations for liver function is not at all clear. Altogether, the authors present an interesting idea for which the data are unconvincing.

Below are detailed concerns throughout the paper.

1. Abstract:

i. Please explain why there was a reason to look at the involvement of Rab32/38 in hepatic lipid metabolism.

ii. It seems rather unlikely that microautophagy can result in the engulfment of an entire lipid droplet in toto; is it more sensible to think of this as a means to transfer the contents of LDs, perhaps piece by piece, into lysosomes? 2. Introduction:

i. There is a vast literature on the roles of Rab32 and/or Rab38 in the biogenesis of other LROs besides melanosomes, including platelet granules, lamellar bodies in lung epithelial type II cells, and various non-vertebrate structures that should be cited.

ii. The authors fail to cite the first papers describing roles of Rab32 or Rab38 in bacterial killing by macrophages (Spano et al 2012, PMID: 23162001 and several additional papers from the Galan/ Spano groups), and papers ascribing roles for Rab32 in mitophagy and perhaps other mitochondrial functions, including ER:mitochondrial contacts, prior to the authors' 2025 paper (various papers).

iii. There have been quite a few papers addressing Rab32/38 effectors in pigment cells (see papers from the Di Pietro group) and other cell types (see Rab32 in mitochondria papers).These facts and at least some of the papers should be cited in the Introduction to better reflect the depth of understanding - and some of the confusion - surrounding Rab32 and Rab38 function.

iv. Reference to the definition of LROs should also be cited.

Results: 3. In all experiments where quantification was done, the number of structures or cells analyzed is listed but not the number of experiments. Were these experiments repeated at least three times, and are the values and statistics calculated from the experiment to experiment variation? If not, the statistical values are inaccurate. In all, the number of structures or cells analyzed appears to be quite small. 4.Figure 1.

i. How did the authors validate the specificity of the anti-Rab32 and anti-Rab38 antibodies used in Figure 1 and elsewhere? Data should be shown with individual knockdowns. Additionally, the overlap with LAMP1 seems too good to be true (it looks 100% and with similar labeling intensities in all cases) - were controls done to ensure lack of cross-reactivity of the secondary antibodies?

ii. If anti-Rab32 and -Rab38 actually labeled all LAMP1-positive compartments, it seems likely that these are classical late endosomes/ lysosomes and not lysosome-related organelles. Rab32 is expressed by many cell types that do not harbor traditional LROs and may have more ubiquitous functions. The larger ring-like structures mentioned in the text only appear when Rab32 or Rab38 are overexpressed as GFP fusion proteins (compare Fig. 1A and B with 1C-F, and note that the scale bars are the same) and fail to overlap with smaller structures only when LAMP1-mRFP is overexpressed (compare Fig. 1A and B with S1A); these structures likely represent earlier endosomal intermediates illuminated by LAMP1 overexpression. The authors need to reconsider their interpretation of these data in light of these overexpression artifacts.

iii. In Fig. 1C-F and Fig. S1, were cells transfected or infected with recombinant lentiviruses? This should be indicated in the figure legend. 5. Figure 2. In Fig. 2E-G, cells depleted of Rab32 and/or Rab38 should be compared to cells transduced with a control shRNA, such as a non-coding shRNA, and not to untransduced cells. The quantification of these data "per field" is quite concerning, given that a field could have very different numbers of cells. The data should be normalized to cell number or cell area. 6. Figure 3.

i. It should be noted in the text that the Lipi- dyes fluoresce in high hydrophobic environments, and thus would indicate a cluster of lipid tails within a lysosome and not just an entire LD. Interpreting these spots as LD under lipase inhibitory conditions is a stretch.

ii. The evidence that the Lipi-Blue labeled structures are actually inside of the lysosomal structures is not convincing. Three-D reconstructions would need to be done to be more convincing of this. 7. Suppl. Fig. S2. In panel A, there is no obvious difference in intensity of p62 under any of the conditions, and this reviewer does not see any LC3-II in the gel- only LC3-I with a very slight smear underneath that may or may not be specific. The interpretation that autophagy is increased at higher confluency is thus not well founded. In panel B, I see weak labeling of the interior of the giant Rab38-GFP-containing compartments for LC3-mRFP, as if the mRFP was in the process of degradation. How this correlates with the biochemistry in panel A is unclear. 8. Fig. 4 and Suppl. Fig. S3.

i. All of the graphs in Fig. S3 require appropriate statistical analyses.

ii. The interpretation of the size of the structures in the double DKD sample is complicated by their accumulation in the perinuclear area, which is very dense. If all samples look like the one in Fig. 3A, then it is not possible to measure their size by this technique and that sample should remain unanalyzed. It is misleading to refer to these as large when they appear to be clusters of small puncta.

iii. The label on the image itself in Fig. 3C should indicate Lysotracker, not "LRO". This is misleading.

iv. The same concern raised above that it is not clear whether the Lipi-Blue labeled structures are present within the lysosomal structures is true here. Indeed, in the unstransfected control, many of the LD structures appear to be present adjacent to (on one side of) the Lysotracker-labeled structures, as is also apparent in the shRab32 and shRab38 cells; those where they appear to be inside might simply be above them in these non-super-resolution images. This is a great example of how it is necessary to do 3D reconstructions to fully determine whether the Lipi-Blue structures are engulfed by or adjacent to lysosomes.

v. Note, the LC3 flux experiment and identification of LC3-II and -I is correct in S4D, unlike the experiment in S2A. 9. Fig. 5. The data in Figure 5A are incorrectly interpreted. PtdIns3P or PtdIns(3,5)P2 are present only on the cytoplasmic leaflet of endosomes and lysosomes; if those membranes were to be internalized, the phosphate would be removed. Thus, the presence of signal on the inside of the lysosomal structures does not indicate the presence of PtdIns3P or PtdIns(3,5)P2; it represents likely free mCherry, or perhaps the full conjugate with 2XFYVE, that has been engulfed by the lysosome and is no longer bound to its ligand. The observation that the mCherry signal accumulates near the Lipi-Blue signal in orlistat-treated cells thus cannot be interpreted as an interaction of the phosphoinositide with the LD or its content phospholipids or acyl chains. The disappearance of a punctate 2XFYVE signal is expected upon treatment with a PI3kinase inhibitor since it eliminates the ligand, and the failure of Lipi-Blue to accumulate in lysosomes of inhibitor-treated cells could reflect just about any defect in endolysosomal maturation since PtdIns3P is required for the early to late endosome transition as well as for several aspects of late endosome and lysosome biology. All this experiment shows is that uptake of Lipi-Blue labeled structures into lysosomes requires endolysosomal maturation. The same goes for the shVps4 experiments in Fig. 5B, which are also less convincing of any phenotype, and Fig. S5.

Significance

Because the conclusions are not supported by the data shown and because the authors exploit an immortalized cell type that does not mimic the behavior of the endogenous cells, the significance of the work as presented is very low. If the conclusions were justified, the advance could potentially be conceptual in showing that RAB32 and RAB38 redundantly functionalize lysosomes in some cell types to metabolize lipids through a mechanism distinct from macroautophagy. Such an advance would be of broad interest to investigators interested in the functions of lysosomes and lysosome-related organelles, as well as membrane trafficking machinery. However, the authors are unfortunately a long way from such an advance.

My expertise is in the biogenesis of LROs, and I am considered a leading expert in the field. In my opinion, the authors require a functional readout unique to LROs to define the compartments shown as LROs. Otherwise, they might consider altering their language, abandon the LRO designation, and focus on mechanisms of fatty acid uptake promoted by RAB32 and/or RAB38 in appropriate cell types. Unfortunately, their own data show that the cell type used here is not such an appropriate cell type.

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Referee #1

Evidence, reproducibility and clarity

This study investigates the roles of Rab32 and Rab38 in hepatic lipid droplet metabolism. The authors propose that Rab32/38-positive lysosome-related organelles (LROs) mediate lipid droplet degradation through a mechanism independent of conventional macroautophagy. While the study addresses an interesting question, several conceptual and technical issues need to be addressed before the conclusions can be fully supported.

Major Concerns

1.The authors primarily define the Rab32/38-positive ring-like structures as "lysosome-related organelles (LROs)" based on their morphological characteristics and co-localization with LAMP1. However, this classification lacks biochemical validation. Would it be more appropriate to include a Lyso-IP assay to provide additional supporting evidence? 2.In hepatocytes, what is the operational definition of LROs? Beyond being "larger in size," how are these structures functionally distinguished from conventional lysosomes? If Rab32/38 defines LRO identity, why does GFP-Rab32/38 not co-localize with all LAMP1-positive structures (Figure S1A)? 3.In Figure 2A, the dextran pulse-chase experiment shows fluid-phase uptake into large vacuoles; however, dextran can enter any endocytic compartment after prolonged chase periods. What evidence supports that these structures are bona fide LROs rather than enlarged late endosomes or lysosomes resulting from long-term culture? What determines why only certain lysosomes become Rab32/38-positive? This heterogeneity is not explained. Does it imply that pre-existing lysosomes convert into LROs, or that LROs are newly formed under high-density stress? The developmental trajectory of these structures has not been explored. 4.The authors propose a microautophagy mechanism based on the "invagination-like" structures observed by light microscopy (Figure 3A). However, the resolution of light microscopy is insufficient to distinguish true membrane invaginations from lipid droplets that are closely apposed to, or partially wrapped by, the outer membrane of LROs in three-dimensional space. Would a CLEM experiment be necessary to confirm that lipid droplets are indeed located within the lumen of LROs, rather than in deep invaginations that remain connected to the cytosol? In addition, multilamellar membrane structures were observed after Bafilomycin A1 treatment (Figure 3A). Have these structures been validated by electron microscopy, or could they simply represent complex membrane infoldings within swollen lysosomes? The conclusions drawn from light microscopy alone appear somewhat insufficient. 5.The authors use ATG4B C74A overexpression to claim macroautophagy independence. However, while this mutant blocks LC3 lipidation, the study still lacks genetic evidence, such as ATG knockouts. In Figure S2B, the authors state that the "majority" of Rab38-positive LRO-associated lipid droplets are LC3-negative, but no quantitative data are provided. 6.The manuscript does not clearly distinguish the functions of Rab32 and Rab38. Although the authors describe these proteins as paralogs with overlapping roles, multiple data points indicate that they have differential effects on lipid droplet (LD) metabolism. Notably, Rab38-but not Rab32-significantly affects LD delivery to acidic compartments, exerts a stronger influence on LRO size, and responds more robustly to VPS4B perturbation. These observations suggest that Rab32 and Rab38 regulate distinct steps of LD metabolism rather than functioning redundantly. However, the manuscript does not clearly highlight these functional differences and lacks mechanistic validation. 7.Figure 5A shows that the PI3P probe (2×FYVE) forms ring-like structures inside or near the LRO membrane. However, LROs themselves are Rab5-negative (Figures 1C-E), and PI3P is typically generated by Vps34 on early endosomes. Where do these PI3P signals originate? Are they transported from other organelles, or is there a local PI3P-generating mechanism on the LRO membrane? If the latter, which kinase is responsible, and is Vps34 recruited to the LRO membrane? This issue is not discussed. If PI3P is indeed locally generated on LROs, it could represent a key feature distinguishing LROs from classical lysosomes.

Minor Concerns

1.The double-knockout mice exhibit obesity and fatty liver; however, Rab32 and Rab38 are expressed in multiple tissues. A whole-body knockout model cannot distinguish whether these effects are hepatocyte-autonomous or arise from contributions by adipose tissue or macrophages, emphasizing the need for liver-specific knockout animals or cell models. Serum TAG levels were unchanged, and the authors speculate that VLDL secretion may be impaired, but this was not directly tested. Furthermore, the authors do not address the observed sex-specific effects, which appear to be male-specific. 2.The concentration of Orlistat used is relatively high (50-200 μM) and may cause non-specific effects. Have dose-response experiments been performed, or have other LAL inhibitors (e.g., Lalistat) been tested? 3.LysoTracker reflects acidity rather than lysosome identity, and reduced acidification in DKD cells may affect co-localization analysis.

Significance

Assessment of Significance Overall Assessment

Strengths:

Conceptual novelty: Introduces lysosome-related organelles (LROs) into hepatic lipid metabolism, expanding the functional repertoire of Rab32/38 beyond pigment cells and macrophages.

Mechanistic exploration: Links LD uptake to PI3P/PI(3,5)P2 signaling and VPS4B, providing molecular handles for future studies.

In vivo validation: DKO mice show age-dependent obesity and HFD sensitivity, establishing physiological relevance.

Weaknesses:

Rab32 vs. Rab38 functions remain blurred: Data suggest differential roles (Rab38 in LD delivery, Rab32 in LD size regulation), but authors default to "redundancy" narrative.

Microautophagy evidence incomplete: Relies on light microscopy; EM/CLEM needed to confirm true internalization.

Model relevance unclear: High-confluence AML12 vacuoles lack clear physiological correlate in healthy liver.

Audience

Primary:

Lysosome biologists

Autophagy researchers

Lipid metabolism researchers

Secondary:

Cell biologists

Metabolic disease researchers

Geneticists

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

1) Summary

This study investigates the mechanochemistry of Arp2/3-mediated branched actin networks at the level of individual branch junctions under load. Using microfluidic single-filament/branch force assays (including constant-force flow and open-chamber imaging) the authors quantify debranching, re‑nucleation, and mother- vs daughter‑interface stability across nucleotide states of Arp2/3 (ADP-Pi, ADP, and an ADP-BeFx proxy for ADP-Pi). They further test effects by two branch regulators (GMF and cortactin). Key findings include: (i) ADP-Pi and ADP complexes share similar force dependence but differ markedly (~20×) in intrinsic dissociation rate; (ii) phosphate turnover on the Arp2/3 complex is rapid ii) affinity for Pi drops when Arp2/3 loses its daughter filament; (iii) quantification from model fits uncovers large stability differences between daughter and mother interfaces of the Arp2/3 complex; (iv) extraordinary high stability of ADP-Pi-like Arp2/3 on the mother filament; and (v) distinct effects of GMF and cortactin on force‑dependent stability. Overall, the work combines technically demanding measurements with mechanistic modeling to probe how nucleotide state and regulatory factors tune branch mechanics.

2) Major comments:

1. Low force kinetics and completeness of survival curves (Figure 1). "For all forces, the surviving curves exhibited a clear single exponential behavior...." While the data can be fitted to monoexponential decay curves, data at low forces is clearly incomplete. >90% of branches have not dissociated by the end of the experiment. For the particular data shown in 1C (F00nN, n=60 total branches) it means that the time information is coming from

Essential; experiment might already be performed. Otherwise straightforward to do (weeks time).

In figure 1B, we indeed show a Survival curve for ADP-Arp2/3 complex branch dissociation at 0 pN up to 900 seconds. As now shown in updated supp figure S2, the data was in fact acquired for at least 5000 seconds for ADP-Arp2/3 and ADP-Pi states (N=2 repeats for each condition, with n = 60 and 90 branches for ADP-Arp2/3 branches, and 90 and 132 branches for ADP-Pi-Arp2/3 branches). The debranching rates reported in the initial submission were already obtained by fitting the surviving curves over the whole duration of the experiments.

1. Stability Analysis (Figure 4). I can follow much of the arguments presented in the stability analysis of the daughter vs mother interfaces, which is in principle extremely interesting! However, there are some concerns here:

i) The authors emphasize the zero force ratio derived from fits (which is linked to the stability difference of the two interfaces in the absence of force) despite this being only weakly constrained by data. Intuitively in the model, the stability difference should grow to very large values as the re-nucleation ratio approaches 1 at low force. This combined with the noise in the data poses an issue in my opinion. Looking at the data and the error margin, I think that the authors cannot state with high confidence that there is a real difference between the relative stability of the daughter and mother interfaces between the two nucleotide states of the complex.

Essential; analysis and textual revision only

We thank the reviewer for this comment. The difference in stability between the two interfaces is strongly constrained by the shape of the branch renucleation ratio versus force curve, and its value at 0 pN. This is illustrated in the figure shown below (new Supp Fig. S8), showing the dissociation rates of the two interfaces (in 'dashed' and 'point-dashed' style) that contribute to the overall debranching rate in each nucleotide condition. Despite the limited force range at which we probed the debranching rate, the branch renucleation ratio curve informs us on which interface is the weakest, and how this evolves with force.

We have assessed the confidence intervals of the parameters obtained from the fits, taking into account the error bars on our experimental datapoints. It seems to indicate that the simultaneous fits of the debranching rate and the branch renucleation ratio curves indeed constrain the parameters quite strongly. These confidence intervals are now reported in the main text and in the summarizing table.

We have repeated branch renucleation experiments for ADP-BeFx- and ADP-Pi-Arp2/3 complex branches (see new figure 4C&D, and our response to the next point). We believe these new measurements allow a better assessment of the relative stability between the two interfaces for Arp2/3 complex branch junctions in the ADP-BeFx state.

Still, we agree with the reviewer that the dispersion of the experimental data does not allow us to have a strong confidence on the crossover force and relative stability difference of the interfaces. Therefore, we have slightly toned down the way we present and discuss the differences in stability when comparing the two nucleotide states.

ii) For ADP-Pi, the renucleation ratio essentially remains flat over the measured force range. Hence, the data can only provide little leverage to estimate both the zero force ratio and, more importantly, the differential distance to the transition state in the slip-bond model in my opinion, which will show in the crossover force. Consequently, the quoted ">100×" stability difference at F=0 and the crossover force >20pN are driven largely by extrapolation rather than direct constraint by data. Given the high number of free parameters in the model, I would anticipate that several crossover forces and differential distances might explain the data nearly equally well. Instead of loosely reporting exact number from fits, I would have hoped for some sort of sensitivity analysis, for instance relying on profile likelihoods. Also parameter values could be reported as bounds (e.g crossover force≫measured range) rather than precise point estimates. This issue re-occurs (albeit not as drastically) for the cortactin experiments (Figure 6).

Essential; analysis and textual revision only

As mentioned in our response to the previous point, we have repeated renucleation experiments for ADP-BeFx- (and also for Arp2/3 complex branches in the presence of 50 mM Pi) (see new figure 4C&D) to better characterize the differential distance between to the transition force. The crossover force for the ADP-BeFx state is now 13.5 pN and the ratio of the stability between the two interfaces is roughly 100 times.

We agree with the reviewer that the dispersion of the experimental data does not allow us to have a strong confidence on the crossover force and relative stability difference of the interfaces. We have thus toned down the way we report these values. We do believe though that the difference we report between the ADP and ADP-BeFx state appears to be significant and needs to be acknowledged.

As a side note, it has proven to be challenging to pull on branches at forces higher than 7 pN. To apply a large force on the branch junction, we need to have a high flow rate. In this case, it appeared that the height of the filaments (both mother and daughter filaments) above the surface seem to deviate from what we have established in our previous studies (Jegou et al, Nat. Comm. 2013 & Wioland et al, PNAS 2019). This may originate from the fact branched filaments have a more complex shape than an individual filament. Characterizing accurately the evolution of the branch height as a function of the flow rate and applied force would require quite extensive additional characterization, which, we believe, is beyond the current focus of this study on the stability of Arp2/3 complexes.

iii) One important expectation from the "two slip bond" model is that branch dissociation rates should not necessarily scale mono-exponentially as they mostly do over the accessible force range of the paper. However, once the "minor" pathway of dissociation from the mother starts to dominate at high forces, rates become more force sensitive. This is nicely recaptured by the model fits in Figure S6 but deserves some explanation in the text. Otherwise, people will simply remember the "ADP-Pi is 20-fold more stable than ADP at all forces" message.

Essential; textual revision only

We now have rephrased the key sentences (in the Abstract and Results sections) to more clearly state that the debranching rate is not increasing mono-exponentially with force.

In the Abstract: "Remarkably, we find that branch junctions are over 30-fold more stable when the Arp2/3 complex is in the ADP-Pi rather than ADP state, and that force accelerates debranching with similar exponential factors in both states."

In the Results section: "The debranching rate seems to increase exponentially with the applied pulling force, in the range of 0 to 6 pN (Fig. 1F; see more refined analysis below). This behaviour is predicted by the Bell-Evans model for a slip bond."

iv) One important prerequisite for the model is that isolated Arp2/3 complexes (without a daughter filament) should dissociate with equal rates from mother filaments at all flow rates. Since the Arp2/3 complex prefers mother filament curvature, forces experienced by the mother might change its off-rate. It would be good to refer to this assumption in the text and experimentally verify it. I could not find it in the paper nor in Ghasemi et al 2024.

Essential; simple experiment (a weeks time).

We thank the reviewer for this important comment.

First, we investigated whether the viscous drag force, applied on the ADP-Arp2/3 complexes which remain bound to mother filaments could affect their stability. We have performed branch renucleation experiments at different flow rates but with the same pulling force on branch junctions (average force 3.9 pN) by adapting the length of the daughter filament. As shown in new supp. figure S11 (shown below), we did not observe any significant differences between 'low' and 'high' flow rates. If the off-rate of the surviving Arp2/3 was significantly affected by the flow, this would have led to a variation of the renucleation ratio with the flow rate.

Second, we have investigated the impact of the tension experienced by the mother filament at the location of the branch junction for ADP-Arp2/3 complex branches, with the same pulling force on the branches (average 4.1 pN pulling force on branches). We have quantified the debranching rate from three groups of branches depending on their position along mother filaments. As shown in new supp. figure S12 (shown below), we can observe a small trend, where the debranching rate decreases with the tension on the mother filament at the branching point.

Doubling the tension on the mother filament from 15 to 30 pN decreases the debranching rate by a third. Though, pairwise logrank tests performed between the survival fractions of the three binned groups do not report any statistical significant difference (all p values > 0.05). One possible explanation for this is the height of the mother filament in the microfluidics flow that increases linearly from the anchoring point to the free barbed end. As a consequence the pulling force on the branches will be higher, as branches experience faster flows.

For these same groups, upon branch dissociation, all remaining-bound Arp2/3 complexes are exposed to the same flow rate; the branch renucleation ratios were similar. Thus branch renucleation ratio seems to not significantly depend on the tension experienced by the mother filament at the branching point.

Similarly, Pandit et al PNAS 2020, Extended figure S1, also reported no detectable impact of the mother filament tension on the debranching rate in their assay.

v) The force dependence of the branch re-nucleation rate (Fig 3D) has been measured previously by the same group (Ghasemi et al). While the data in the older paper has not been fitted by a model, the trend of the data in the previous paper looks conspicuously different. Are there any explanations for this? I speculate that it might be related to actin and ATP not being saturated (low-force re-nucleation rate rarely exceeds 80%) in Ghasemi et al., but it would be good to know what the authors think about this. Essential; textual revision only

This is a good point. We have plotted the data of the renucleation ratio from ADP-Arp2/3 complex from figure 1F of Ghasemi et al, Sc. Adv. 2024 (performed at 0.3 and 1 µM actin), together with the data of the current study from figure 4D (performed at 1.5 µM actin). We feel this comparison could be of interest to the readers, and have thus integrated it in the manuscript as new supp. figure S13 (shown below).

As expected, the branch renucleation ratio is lower with lower concentrations of actin. The experimental data points from Ghasemi et al are similarly well fitted by the branch renucleation function obtained for 1.5 µM multiplied by a scaling parameter, which reflects the fact that the branch renucleation ratio is actin concentration dependent (Fig. 6A in Ghasemi et al). This scaling parameter was the only free parameter of those fits.

Since the branch renucleation ratio depends on the actin concentration as follows, 0.97.kon.([actin] - Cc)kon.([actin] - Cc)+koffATP-Arp2/3 , with kon = 3.4 µM-1.s-1 and koff ATP-Arp2/3 = 0.66 s-1 from (Ghasemi et al. 2024), the scaling parameter obtained by the fits give estimates of the actin concentration in these experiments, of 0.6({plus minus}0.05) and 0.9({plus minus}0.2) µM for the experiments performed at 0.3 and 1 µM respectively in (Ghasemi et al. 2024).

1. Stability of the authentic ADP-Pi-Arp2/3 complex on the mother filament. The extraordinary stability of the isolated ADP-BeFx-Arp2/3 complex on mother filaments is surprising, especially considering that both ATP and ADP states are much more labile (Ghasemi et al 2024). I would recommend repeating this experiment in the authentic ADP-Pi state with labelled Arp2/3 complexes as a more direct readout, even if this would require working with very high phosphate concentrations.

Essential; simple experiment (a weeks time).

We have followed the recommendation of the reviewer and have performed new experiments using fluorescent Arp2/3 complexes for ADP, ADP-BeFx and ADP-Pi states, now displayed in new figure 5C (also shown below).

For fluorescent Arp2/3 complexes remaining bound to the mother filament, the Arp2/3 complex - mother filament interface is ~ 100 times more stable in the ADP-BeFx state (0.0046 s-1) compared to the ADP state (0.56 s-1). We also assessed the dissociation of surviving ADP-BeFx-Arp2/3 complexes using unlabelled Arp2/3 complexes (previously in figure 4B, repeated experiment shown in new supp. figure S10), which also indicates a remarkable stability.

The dissociation curve of surviving Arp2/3 complexes in the presence of 50 mM Pi and 200 µM ATP in solution reflects the mixture of Arp2/3 dissociating in the ADP/ATP state and ADP-Pi-Arp2/3 that can either dissociate in the ADP-Pi state or lose their Pi and dissociate in the ATP state. Despite the presence of 50 mM Pi, the rate at which ADP dissociates and ATP reloads rate is much faster than Pi binding. Fitting this survival curve with a function that accounts for the initial double populations and the evolution of the ADP-Pi population (see Methods) gives a good estimate of the Pi release rate.

OPTIONAL: Further, but beyond the scope of the present paper, would be titrating phosphate in these experiments, which would even allow the authors to independently verify the reduced Pi affinity for Arp2/3 in the mother filament. Of note, this affinity difference is needed to satisfy detailed balance in the reaction scheme (Fig 4 D)!

We thank the reviewer for this suggestion. High concentrations of phosphate in the buffer renders glass surfaces quite sticky in our assays. We've tried several different passivation strategies (BSA, PLL-PEG, K-casein, ...) but none gave satisfactory results. So titrating phosphate, by going beyond 50 mM phosphate, proved to be quite challenging.

Detailed balance, considering the two possible routes connecting the ADP-Pi-Arp2/3 complex branch junction state and the surviving ADP-Arp2/3 complex state, can be written as KPi rel.branch junction . Kdebranching ADP-Arp2/3 = KdebranchingADP-Pi-Arp2/3 . KPi rel.surviving Arp2/3.. Some of these affinity constants are not known, because of the inability to determine reverse reactions rates such as the rebinding of a daughter filament to a surviving Arp2/3. It is thus hard to determine how the affinity of Pi for Arp2/3 complex changes between Arp2/3 complexes at branch junctions and surviving Arp2/3 complexes on mother filaments.

While we cannot determine the affinity constant of Pi for a surviving Arp2.3 complex, our data indicates that the dissociation rate of Pi is higher from Arp2/3 complexes at branch junction (koff = 0.21 s-1) than from surviving Arp2/3 complexes (koff = 0.05 s-1). This unexpected finding indicates that surviving Arp2/3 complexes adopt a conformation where the nucleotides are readily exchanged, but where the 'back door' for Pi release is less open. We now discuss this point in our revised manuscript.

1. Importance of "surviving" ADP-Pi-Arp2/3 complexes. The authors show a) rapid turnover of Pi on the ADP-Arp2/3 complex in both branch- or mother filament-bound state and b) the lowered Pi affinity of the latter. Nonetheless, they emphasize the importance of long-lived "surviving" ADP-Pi bound complexes on the mother (even stated in the abstract). I understand that this fraction shows under some experimental conditions (BeFx), but unless I am missing something, most complexes should rapidly lose their phosphate and either exchange nucleotide or dissociate from the mother under physiological conditions. Please clarify or tone done.

Essential; textual revision only

We thank the reviewer for their remark. We have tried to clarify this aspect in the manuscript.

As shown now with the departure rate of fluorescent surviving Arp2/3 complexes together with branch renucleation data, we show that surviving ADP-Pi-Arp2/3 complexes are quite stable on mother filaments, because they detach and release their Pi slowly, such that branch regrowth will occur provided there is actin in solution. In the absence of actin monomers, as the reviewer correctly points out, the surviving ADP-Pi-Arp2/3 will predominantly release its Pi and thus become a surviving ADP-Arp2/3 complex. We have modified the text to avoid any confusion.

1. GMF mechanism. The authors claim that GMF "...accelerates the departure of the surviving Arp2/3 complex from the mother...". I assume that they infer this from decrease in the re-nucleation ratio. However, alternatively GMF could simply dwell on the complex, inhibiting re-nucleation without promoting dissociation from the mother. The authors should either monitor Arp2/3 dwell times directly to discriminate between these possibilities or be more cautious in their conclusions.

Essential; simple experiment (a weeks time) or textual revision.

In Ghasemi et al. Sci. Adv. 2024, we examined the departure of Arp2/3 from the mother filament after GMF-induced debranching using fluorescent Arp2/3. Most of the fluorescent Arp2/3 dissociated from mother filaments within the same frame as the branch, i.e. within 0.5 seconds after the debranching event, and none were visible after another second . This could be due to Arp2/3 departing with the branch or an accelerated departure after branch dissociation. In any case, this rules out the possibility that GMF would dwell on the surviving complex for a substantial amount of time without promoting dissociation from the mother.

In the present manuscript, we now show that increasing the ATP concentration 10-fold (from 0.2 to 2 mM) is sufficient to restore the branch renucleation ratio to its level without GMF. This shows that GMF does not cause Arp2/3 to leave with the branch, but rather that it (also) acts on the surviving Arp2/3 complex, in a way that is countered by high concentrations of ATP. More specifically, it suggests that GMF accelerates the departure of the surviving ADP-Arp2/3 complex, either directly and by hindering the reloading of ATP, and that GMF does not affect the surviving Arp2/3 complex once it has reloaded ATP.

We now discuss these two non-mutually exclusive possibilities for the accelerated dissociation of the surviving ADP-Arp2/3 complex in the manuscript.

6.Cortactin mechanism and the "leash model". I must say that the cortactin data are the most puzzling part of the paper and hard to reconcile with what we know from structure. I was hoping to find some of this resolved in the discussion. However, I do not understand the "leash model" in the discussion section for cortactin-mediated branch stabilization: "This would explain the observed increase in branch survival compared to the absence of cortactin. As the pulling force is increased, this rebinding mechanism becomes less efficient." According to my understanding of the data, this is opposite to what happens. Cortactin only stabilizes the labile interface at elevated forces! Some re-writing might help here.

Essential; textual revision.

We thank the reviewer for having us think more thoroughly about the model we initially proposed. We now believe that our 'leash' mechanism is not able to fully recapitulate our observations in a simple and satisfactory manner.

We now propose a much simpler model, where the binding of cortactin to the Arp2/3 complex at the branch junction simply changes the energy landscape of the Arp2/3-daughter interface without the need to invoke a rebinding of the daughter filament upon branch departure. We have updated our interpretation of the data in the Discussion section accordingly.

Overall, our results on the impact of cortactin on branch renucleation highlights a surprising behaviour that would require further investigation to fully decipher the underlying molecular mechanism.

3) Minor comments

Organization: - I do not want to impose on how to best tell the story, but I felt that Fig1 A-D and Fig 2 A-B belong to one logical unit (nucleotide dependence), whereas Fig 1 E-F and Fig 2 C belong to the other (Pi binding and exchange). Perhaps consider re-organizing to streamline presentation?

We thank the reviewer for their suggestion. We agree that it flows more naturally as suggested, and have made the changes! Thank you.

Semantics/Typos: - Abstract: „... ADP-Pi and ADP-Arp2/3 detach with the same exponential increase as a function of force...". Increase should refer to the dissociation rate, which should be added to the sentence.

We have corrected this.

Results page 8: "...and the majority of Arp2/3 complexes detach from the mother filament while remaining bound to the branch at the debranching time." "Branch" should likely be daughter here, as there is no branch after dissociation of either interface.

We have corrected this, thank you.

Results page 13: "Exposing ADP-BeFx-Arp2/3 complex branch junctions to a saturating amount of GMF...". It is strange to imply saturation, because GMF likely simply does not bind to the complex in this nucleotide state with appreciable affinity. Suggest to change to "high".

We have made the changes accordingly.

Discussion page 18: "Moreover, in mammalian Arp2/3, His80 in Arp3 (corresponding to His73 in mammalian actin) is not methylated, and corresponds to residue N77 in Arp3, which is also not modified." N77 likely belongs to Arp2?

We have made the changes accordingly.

Discussion page 19: "We showed that Pi affinity for Arp2/3 complexes at branch junctions is around 3.7 mM (Fig. 1), a value which lies within the reported 1-10 mM Pi concentration measured in the cytosol in different mammalian cell types". Notably, this is not too different from F-actin, which should be mentioned. By this measure alone, free inorganic phosphate could also directly regulate actin filament stability!

We now mention this and discuss that intracellular Pi can also impact actin filament nucleotide state.

Future interest (non essential): - It would be utterly exciting (but beyond current scope) to quantify how instantaneous debranching rates evolve for naturally aging branches starting from ATP-Arp2/3 complexes!

We thank the reviewer for this remark. It is indeed quite beyond the scope of the current study, as this would require a way to probe ATP-Arp2/3 complex branches while daughter filaments are still quite short (so pulling on them is difficult). An interesting alternative could be to use ATP analogs, such as App-NHp (aka AMP-PNP), to stabilize this state. However, some studies have mentioned that App-NHp is not very stable.

Significance

General assessment:

This is a compelling and carefully executed study that delivers a clear mechanistic framework for how Arp2/3 branch junctions fail and re‑form under load. The central strength is the tight integration of state‑of‑the‑art reconstitutions with careful and original kinetic analysis. The experimental design is elegant and experiments have been carried out to a masterful standard. The figures are clear, the statistics are appropriate with some exceptions as detailed above. There are very few labs in the world that could have achieved this feat!

A few aspects could be further strengthened, most notably the explanation and application of the "two slip bond" model as well as slightly more restraint in speculating around specific regulatory mechanisms. However, these are minor refinements that do not detract from the important contributions of the paper.

Overall, the clearly work merits publication with high priority after revision; most requested changes are textual/analytical with very few targeted experiments, which would substantially strengthen core claims.

We thank the reviewer for their positive evaluation of our manuscript. We hope that our responses to the detailed points above, along with the corresponding revisions of the manuscript, will alleviate their concerns.

Advance relative to prior literature: The major novel findings of the paper are already summarized above. There is some recent work done on the subject of branch mechanics by the authors (Ghasemi et al 2024, PMID: 38277459) and others (Pandit et al 2020 PMID: 32461373), but the focus of the present work is clearly unique and the there is plenty of novel insight.

Audience and impact: Primary audience: specialists in cytoskeleton dynamics, in vitro reconstitution single molecule biophysics, and mechanobiochemistry. Secondary: researchers in cell motility, morphogenesis and mechanobiology, physicists working on active matter and modelers studying force producing and load-bearing biopolymer networks. The results and analysis framework should inform quantitative models of branched network turnover under load and the interpretation of regulatory factor action in vivo and in cells.

Reviewer expertise: Actin dynamics; biochemical reconstitution; single molecule approaches; biophysics.

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

Xiao et al examine the molecular events occurring when Arp2/3 complex-mediated actin filament branches are removed from mother actin filaments. They do this using microfluidics assay with purified proteins combined with single filament TIRF imaging of branched actin filaments with distinct fluorescent labels. The contribution of different nucleotide states of Arp2/3 complex are tested in conjunction with the relationship force exerted on the branches and regulatory protein involvement from GMF and cortactin. The data seem comprehensive and highly quantified in response to concentration, force, fraction of branches and survival times and branching rates. They find that ADP-BeFx and high phosphate concentrations (leading to the ADP-Pi state) leads to a slower debranching rate at a given level of force applied. The ability to rapidly switch the buffer gives powerful information about response times of debranching compared with other actin remodelling events. They use renucleation experiments to determine that the previous debranching event most often occurs at the Arp2/3 complex/daughter interface, showing that filaments will be ready to re-branch in the stable ADP-Pi bound state. GMF addition allows debranching of the ADP state to occur at a lower force. Cortactin acts similarly to the ADP-Pi state to increase branch stability.

Specific comments

The pulling force on the branches seems to arise from different flow rates in the microfluidics. Viscous drag is mentioned and I can see there is methylcellulose in the buffer. It would be helpful to have the explanation of the conversion between flow and force, even if it has been standard in previous work.

We apologize if this was unclear: in microfluidics experiments, the buffer does not contain methylcellulose. Methylcellulose is only used for 'open chamber' experiments, where no force is applied to Arp2/3 branches, to maintain them in the TIRF field of excitation (Figure S2).

To better clarify the conversion between flow and force, we have rephrased and extended the Methods section to explain how the force on the branch junction is computed based on the local flow velocity and the length of the daughter filament.

Pg 5 - what was the motivation to titrate phosphate? It seems a stretch that intracellular Pi levels are tuning branching inside cells more than protein-mediated control (GMF or cortactin) - can the authors evidence this at all?

We are not claiming that the level of Pi plays a stronger regulatory role than proteins. We show that inorganic phosphate tunes the state of the Arp2/3 complex, which in turn modulates the action of regulatory proteins, such as GMF and cortactin.

Nonetheless, we do show that the contribution of inorganic phosphate is quite central as it can (1) strongly stabilize branch junctions (~30-fold decrease in the dissociation rate), and (2) tune the activity of GMF and cortactin on Arp2/3 complexes at branch junctions as well as on the 'surviving' Arp2/3 complexes that remain bound to mother filaments.

We thus titrated phosphate and found that its impact on Arp2/3 complex stability is significant in the range of Pi concentration that is explored in cells. For the sake of completeness, and following a comment from reviewer #1, we now also mention the affinity of Pi for actin subunits in filaments in the Discussion, and discuss the impact of intracellular Pi on actin itself.

Minor comments

• In the introduction, while the structural and mutagenesis evidence is clearly stated, in other cases a bit more detail would be helpful e.g. 'biochemical studies', which referred measurement of hydrolysis rates using radiolabelling

We have made changes to more precisely define which biochemical assays were used in previous studies.

• Page 3 Figures shouldn't be referenced in the introduction

We have removed the references to the figures from the introduction.

• Page 3 slip bond behaviour needs explanation

We now explain the concept when first using this concept in the manuscript, as follows: "The debranching rate seems to increase exponentially with the applied pulling force, in the range of 0 to 6 pN (Fig. 1F; see more refined analysis below). This behaviour of accelerated debranching with the increase of the applied force is similar to the 'slip bond' concept, as predicted by the Bell-Evans model of the force-dependent lifetime of the interaction between two proteins".

• Figure 1B seems to be a theoretical schematic which is superfluous

We suppose that the reviewer is actually referring to figure 3B of the initial manuscript, describing the energy potential of a molecular interaction as a function of the reaction coordinate. We agree with the reviewer that it is not absolutely required and we have removed it.

• Figure 4D is helpful, different weight lines might help even more to explain the dominant pathways

We have made modifications to the biochemical reaction scheme in this figure (now figure 5F in the revised version). We hope we succeeded in improving its readability. Since the different paths depend on mechano-chemical parameters, there is no real dominant pathway per se.

**Referee cross-commenting**

Rev1 sounds like the specialist here. I can't comment on their requests. Some similar points arise between the reviewers which need addressing.

Reviewer #2 (Significance (Required)):

Significance

Taking a look at references 16 and 19, I do not find it clear what is achieved differently in the current work compared to these papers and what agrees and what disagrees. If it's a species difference I might expect the two species would be analysed side-by-side in this paper.

We thank the reviewer for this important comment. The goal of our study was not to compare the behaviour of mammalian and yeast Arp2/3 complexes.

We now try to better explain that the motivation of the present work is to address how the nucleotide state of the Arp2/3 complex tunes actin branch mechanosensitive stability, and regulates interactions with well known Arp2/3 complex binding proteins. Most of the reactions are quantified here for the first time. Moreover, the experiments with branch junctions in different nucleotide states are done under controlled mechanical conditions, providing the first direct measurements of the force-dependence of the debranching reactions. Our detailed kinetic analysis of the full reaction scheme allows us to model the different binding interfaces of the Arp2/3 complex.

In addition, it is worth noting that:

1. Species matter and this is why ref 16 and 19 can give the impression to disagree on the ability to renucleate branches thanks to the stability of surviving Arp2/3 complexes on mother filaments.
2. In ref 16 (Pandit et al, PNAS 2020) species are mixed (yeast Arp2/3 and mammalian alpha actin from skeletal muscle), likely leading to a different behaviour compared to the only mammalian protein situation we examine in our current work. In particular, with mixed species one misses the ability to renucleate, as shown in our previous study Ghasemi et al (ref 19). However, since mixing species does not correspond to anything physiological, we do not think it is worth repeating these conditions alongside our experiments.
3. Further, the analysis carried out in ref 16 suffers from important limitations: the force was unknown (not calibrated) and the data was fitted by a model that compounded several reactions, providing only an indirect estimation of the rates, in particular at zero force. In contrast, we have worked with calibrated forces (including dedicated experiments at zero force) and we have carried out specific experiments to directly measure several rates.
4. In ref 19 (our earlier work) we did not investigate the impact of the nucleotide state of the branch junction at all, and we did not systematically measure the dissociation rates as a function of force. Contrary to Pandit et al, we directly measure the difference in branch stability at zero force between ADP and ADP-Pi states and show that the ~ 30 fold difference holds true at all probed forces. Last, the force dependence of the branch renucleation success rate gives us crucial information on which of the two Arp2/3 complex interfaces ruptures first.

I'm not understanding how the authors can distinguish effects of adding phosphate and BeFx on Arp 2 and 3 compared to effects on actin. Importantly, are possible accompanying changes in the actin filament a confounding factor?

We have checked that the nucleotide state (ADP-BeFx and ADP-Pi versus ADP) of the mother and daughter filaments have no impact on branch stability:

• In the experiments shown in figure 2F, where the buffer condition to which branches are exposed is quickly changed from phosphate buffer to buffer without phosphate, we observe a rapid change of branch stability. Actin subunits at the branch junction are in F-actin conformation according to recent cyroEM observations (ref. Chavani et al, Nat Comm. 2024; Liu et al, NSMB 2024). These actin subunits, initially in the ADP-Pi state, are expected to age and become ADP with a rate of ~ 0.007 s-1 (ie half-time of 100 s; ref. Jegou et al, PLoS Biology 2011, Ooosterhert et al, NSMB 2023), a much lower rate than the observed change of the debranching rate (0.21 s-1). This means that the debranching rate is independent of the nucleotide state of daughter and mother filaments.

• In new supp. Figure S4, we show that the debranching rate is similar for ADP-Arp2/3 complex branch junctions initiated from ADP- or ADP-BeFx-actin mother filaments.

• In new supp. Figure S9, we initially exposed branch junctions to a BeFx solution then monitored debranching and branch renucleation in our standard buffer (ie without BeFX or Pi). We observed multiple rounds of branch renucleation, the first with ADP-BeFx-actin daughter filaments, and the following with daughter filaments never exposed to BeFx. They all had the same debranching rates and renucleation success rates.

The paper is quite specialist to read and the advance appears to be incremental. My expertise is in molecular pathways to actin regulation outside the main area of the paper.

The results we present in this study are often unexpected, and some go counter long-standing assumptions. The regulation of Arp2/3-nucleated branches is of importance for the stability and the force-generating capabilities of many actin networks in cells. Last, most of the measurements that we present had never been done, mainly because experiments are difficult to achieve, and require specific tools to monitor several events while controlling the applied force.

We believe our results are of broad interest as they go counter long-standing assumptions. We have rewritten the text in several instances to convey our message more clearly.

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

Please find enclosed the review of the manuscript "Inorganic phosphate in Arp2/3 complex acts as a rapid switch for the stability of actin filament branches" by Xiao et al.

The authors provide a detailed investigation of how the nucleotide bound to the Arp2/3 complex affects branch stability under flow force. From a kinetic perspective, this is an elegant study with generally high-quality data, although some conclusions rest on assumptions rather than direct experimental evidence.

We thank the reviewer for their positive feedback. We have improved our manuscript and performed important additional experiments to provide more direct experimental evidence of our conclusions.

A key question concerns the physiological relevance of these findings. For instance, the concept of branch regrowth may not be applicable in cellular contexts, since forces by actin polymerization would displace existing branches away from sites where they generate this active forces. The authors should clarify the relevance of regrowth during active force generation by branched networks.

We thank the reviewer for this comment. Our in vitro results indeed point to a previously unreported property of branched actin networks, i.e. the ability of Arp2/3 complexes to readily renucleate branches in the ADP-Pi state and that it does require reloading ATP within Arp2/3.

Branched actin networks, especially the lamellipodia or endocytotic patches, do exert active force thanks to actin polymerization of the individual branches at the forefront. Though, the whole actin network is exposed to stress, and the architecture of the network (inter-branch distance, crosslink between branches, ...) presumably strongly impact its mechanical properties.

In the case of other types of branched actin networks, such as the actin cortex, myosin motor put the whole network under tension. Such pulling forces on actin branches, depending on the amplitude of the pulling force, can lead to branch regrowth, and network self-repair.

We have modified the text to make the physiological relevance clearer.

Additionally, all experiments employ flow conditions that branches would probably not experience in cells-notably, the flow direction in the cellular context would be reversed. Altering the flow direction relative to the branches could affect not only the relationship between flow rate and branch stability, but potentially other system properties as well.

We agree with the reviewer that in cells branches will not experience flow conditions similar to the ones we use in our in vitro assay. Nonetheless, in cells we expect mechanical stress on the branch junction to be applied in all directions. In lamellipodia, the compressive force applied at the leading edge is expected to result in diverse local orientations of the force on individual branch junctions within the network (as explained in Lappalainen et al. Nat Rev MBC 2022). Also, branch junctions are found in the cell cortex, where they are exposed to pulling forces resulting from the action of myosin motors and crosslinkers on mother and daughter filaments.

This impact of the direction of the flow was addressed in our previous publication (Ghasemi et al, Sc. Adv. 2024, figure 2) and, to a lesser extent, by the lab of Enrique de la Cruz in Pandit et al, PNAS 2020 (ref. 16). We reported that flow direction has a minimal effect, if any, on branch dissociation rate and renucleation ratio.

Reviewer #3 (Significance (Required)):

Furthermore, the study appears not to account for the mother filament (particularly its nucleotide state) or the actin subunit bound to the Arp2/3 complex. The authors should discuss why their interpretation focuses exclusively on the Arp2/3 complex rather than on the actin filaments or Arp2/3-bound actin subunit.

We have checked that the nucleotide state (ADP-BeFx and ADP-Pi versus ADP) of the mother and daughter filaments has no impact on branch stability :

• In the experiments shown in figure 2F, where the buffer condition to which branches are exposed is quickly changed from phosphate buffer to buffer without phosphate, we observe a rapid change of branch stability. Actin subunits at the branch junction are in F-actin conformation according to recent cyroEM observations (ref. Chavani et al, Nat Comm. 2024; Liu et al, NSMB 2024). These actin subunits, initially in the ADP-Pi state, are expected to age and become ADP with a rate of ~ 0.007 s-1 (ie half-time of 100 s; ref. Jegou et al, PLoS Biology 2011, Ooosterhert et al, NSMB 2023), a rate much lower than the observed change of the debranching rate (0.21 s-1). This means that the debranching rate is independent of the nucleotide state of daughter and mother filaments.

• In new supp. Figure S4, we show that the debranching rate is similar for ADP-Arp2/3 complex branch junctions initiated from ADP- or ADP-BeFx-actin mother filaments.

• In new supp. Figure S9, we initially exposed branch junctions to a BeFx solution then monitored debranching and branch renucleation in a regular buffer. We observed multiple rounds of branch renucleation, the first with ADP-BeFx-actin daughter filaments, and the following with daughter filaments never exposed to BeFx. They all had the same debranching rates and renucleation success rates.

An important concern involves the use of KPi (inorganic phosphate). Based our experience, KPi appears to have effects beyond simply impacting nucleotide state-actin filaments seem to assemble differently in the presence of KPi. The authors should exercise caution in their interpretation of KPi-based experiments.

Concentration of KPi (up to 50 mM Pi) did not slow down barbed end elongation rate in our experiments.

Overall, while the technical quality and kinetic analyses are state-of-the-art, relating this work to physiological contexts remains challenging, and some conclusions appear overstated.

We have made changes in the discussion to try to more clearly relate our in vitro observations and conclusions with the cellular context where branch renucleation could have a strong impact on the architecture and mechanics of actin networks.

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

Please find enclosed the review of the manuscript "Inorganic phosphate in Arp2/3 complex acts as a rapid switch for the stability of actin filament branches" by Xiao et al.

The authors provide a detailed investigation of how the nucleotide bound to the Arp2/3 complex affects branch stability under flow force. From a kinetic perspective, this is an elegant study with generally high-quality data, although some conclusions rest on assumptions rather than direct experimental evidence.

A key question concerns the physiological relevance of these findings. For instance, the concept of branch regrowth may not be applicable in cellular contexts, since forces by actin polymerization would displace existing branches away from sites where they generate this active forces. The authors should clarify the relevance of regrowth during active force generation by branched networks.

Additionally, all experiments employ flow conditions that branches would probably not experience in cells-notably, the flow direction in the cellular context would be reversed. Altering the flow direction relative to the branches could affect not only the relationship between flow rate and branch stability, but potentially other system properties as well.

Significance

Furthermore, the study appears not to account for the mother filament (particularly its nucleotide state) or the actin subunit bound to the Arp2/3 complex. The authors should discuss why their interpretation focuses exclusively on the Arp2/3 complex rather than on the actin filaments or Arp2/3-bound actin subunit.

An important concern involves the use of KPi (inorganic phosphate). Based our experience, KPi appears to have effects beyond simply impacting nucleotide state-actin filaments seem to assemble differently in the presence of KPi. The authors should exercise caution in their interpretation of KPi-based experiments.

Overall, while the technical quality and kinetic analyses are state-of-the-art, relating this work to physiological contexts remains challenging, and some conclusions appear overstated.

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

Xiao et al examine the molecular events occurring when Arp2/3 complex-mediated actin filament branches are removed from mother actin filaments. They do this using microfluidics assay with purified proteins combined with single filament TIRF imaging of branched actin filaments with distinct fluorescent labels. The contribution of different nucleotide states of Arp2/3 complex are tested in conjunction with the relationship force exerted on the branches and regulatory protein involvement from GMF and cortactin. The data seem comprehensive and highly quantified in response to concentration, force, fraction of branches and survival times and branching rates. They find that ADP-BeFx and high phosphate concentrations (leading to the ADP-Pi state) leads to a slower debranching rate at a given level of force applied. The ability to rapidly switch the buffer gives powerful information about response times of debranching compared with other actin remodelling events. They use renucleation experiments to determine that the previous debranching event most often occurs at the Arp2/3 complex/daughter interface, showing that filaments will be ready to re-branch in the stable ADP-Pi bound state. GMF addition allows debranching of the ADP state to occur at a lower force. Cortactin acts similarly to the ADP-Pi state to increase branch stability.

Specific comments

The pulling force on the branches seems to arise from different flow rates in the microfluidics. Viscous drag is mentioned and I can see there is methylcellulose in the buffer. It would be helpful to have the explanation of the conversion between flow and force, even if it has been standard in previous work.

Pg 5 - what was the motivation to titrate phosphate? It seems a stretch that intracellular Pi levels are tuning branching inside cells more than protein-mediated control (GMF or cortactin) - can the authors evidence this at all?

Minor comments

• In the introduction, while the structural and mutagenesis evidence is clearly stated, in other cases a bit more detail would be helpful e.g. 'biochemical studies', which referred measurement of hydrolysis rates using radiolabelling
• Page 3 Figures shouldn't be referenced in the introduction
• Page 3 slip bond behaviour needs explanation
• Figure 1B seems to be a theoretical schematic which is superfluous
• Figure 4D is helpful, different weight lines might help even more to explain the dominant pathways

Referee cross-commenting

Rev1 sounds like the specialist here. I can't comment on their requests. Some similar points arise between the reviewers which need addressing.

Significance

Taking a look at references 16 and 19, I do not find it clear what is achieved differently in the current work compared to these papers and what agrees and what disagrees. If it's a species difference I might expect the two species would be analysed side-by-side in this paper.

I'm not understanding how the authors can distinguish effects of adding phosphate and BeFx on Arp 2 and 3 compared to effects on actin. Importantly, are possible accompanying changes in the actin filament a confounding factor?

The paper is quite specialist to read and the advance appears to be incremental. My expertise is in molecular pathways to actin regulation outside the main area of the paper.

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

This study investigates the mechanochemistry of Arp2/3-mediated branched actin networks at the level of individual branch junctions under load. Using microfluidic single-filament/branch force assays (including constant-force flow and open-chamber imaging) the authors quantify debranching, re‑nucleation, and mother- vs daughter‑interface stability across nucleotide states of Arp2/3 (ADP-Pi, ADP, and an ADP-BeFx proxy for ADP-Pi). They further test effects by two branch regulators (GMF and cortactin). Key findings include: (i) ADP-Pi and ADP complexes share similar force dependence but differ markedly (~20×) in intrinsic dissociation rate; (ii) phosphate turnover on the Arp2/3 complex is rapid ii) affinity for Pi drops when Arp2/3 loses its daughter filament; (iii) quantification from model fits uncovers large stability differences between daughter and mother interfaces of the Arp2/3 complex; (iv) extraordinary high stability of ADP-Pi-like Arp2/3 on the mother filament; and (v) distinct effects of GMF and cortactin on force‑dependent stability. Overall, the work combines technically demanding measurements with mechanistic modeling to probe how nucleotide state and regulatory factors tune branch mechanics.

Major comments:

1. Low force kinetics and completeness of survival curves (Figure 1). "For all forces, the surviving curves exhibited a clear single exponential behavior...." While the data can be fitted to monoexponential decay curves, data at low forces is clearly incomplete. >90% of branches have not dissociated by the end of the experiment. For the particular data shown in 1C (F00nN, n=60 total branches) it means that the time information is coming from <6 observations, which is rather low for the single molecule field. I am slightly worried by this point, since the debranching rates under ADP-Pi conditions at zero force, are even by one magnitude slower. Yet, no raw data is shown. Given that the dissociation rate at low forces is a contentious point, the authors should show the raw data and the corresponding fits. At present, they only show an experimental scheme and images for these "open chamber" assay (Fig S2). Ideally, they would image for much longer than 900s with lower sampling time in those assays, to firmly establish that 20-fold difference also holds at 0 force.

Essential; experiment might already be performed. Otherwise straightforward to do (weeks time).

1. Stability Analysis (Figure 4). I can follow much of the arguments presented in the stability analysis of the daughter vs mother interfaces, which is in principle extremely interesting! However, there are some concerns here:

i) The authors emphasize the zero force ratio derived from fits (which is linked to the stability difference of the two interfaces in the absence of force) despite this being only weakly constrained by data. Intuitively in the model, the stability difference should grow to very large values as the re-nucleation ratio approaches 1 at low force. This combined with the noise in the data poses an issue in my opinion. Looking at the data and the error margin, I think that the authors cannot state with high confidence that there is a real difference between the relative stability of the daughter and mother interfaces between the two nucleotide states of the complex.

Essential; analysis and textual revision only

ii) For ADP-Pi, the renucleation ratio essentially remains flat over the measured force range. Hence, the data can only provide little leverage to estimate both the zero force ratio and, more importantly, the differential distance to the transition state in the slip-bond model in my opinion, which will show in the crossover force. Consequently, the quoted ">100×" stability difference at F=0 and the crossover force >20pN are driven largely by extrapolation rather than direct constraint by data. Given the high number of free parameters in the model, I would anticipate that several crossover forces and differential distances might explain the data nearly equally well. Instead of loosely reporting exact number from fits, I would have hoped for some sort of sensitivity analysis, for instance relying on profile likelihoods. Also parameter values could be reported as bounds (e.g crossover force≫measured range) rather than precise point estimates. This issue re-occurs (albeit not as drastically) for the cortactin experiments (Figure 6).

Essential; analysis and textual revision only

iii) One important expectation from the "two slip bond" model is that branch dissociation rates should not necessarily scale mono-exponentially as they mostly do over the accessible force range of the paper. However, once the "minor" pathway of dissociation from the mother starts to dominate at high forces, rates become more force sensitive. This is nicely recaptured by the model fits in Figure S6 but deserves some explanation in the text. Otherwise, people will simply remember the "ADP-Pi is 20-fold more stable than ADP at all forces" message.

Essential; textual revision only

iv) One important prerequisite for the model is that isolated Arp2/3 complexes (without a daughter filament) should dissociate with equal rates from mother filaments at all flow rates. Since the Arp2/3 complex prefers mother filament curvature, forces experienced by the mother might change its off-rate. It would be good to refer to this assumption in the text and experimentally verify it. I could not find it in the paper nor in Ghasemi et al 2024.

Essential; simple experiment (a weeks time).

v) The force dependence of the branch re-nucleation rate (Fig 3D) has been measured previously by the same group (Ghasemi et al). While the data in the older paper has not been fitted by a model, the trend of the data in the previous paper looks conspicuously different. Are there any explanations for this? I speculate that it might be related to actin and ATP not being saturated (low-force re-nucleation rate rarely exceeds 80%) in Ghasemi et al., but it would be good to know what the authors think about this.

Essential; textual revision only 3. Stability of the authentic ADP-Pi-Arp2/3 complex on the mother filament. The extraordinary stability of the isolated ADP-BeFx-Arp2/3 complex on mother filaments is surprising, especially considering that both ATP and ADP states are much more labile (Ghasemi et al 2024). I would recommend repeating this experiment in the authentic ADP-Pi state with labelled Arp2/3 complexes as a more direct readout, even if this would require working with very high phosphate concentrations.

Essential; simple experiment (a weeks time).

OPTIONAL: Further, but beyond the scope of the present paper, would be titrating phosphate in these experiments, which would even allow the authors to independently verify the reduced Pi affinity for Arp2/3 in the mother filament. Of note, this affinity difference is needed to satisfy detailed balance in the reaction scheme (Fig 4 D)! 4. Importance of "surviving" ADP-Pi-Arp2/3 complexes. The authors show a) rapid turnover of Pi on the ADP-Arp2/3 complex in both branch- or mother filament-bound state and b) the lowered Pi affinity of the latter. Nonetheless, they emphasize the importance of long-lived "surviving" ADP-Pi bound complexes on the mother (even stated in the abstract). I understand that this fraction shows under some experimental conditions (BeFx), but unless I am missing something, most complexes should rapidly lose their phosphate and either exchange nucleotide or dissociate from the mother under physiological conditions. Please clarify or tone done.

Essential; textual revision only 5. GMF mechanism. The authors claim that GMF "...accelerates the departure of the surviving Arp2/3 complex from the mother...". I assume that they infer this from decrease in the re-nucleation ratio. However, alternatively GMF could simply dwell on the complex, inhibiting re-nucleation without promoting dissociation from the mother. The authors should either monitor Arp2/3 dwell times directly to discriminate between these possibilities or be more cautious in their conclusions.

Essential; simple experiment (a weeks time) or textual revision. 6. Cortactin mechanism and the "leash model". I must say that the cortactin data are the most puzzling part of the paper and had to reconcile with what we know from structure. I was hoping to find some of this resolved in the discussion. However, I do not understand the "leash model" in the discussion section for cortactin-mediated branch stabilization: "This would explain the observed increase in branch survival compared to the absence of cortactin. As the pulling force is increased, this rebinding mechanism becomes less efficient." According to my understanding of the data, this is opposite to what happens. Cortactin only stabilizes the labile interface at elevated forces! Some re-writing might help here.

Essential; textual revision.

Minor comments

Organization:

• I do not want to impose on how to best tell the story, but I felt that Fig1 A-D and Fig 2 A-B belong to one logical unit (nucleotide dependence), whereas Fig 1 E-F and Fig 2 C belong to the other (Pi binding and exchange). Perhaps consider re-organizing to streamline presentation?

Semantics/Typos:

• Abstract: „... ADP-Pi and ADP-Arp2/3 detach with the same exponential increase as a function of force...". Increase should refer to the dissociation rate, which should be added to the sentence.
• Results page 8: "...and the majority of Arp2/3 complexes detach from the mother filament while remaining bound to the branch at the debranching time." "Branch" should likely be daughter here, as there is no branch after dissociation of either interface.
• Results page 13: "Exposing ADP-BeFx-Arp2/3 complex branch junctions to a saturating amount of GMF...". It is strange to imply saturation, because GMF likely simply does not bind to the complex in this nucleotide state with appreciable affinity. Suggest to change to "high".
• Discussion page 18: "Moreover, in mammalian Arp2/3, His80 in Arp3 (corresponding to His73 in mammalian actin) is not methylated, and corresponds to residue N77 in Arp3, which is also not modified." N77 likely belongs to Arp2?
• Discussion page 19: "We showed that Pi affinity for Arp2/3 complexes at branch junctions is around 3.7 mM (Fig. 1), a value which lies within the reported 1-10 mM Pi concentration measured in the cytosol in different mammalian cell types". Notably, this is not too different from F-actin, which should be mentioned. By this measure alone, free inorganic phosphate could also directly regulate actin filament stability!

Future interest (non essential):

• It would be utterly exciting (but beyond current scope) to quantify how instantaneous debranching rates evolve for naturally aging branches starting from ATP-Arp2/3 complexes!

Significance

General assessment:

This is a compelling and carefully executed study that delivers a clear mechanistic framework for how Arp2/3 branch junctions fail and re‑form under load. The central strength is the tight integration of state‑of‑the‑art reconstitutions with careful and original kinetic analysis. The experimental design is elegant and experiments have been carried out to a masterful standard. The figures are clear, the statistics are appropriate with some exceptions as detailed above. There are very few labs in the world that could have achieved this feat!

A few aspects could be further strengthened, most notably the explanation and application of the "two slip bond" model as well as slightly more restraint in speculating around specific regulatory mechanisms. However, these are minor refinements that do not detract from the important contributions of the paper.

Overall, the clearly work merits publication with high priority after revision; most requested changes are textual/analytical with very few targeted experiments, which would substantially strengthen core claims.

Advance relative to prior literature:

The major novel findings of the paper are already summarized above. There is some recent work done on the subject of branch mechanics by the authors (Ghasemi et al 2024, PMID: 38277459) and others (Pandit et al 2020 PMID: 32461373), but the focus of the present work is clearly unique and the there is plenty of novel insight.

Audience and impact:

Primary audience: specialists in cytoskeleton dynamics, in vitro reconstitution single molecule biophysics, and mechanobiochemistry. Secondary: researchers in cell motility, morphogenesis and mechanobiology, physicists working on active matter and modelers studying force producing and load-bearing biopolymer networks. The results and analysis framework should inform quantitative models of branched network turnover under load and the interpretation of regulatory factor action in vivo and in cells.

Reviewer expertise:

Actin dynamics; biochemical reconstitution; single molecule approaches; biophysics.

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)):

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Background and unknown in the field:

This study investigates how fibroblast alignment influences the migration of intestinal epithelial cells, contributing to tissue integrity and repair. It is well established that intestinal fibroblasts are important regulators in the tissue through their ability to secrete essential paracrine factors for the epithelium. However, it is less well understood if they also play additional structural, tissue architecture instructing role and how the communication between the fibroblasts and the epithelia is regulated.

Advance over state of the art:

Here the authors have set-up an elegant three-component system to investigate this. They have gone beyond the recent advances of culturing intestinal and colonic organoids in 2D (in a manner that preserves- and villus-like organization) and bioengineered epithelial-stromal model comprising organoid-derived intestinal epithelial cells (IECs), primary intestinal fibroblasts, and a basement membrane matrix. Using this model, they have uncovered fibroblasts enhancing the directed and persistent migration of intestinal epithelial cells (IECs). They used scRNAseq to carefully analyse the stromal cell populations present in their co-cultures of primary mouse intestinal subepithelial fibroblasts and organoid-derived intestinal mouse epithelial cells. They observed that this reflected well the stromal cell-type composition as well as the paracrine activity previously reported for these cells in tissue. Using a clever system with Matrigel and an elastomeric barrier, the authors were able to induce non-epithelial gaps in different scenarios (IECs alone or with fibroblasts or with conditioned media) and observe the wound-closure as well as the presence of specific cell types. They observed that the epithelial monolayers showed significant gap closure when in direct contact with fibroblasts compared to controls. Interestingly, the enhanced efficiency of epithelial migration and gap closure, in the presence of fibroblasts, was independent of PGE₂-EP4 signaling and was not due to differences in cell proliferation. Instead, the imaging revealed that the fibroblasts were in direct contact with the epithelium. The authors observed that in the absence of fibroblasts the migration properties of cells in the villus and the crypt regions were dramatically different and the fibroblast presence was necessary to efficiently synchronize these to support gap closure. In addition, the presence of fibroblasts enhanced the directionality of the epithelial cell migration. Detailed imaging and image analyses revealed that gap closure involved activation of the fibroblasts and co-ordinated coalignment of IECs and fibroblasts. They also explored matrix deposition of the fibroblasts during the process and found that they deposited aligned ECM fibers that guide epithelial migration. Mere cell-derived matrix (devoid of live fibroblasts) was able to partially recapitulate the fibroblast-coordinated epithelial migration that the fibroblast generated matrix and its alignment are key contributors to the phenotype.

Comments:

This is overall a very interesting and well-written study. The imaging and the image analysis are state-of-the art and the bioengineered model is an exciting advancement over current methods developed by these researchers and others. This study meets all the criteria for a publication in the since that all the experiments seem to be carefully conducted, with appropriate controls and sufficient quantifications and statistics. The claims made by the authors are supported by the data. This is currently suitable to be published as a method/protocol and as a descriptive study uncovering interesting cross-talk and co-dependencies of epithelial and stromal cells during injury repair. There are of course aspects that could improve the study further like more mechanistic insight into the underpinnings of the direct epithelia-fibroblast interaction and its involvement in the directed IEC migration. However, these may be topics to investigate in a future study.

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Reviewer #1 (Significance (Required)):

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The strengths of the study are the highly in vivo relevant model system that is amendable to imaging and detailed image analysis of distinct cell populations. This may be adapted by others in in the field and has the potential to transform the way cell dynamics in the intestinal epithelium are visualized and investigated in vitro

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We thank the reviewer for their thoughtful and positive assessment of our work, and their recognition of the relevance of the bioengineered epithelial-stromal model and its potential for quantitative imaging and analysis of epithelial and fibroblast dynamics.

We agree that further mechanistic insight into epithelial-fibroblast crosstalk would strengthen the study. While the current manuscript establishes this tractable system and identifies a role for fibroblast organization and matrix alignment in coordinating epithelial migration, we also aim to deepen the mechanistic understanding in the revision. As outlined in our response to Reviewer 2, we will perform additional experiments to further investigate the epithelial-fibroblast crosstalk and force-dependent interactions underlying this process.

We believe that these additions will complement the current findings and strengthen the conceptual contribution of the study beyond its methodological advances.

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

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Please find enclosed my review comments on the manuscript entitled "Fibroblast alignment coordinates epithelial migration and maintains intestinal tissue integrity" by Jordi Comelles et al.

In this manuscript, the authors use a bioengineered epithelial-stromal system composed of organoid-derived intestinal epithelial cells, primary intestinal fibroblasts, and a basement membrane matrix to show that direct physical interactions between fibroblasts and epithelial cells drive a large-scale organization of the fibroblast network. This spatial reorganization, in turn, promotes persistent and oriented migration of epithelial cells, ultimately enabling restoration of the intestinal epithelium in an in vitro gap-closure assay. Overall, while the authors use an elegant in vitro model to study intestinal wound closure, and more specifically the role of fibroblasts in this context, I find this manuscript not suitable for publication in its present form. The data are overinterpreted, the novelty is limited, and the molecular mechanisms underlying WAE-fibroblast interactions are insufficiently addressed.

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We thank the reviewer for their contribution to the revision process with their valuable assessments. We will address their specific points below.

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Figure 1 - What are the units of the "fraction gap closure" shown in panels d and e? Is it expressed as a percentage?

We thank the reviewer for pointing this out. The "fraction of gap closed" was calculated as (A(t = 0h)-A(t))/A(t = 0h), where A(t = 0h) corresponds to the initial gap area and A(t) is the area of the gap measured at the time point t. With this definition, the fraction of gap closed is dimensionless, it is 0 at the initial time point, will reach 1 if the gap is fully closed and will have negative values if the gap area increases beyond the initial size, as observed in some replicates of the control condition. To avoid misinterpretation, we will express this quantity as a percentage (i.e., multiplied by 100), as suggested by the reviewer. Moreover, we realized it was ill defined in the methods section. This will be corrected as well in the revised version.

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"Actually, epithelial monolayers achieved the most effective gap closure when cultured in direct physical contact with fibroblasts (Figure 1e and Movies 2 and 3)." From the data shown in panels c, d, and e, it appears that fibroblast-conditioned medium alone promotes efficient gap closure, comparable to the + fibroblast condition.

We agree with the reviewer that the original closing sentence overstated the effect. While both fibroblast-conditioned medium and direct fibroblast contact promote efficient gap closure compared to control conditions, the data do not support a consistent difference between these two conditions. We will therefore remove this statement in the revised version to more accurately reflect the results.

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Figure 2 - The use of a cell proliferation inhibitor during the gap-closure assay would help determine the contribution of cell proliferation at the migration front.

We agree with the reviewer that inhibiting proliferation would help assess the contribution of cell proliferation to gap closure. However, in the 2D gap-closure assay, our Ki67 immunostaining showed no significant differences in the proportion of proliferative cells between conditions, either within the monolayer or at the migration front. This suggests that differential proliferation is unlikely to account for the differences in gap closure observed between control and fibroblast-containing conditions.

We note that, in a separate 3D organoid assay, fibroblast-derived signals induced a WAE-like transcriptional program associated with reduced Ki67 mRNA expression, indicating that fibroblasts can promote a more migratory epithelial state without increasing proliferation. Thus, while proliferation may contribute to epithelial homeostasis and repair, our data do not point it as the main determinant of the differences observed in the 2D gap-closure phenotypes.

In addition, pharmacological inhibition of proliferation would likely perturb the homeostasis of the organoid-derived epithelial monolayers, in which proliferative crypt compartments are essential, and would be difficult to restrict to epithelial cells without also affecting fibroblasts in co-culture. For these reasons, although such experiments could inform the general contribution of proliferation to gap closure, we do not think they would directly clarify the differences observed between conditions in our system.

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Figure 2f and 2g - Has a dose-dependent effect of PGE2 been tested?

We thank the reviewer for pointing this out. We did not perform a dose-response analysis of PGE2 in this study, as our aim was to assess the involvement of the PGE2-EP4 axis rather than to characterize its quantitative dynamics. We therefore selected a concentration based on previous work demonstrating dose-dependent induction of the WAE program in 3D organoid systems (Miyoshi et al., 2017). In that study, 1 µM PGE2 was sufficient to induce a significant increase in the WAE marker Cldn4, and we used this concentration as a biologically relevant reference condition. We will clarify this in the methods section.

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Figure 2i - The + fibroblast + EP4i condition (pink) is missing.

We thank the reviewer for pointing this out. The + fibroblast + EP4i condition is present in the plot but not visually distinguishable because it overlaps with the + fibroblast condition and is therefore masked by it. As shown in Figure S4e, the + fibroblast + EP4i condition falls within the variability range of the + fibroblast condition. To improve clarity, we will revise the figure to ensure that this condition is visually identifiable.

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"This suggests a mechanical or contact-mediated role for fibroblasts in preserving epithelial integrity and promoting coordinated migration beyond their paracrine signaling." While PGE2-EP4 signaling does not appear to be involved in the fibroblast-mediated enhancement of gap-closure efficiency, the conclusion that physical interactions are more important than paracrine effects is overstated. For instance, an experimental condition in which fibroblast-conditioned medium is inactivated (boiling for 5 minutes) would strengthen this conclusion. In addition, inhibition of actomyosin contractility in fibroblasts would be informative.

Figure 3 - The data presented here do not convincingly support the dismissal of conditioned medium as a contributing factor. The differences between the + fibroblast-conditioned medium and + fibroblast conditions are modest. In both cases, epithelial cells migrate and gaps close.

We agree with the reviewer that inhibition of actomyosin contractility in fibroblasts would provide valuable insight into the role of force-dependent interactions in epithelial-stromal coupling. However, pharmacological inhibitors of the Rho-ROCK-myosin pathway (e.g., blebbistatin, ML-7, or the ROCK inhibitor Y-27632) would also affect epithelial contractility in our co-culture system, making it difficult to specifically attribute any observed effects to fibroblast mechanics.

We also agree that paracrine signaling plays an important role in epithelial gap closure. Indeed, supplementation of control media with PGE₂ improves gap closure compared to control conditions, although it does not reach the levels observed with fibroblast-conditioned medium, suggesting that additional soluble factors contribute beyond the PGE₂-EP4 axis. However, time-lapse imaging revealed direct and dynamic interactions between fibroblasts and epithelial cells (Movie 6; Figure S5a-d; Movie 7), which prompted us to further investigate the contribution of physical interactions, as addressed in Figure 3.

In Figure 3, we analyzed migration at the single-cell level, in contrast to the tissue-level measurements used for gap closure quantification. In organoid-derived intestinal monolayers, two distinct compartments can be identified: crypt-like and villus-like regions. In vivo, these compartments exhibit different migration behaviors: cells in the crypt are primarily displaced due to crowding, whereas cells in the villus actively migrate, as suggested by the presence of cryptic lamellipodia (Krndija et al., 2019). Consistent with this, tracking individual cells revealed that crypt cells are largely static, while villus cells migrate toward the gap. This compartmentalized behavior was observed in both control and fibroblast-conditioned medium conditions. Strikingly, in the presence of fibroblasts, this differential behavior was reduced, resulting in coordinated migration of both crypt and villus regions.

This mismatch between compartments in control conditions may contribute to the appearance of discontinuities ("holes") within the epithelial layer during migration. In control experiments, these defects failed to close, whereas in conditioned medium they closed slowly or incompletely. In contrast, in the presence of fibroblasts, these disruptions were rapidly and efficiently resolved, indicating improved tissue integrity.

Additionally, analysis of individual trajectories near the migration front showed that cells exhibit significantly increased directional persistence (i.e., movement aligned with the direction of gap closure) in the presence of fibroblasts compared to conditioned medium alone.

Taken together, while paracrine signaling from fibroblasts contributes to epithelial migration and gap closure, the physical presence of fibroblasts induces qualitative changes in epithelial behavior, including coordinated migration across compartments, improved hole closure, and enhanced directional persistence.

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Figure 4a - "Upon removal of the barrier (t = 0 h), fibroblasts at the epithelial front were small and evenly distributed, with no prominent α-SMA fibers present." Here, fibroblasts are α-SMA positive but not elongated. α-SMA may therefore not be the most appropriate marker. What are the levels of phosphorylated MLC2? These may increase during wound closure. Also, fibroblasts culture promotes aSMA expression, therefore, it may be possible that the fibroblasts used in this assay may not represent the healthy fibroblasts found in vivo.

We agree with the reviewer that fibroblasts are α-SMA positive at early time points but are not yet elongated. In our system, we observe that α-SMA is already present at t = 0 h, while fibroblasts progressively elongate and reorganize α-SMA into prominent fiber structures over time. This suggests that changes in α-SMA organization, rather than its initial presence, are associated with fibroblast activation during gap closure.

We note that baseline α-SMA expression may be influenced by in vitro culture conditions prior to the assay, which could differ from the state of fibroblasts in vivo. We will clarify this point in the Discussion to better contextualize our observations relative to native fibroblast populations.

In addition, we agree that assessing phosphorylated myosin light chain 2 (pMLC2) levels would provide complementary information on contractile activity. We will therefore perform pMLC2 staining, as suggested, to further evaluate force generation by fibroblasts during the wound closure process.

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Figure 5 - Fibroblast alignment could also result from paracrine signals secreted by epithelial cells. This possibility should be tested.

We thank the reviewer for this suggestion. To test whether fibroblast alignment could be driven by epithelial-derived paracrine signals, we will culture fibroblasts in conditioned medium collected from epithelial monolayers undergoing gap closure (control condition without fibroblasts) and quantify their alignment over time. This will be compared to fibroblasts maintained in standard fibroblast medium.

This experiment will directly assess whether epithelial-derived soluble factors are sufficient to induce fibroblast alignment, or whether direct physical interactions are required.

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In summary, this manuscript demonstrates that epithelial cells migrate more efficiently on extracellular matrix proteins deposited and oriented by fibroblasts. This concept is not novel. Identifying the molecular mechanisms governing interactions between WAE and subepithelial fibroblasts would significantly enhance the novelty and impact of this study.

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Reviewer #2 (Significance (Required)):

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In this manuscript, the authors use a bioengineered epithelial-stromal system composed of organoid-derived intestinal epithelial cells, primary intestinal fibroblasts, and a basement membrane matrix to show that direct physical interactions between fibroblasts and epithelial cells drive a large-scale organization of the fibroblast network. This spatial reorganization, in turn, promotes persistent and oriented migration of epithelial cells, ultimately enabling restoration of the intestinal epithelium in an in vitro gap-closure assay. Overall, while the authors use an elegant in vitro model to study intestinal wound closure, and more specifically the role of fibroblasts in this context, I find this manuscript not suitable for publication in its present form. The data are overinterpreted, the novelty is limited, and the molecular mechanisms underlying WAE-fibroblast interactions are insufficiently addressed.

*We thank the reviewer for this thorough and critical assessment. We have clarified the overstatements in the rebuttal and we will modify the text to address concerns regarding overinterpretation and clearly acknowledge the limitations of our approach. In particular, we will refine the framing of the study to better distinguish between the contributions of paracrine signaling and physical epithelial-stromal interactions. *

*To address the reviewer's concerns regarding mechanism and novelty, we will perform additional experiments aimed at further characterizing epithelial-stromal cross-talk, and experiments to assess fibroblast contractility and its contribution to epithelial coordination. *

We believe that these revisions and proposed experiments will strengthen the manuscript and clarify its conceptual contribution.

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

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Summary:

- Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The study by Comelles et al. focuses on how primary intestinal fibroblasts contribute to organoid-derived intestinal epithelial migration in wound healing assays. Using fibroblast-epithelial co-cultures in a 2D in vitro gap closure system, the authors found that direct interaction with fibroblasts drives cohesive and directed migration of intestinal epithelia toward the gap. They further propose that long-range fibroblast alignment promotes the deposition of extracellular matrix (ECM) proteins in an oriented fashion, contributing to directed epithelial migration.

Major comments:

- Are the key conclusions convincing?

Some of the key conclusions of this manuscript are not entirely convincing given the available data. The manuscript would benefit from additional evidence and/or clarifications to support their conclusions. See comments below.

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- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

(Fig 4a) The authors claim that fibroblasts become activated during gap closure as evidenced by the enhanced assembly of a-SMA fibers 24 hours following barrier removal. Yet, long a-SMA fibers are also observed when fibroblasts are cultured in the absence of epithelial cells or barrier removal (Fig. S1b). To support this conclusion, the authors should consider including additional controls to account for potential time-dependent assembly of a-SMA fibers (e.g., fibroblast-only control).

We thank the reviewer for pointing this out. We agree that a fibroblast-only control would be important to account for potential time-dependent assembly of α-SMA fibers. We will therefore perform additional experiments monitoring α-SMA organization in fibroblasts cultured alone over time, which will allow us to better interpret the dynamics observed in the co-culture conditions.

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(Fig. 5a) The authors conclude that fibroblasts align parallel to the direction of epithelial migration during gap closure. While quantifications are convincing, again, a fibroblast-only control accounting for time-dependent spreading and elongation (as seen in Fig. S1) is missing. Including such a control would strengthen their claim that alignment is specific to the gap closure context rather than a time-dependent phenotype.

We agree with the reviewer that, given the intrinsic ability of fibroblasts to form ordered domains with long-range alignment, this control would be highly informative. We will therefore quantify fibroblast alignment over time in fibroblast-only cultures, which will allow us to determine to what extent the long-range organization observed in co-culture is specific to the gap closure context.

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(Fig 6) The authors claim that fibroblast-derived aligned ECM drives directional epithelial migration. While fibronectin fibers appear scarce and weakly aligned with the direction of migration, laminin and type IV collagen fibers are barely detectable (Fig. 6f). This may reflect a defect in ECM deposition rather than fiber alignment, which contrasts with Fig. S1, where fibroblasts are shown to deposit and assemble laminin and type IV collagen fibers. One possible explanation is that primary fibroblasts were not cultured long enough to allow robust ECM deposition. Alternatively, the observed effect may be specific to fibronectin, which is consistent with fibroblasts being its major source. The authors should revise their interpretation or provide additional evidence to support their current claim.

We thank the reviewer for this important point. We agree that differences in ECM signal within the gap may reflect not only fiber alignment but also differences in the amount of protein deposited. In the +fibroblast condition, fibroblasts in the gap have more time to secrete ECM compared to the "empty gap" condition, where fibroblasts remain confined beneath the epithelium.

In addition, the presence of Matrigel likely masks the contribution of certain ECM components, making laminin or type IV collagen more apparent than fibronectin. We will therefore revise the interpretation of these results to explicitly acknowledge the contribution of ECM abundance in addition to alignment.

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(Fig 6i) The authors propose that the presence of ECM alone within the gap enhances epithelial gap closure compared to empty gap conditions, although gap closure remains less effective than in the presence of primary fibroblasts. From the figure legend and methods, it seems that the decellularized ECM condition is generated using NIH-3T3 fibroblasts cultured for 8 days, whereas the other conditions used primary fibroblasts cultured for 1 day (Fig. 6a-h). This comparison is confounded by differences in cell source and ECM deposition time. If I am misunderstanding this, please clarify, otherwise consider repeating the decellularized ECM condition using primary fibroblasts and matching culture times for a fair comparison. Along these lines, please include images showing that ECM fibers remain intact following decellularization.

We thank the reviewer for this suggestion. We will include additional staining to confirm that ECM fibers remain intact after decellularization in the revised version.

Regarding the use of NIH-3T3 fibroblasts for CDM generation, this choice was made to minimize potential residual paracrine signaling from primary intestinal fibroblasts after decellularization. We acknowledge that this introduces differences in cell source.

Concerning culture time, we followed established protocols for CDM formation, which recommend extended culture periods ({greater than or equal to}8 days) to allow robust ECM deposition (Cukierman et al., 2001; Franco-Barraza et al., 2016; Godeau et al., 2020). We will clarify these points in the revised manuscript and discuss the limitations associated with these differences.

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- 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 additional experiments outlined above would help support the current conclusions of the manuscript, rather than to explore new directions beyond its scope.

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- 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.

Yes, the additional experiments primarily involve the inclusion of controls and additional immunofluorescence imaging to their existing experimental setups. They should be relatively straightforward to implement (~2-3 months).

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

Yes.

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- Are the experiments adequately replicated and statistical analysis adequate?

Overall, yes. But some plot legends should specify the number of replicates analyzed (e.g. Fig. 2b, Fig. 2d, Fig. 3h).

We will review and correct these issues.

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Minor comments:

- Specific experimental issues that are easily addressable.

(Fig. 1c-e) The authors state that intestinal epithelial monolayers exhibit the most effective gap closure when in direct contact with fibroblasts. However, fibroblast-conditioned media and co-cultures show comparable gap closure efficiencies (Fig. 1e). The authors should consider revising this interpretation based on the provided data.

We thank the reviewer for pointing this out, which was also raised by Reviewer 2. As discussed above, we agree that the original statement overstated the effect. Both fibroblast-conditioned medium and direct fibroblast contact promote efficient gap closure compared to control conditions, and we will revise the text accordingly to reflect that no consistent quantitative difference is observed between these two conditions.

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(Fig. 3b) The authors suggest that crypt-like epithelial cells undergo migration when grown on fibroblasts, but not in conditioned media alone. This is interesting, but it is not clear how they identify crypt-like cells for tracking. The authors should clarify if crypt-like cells are defined based on markers or inferred from their morphology.

We thank the reviewer for this comment. In these tracking analyses, crypt-like cells were identified based on morphology. As shown in Figure S3 and in Larrañaga et al., 2025, crypt-like cells, defined by specific molecular markers, are significantly smaller than villus-like cells and form high-density regions. These features allow their identification based on morphology in fluorescently labeled monolayers. We will clarify this criterion in the Methods section of the revised manuscript.

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(Fig 3f-h) The authors conclude that fibroblasts promote directed epithelial cell motility based on cell trajectory analysis. Although they state that this analysis is performed on epithelial monolayers, their tdTomato epithelial population appears sparse in some conditions (control and conditioned media; Fig. S6a). Such variability in cell density may bias measurements of migration directionality at the cell-level, unless a mixed population is being used for tracking. The authors should clarify whether this analysis was indeed conducted on confluent monolayers.

We thank the reviewer for this comment. For trajectory analysis, we used a mixed population of tdTomato-positive and non-fluorescent epithelial cells in some experiments to facilitate individual cell tracking. Importantly, epithelial monolayers were confluent in all conditions analyzed. We will clarify this in the Methods section.

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(Fig 6b) Their gap closure experimental setup indicates that fibroblasts are cultured on a Matrigel-coated surface, which should already contain abundant laminin and type IV collagen. Thus, it is unclear why type IV collagen is not detected underneath fibroblasts. The authors should explain why this is the case for clarity.

We thank the reviewer for pointing out this observation. Indeed, fibroblasts are cultured on a Matrigel-coated surface which contains laminin and collagen type IV among many other components. We observed thick collagen-rich structures between the fibroblasts and the epithelia that we atributed, not only to fibroblasts' secreted collagen, but also a rearrengement of the collagen available in the coated surface. We will clarify this in the discussion of the revised version for clarity.

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- Are prior studies referenced appropriately?

Yes

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- Are the text and figures clear and accurate?

Mostly. Figures 6d and 6g seem to be duplicated by mistake.

We thank the reviewer for noting this. We will correct this mistake.

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

There are some missing frames in Movie 2. If they are not available, it's okay to include black frames, so that the sequence remains consistent with the timestamps.

The authors may consider using asterisks as significance indicators instead of reporting precise p-values directly on their plots. Having this format would facilitate visual comparison of statistical significance across conditions.

Displaying single channels of experiments where co-cultures are used would help to better interpret their data.

We thank the reviewer for pointing out these issues and for their valuable suggestions. We will correct the errors in the movie and improve the presentation as suggested where possible.

• *

Reviewer #3 (Significance (Required)):

• *

- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This study provides a valuable contribution to understanding how fibroblasts influence intestinal epithelial migration. The main advance lies in the use of a co-culture system combining organoid-derived intestinal epithelial cells that assemble into a crypt-villus organization with primary intestinal fibroblasts in a 2D gap closure system. This approach allows the authors to examine epithelial-fibroblast interactions in a more physiologically relevant context compared to prior work.

We thank the reviewer for their positive assessment of the significance of our work.

• *

- Place the work in the context of the existing literature (provide references, where appropriate).

Addressed above.

• *

- State what audience might be interested in and influenced by the reported findings.

Cell and developmental biology, extracellular matrix biology, tissue regeneration.

• *

- 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.

Tissue morphogenesis, cell motility, extracellular matrix dynamics.

We thank the reviewer for their positive assessment and for their suggestions to improve the manuscript.

• *

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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).

The study by Comelles et al. focuses on how primary intestinal fibroblasts contribute to organoid-derived intestinal epithelial migration in wound healing assays. Using fibroblast-epithelial co-cultures in a 2D in vitro gap closure system, the authors found that direct interaction with fibroblasts drives cohesive and directed migration of intestinal epithelia toward the gap. They further propose that long-range fibroblast alignment promotes the deposition of extracellular matrix (ECM) proteins in an oriented fashion, contributing to directed epithelial migration.

Major comments:

• Are the key conclusions convincing?

Some of the key conclusions of this manuscript are not entirely convincing given the available data. The manuscript would benefit from additional evidence and/or clarifications to support their conclusions. See comments below. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

(Fig 4a) The authors claim that fibroblasts become activated during gap closure as evidenced by the enhanced assembly of a-SMA fibers 24 hours following barrier removal. Yet, long a-SMA fibers are also observed when fibroblasts are cultured in the absence of epithelial cells or barrier removal (Fig. S1b). To support this conclusion, the authors should consider including additional controls to account for potential time-dependent assembly of a-SMA fibers (e.g., fibroblast-only control). (Fig. 5a) The authors conclude that fibroblasts align parallel to the direction of epithelial migration during gap closure. While quantifications are convincing, again, a fibroblast-only control accounting for time-dependent spreading and elongation (as seen in Fig. S1) is missing. Including such a control would strengthen their claim that alignment is specific to the gap closure context rather than a time-dependent phenotype. (Fig 6) The authors claim that fibroblast-derived aligned ECM drives directional epithelial migration. While fibronectin fibers appear scarce and weakly aligned with the direction of migration, laminin and type IV collagen fibers are barely detectable (Fig. 6f). This may reflect a defect in ECM deposition rather than fiber alignment, which contrasts with Fig. S1, where fibroblasts are shown to deposit and assemble laminin and type IV collagen fibers. One possible explanation is that primary fibroblasts were not cultured long enough to allow robust ECM deposition. Alternatively, the observed effect may be specific to fibronectin, which is consistent with fibroblasts being its major source. The authors should revise their interpretation or provide additional evidence to support their current claim. (Fig 6i) The authors propose that the presence of ECM alone within the gap enhances epithelial gap closure compared to empty gap conditions, although gap closure remains less effective than in the presence of primary fibroblasts. From the figure legend and methods, it seems that the decellularized ECM condition is generated using NIH-3T3 fibroblasts cultured for 8 days, whereas the other conditions used primary fibroblasts cultured for 1 day (Fig. 6a-h). This comparison is confounded by differences in cell source and ECM deposition time. If I am misunderstanding this, please clarify, otherwise consider repeating the decellularized ECM condition using primary fibroblasts and matching culture times for a fair comparison. Along these lines, please include images showing that ECM fibers remain intact following decellularization. - 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 additional experiments outlined above would help support the current conclusions of the manuscript, rather than to explore new directions beyond its 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.

Yes, the additional experiments primarily involve the inclusion of controls and additional immunofluorescence imaging to their existing experimental setups. They should be relatively straightforward to implement (~2-3 months). - Are the data and the methods presented in such a way that they can be reproduced?

Yes. - Are the experiments adequately replicated and statistical analysis adequate?

Overall, yes. But some plot legends should specify the number of replicates analyzed (e.g. Fig. 2b, Fig. 2d, Fig. 3h).

Minor comments:

• Specific experimental issues that are easily addressable.

(Fig. 1c-e) The authors state that intestinal epithelial monolayers exhibit the most effective gap closure when in direct contact with fibroblasts. However, fibroblast-conditioned media and co-cultures show comparable gap closure efficiencies (Fig. 1e). The authors should consider revising this interpretation based on the provided data. (Fig. 3b) The authors suggest that crypt-like epithelial cells undergo migration when grown on fibroblasts, but not in conditioned media alone. This is interesting, but it is not clear how they identify crypt-like cells for tracking. The authors should clarify if crypt-like cells are defined based on markers or inferred from their morphology. (Fig 3f-h) The authors conclude that fibroblasts promote directed epithelial cell motility based on cell trajectory analysis. Although they state that this analysis is performed on epithelial monolayers, their tdTomato epithelial population appears sparse in some conditions (control and conditioned media; Fig. S6a). Such variability in cell density may bias measurements of migration directionality at the cell-level, unless a mixed population is being used for tracking. The authors should clarify whether this analysis was indeed conducted on confluent monolayers. (Fig 6b) Their gap closure experimental setup indicates that fibroblasts are cultured on a Matrigel-coated surface, which should already contain abundant laminin and type IV collagen. Thus, it is unclear why type IV collagen is not detected underneath fibroblasts. The authors should explain why this is the case for clarity. - Are prior studies referenced appropriately?

Yes - Are the text and figures clear and accurate?

Mostly. Figures 6d and 6g seem to be duplicated by mistake. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

There are some missing frames in Movie 2. If they are not available, it's okay to include black frames, so that the sequence remains consistent with the timestamps. The authors may consider using asterisks as significance indicators instead of reporting precise p-values directly on their plots. Having this format would facilitate visual comparison of statistical significance across conditions. Displaying single channels of experiments where co-cultures are used would help to better interpret their data.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This study provides a valuable contribution to understanding how fibroblasts influence intestinal epithelial migration. The main advance lies in the use of a co-culture system combining organoid-derived intestinal epithelial cells that assemble into a crypt-villus organization with primary intestinal fibroblasts in a 2D gap closure system. This approach allows the authors to examine epithelial-fibroblast interactions in a more physiologically relevant context compared to prior work. - Place the work in the context of the existing literature (provide references, where appropriate). Addressed above.

• State what audience might be interested in and influenced by the reported findings.

Cell and developmental biology, extracellular matrix biology, tissue regeneration. - 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.

Tissue morphogenesis, cell motility, extracellular matrix dynamics.

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Referee #2

Evidence, reproducibility and clarity

Please find enclosed my review comments on the manuscript entitled "Fibroblast alignment coordinates epithelial migration and maintains intestinal tissue integrity" by Jordi Comelles et al. In this manuscript, the authors use a bioengineered epithelial-stromal system composed of organoid-derived intestinal epithelial cells, primary intestinal fibroblasts, and a basement membrane matrix to show that direct physical interactions between fibroblasts and epithelial cells drive a large-scale organization of the fibroblast network. This spatial reorganization, in turn, promotes persistent and oriented migration of epithelial cells, ultimately enabling restoration of the intestinal epithelium in an in vitro gap-closure assay. Overall, while the authors use an elegant in vitro model to study intestinal wound closure, and more specifically the role of fibroblasts in this context, I find this manuscript not suitable for publication in its present form. The data are overinterpreted, the novelty is limited, and the molecular mechanisms underlying WAE-fibroblast interactions are insufficiently addressed.

Figure 1 - What are the units of the "fraction gap closure" shown in panels d and e? Is it expressed as a percentage? "Actually, epithelial monolayers achieved the most effective gap closure when cultured in direct physical contact with fibroblasts (Figure 1e and Movies 2 and 3)." From the data shown in panels c, d, and e, it appears that fibroblast-conditioned medium alone promotes efficient gap closure, comparable to the + fibroblast condition. Figure 2 - The use of a cell proliferation inhibitor during the gap-closure assay would help determine the contribution of cell proliferation at the migration front. Figure 2f and 2g - Has a dose-dependent effect of PGE2 been tested? Figure 2i - The + fibroblast + EP4i condition (pink) is missing. "This suggests a mechanical or contact-mediated role for fibroblasts in preserving epithelial integrity and promoting coordinated migration beyond their paracrine signaling." While PGE2-EP4 signaling does not appear to be involved in the fibroblast-mediated enhancement of gap-closure efficiency, the conclusion that physical interactions are more important than paracrine effects is overstated. For instance, an experimental condition in which fibroblast-conditioned medium is inactivated (boiling for 5 minutes) would strengthen this conclusion. In addition, inhibition of actomyosin contractility in fibroblasts would be informative. Figure 3 - The data presented here do not convincingly support the dismissal of conditioned medium as a contributing factor. The differences between the + fibroblast-conditioned medium and + fibroblast conditions are modest. In both cases, epithelial cells migrate and gaps close. Figure 4a - "Upon removal of the barrier (t = 0 h), fibroblasts at the epithelial front were small and evenly distributed, with no prominent α-SMA fibers present." Here, fibroblasts are α-SMA positive but not elongated. α-SMA may therefore not be the most appropriate marker. What are the levels of phosphorylated MLC2? These may increase during wound closure. Also, fibroblasts culture promotes aSMA expression, therefore, it may be possible that the fibroblasts used in this assay may not represent the healthy fibroblasts found in vivo. Figure 5 - Fibroblast alignment could also result from paracrine signals secreted by epithelial cells. This possibility should be tested. In summary, this manuscript demonstrates that epithelial cells migrate more efficiently on extracellular matrix proteins deposited and oriented by fibroblasts. This concept is not novel. Identifying the molecular mechanisms governing interactions between WAE and subepithelial fibroblasts would significantly enhance the novelty and impact of this study.

Significance

In this manuscript, the authors use a bioengineered epithelial-stromal system composed of organoid-derived intestinal epithelial cells, primary intestinal fibroblasts, and a basement membrane matrix to show that direct physical interactions between fibroblasts and epithelial cells drive a large-scale organization of the fibroblast network. This spatial reorganization, in turn, promotes persistent and oriented migration of epithelial cells, ultimately enabling restoration of the intestinal epithelium in an in vitro gap-closure assay. Overall, while the authors use an elegant in vitro model to study intestinal wound closure, and more specifically the role of fibroblasts in this context, I find this manuscript not suitable for publication in its present form. The data are overinterpreted, the novelty is limited, and the molecular mechanisms underlying WAE-fibroblast interactions are insufficiently addressed.

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Referee #1

Evidence, reproducibility and clarity

Background and unknown in the field:

This study investigates how fibroblast alignment influences the migration of intestinal epithelial cells, contributing to tissue integrity and repair. It is well established that intestinal fibroblasts are important regulators in the tissue through their ability to secrete essential paracrine factors for the epithelium. However, it is less well understood if they also play additional structural, tissue architecture instructing role and how the communication between the fibroblasts and the epithelia is regulated.

Advance over state of the art:

Here the authors have set-up an elegant three-component system to investigate this. They have gone beyond the recent advances of culturing intestinal and colonic organoids in 2D (in a manner that preserves- and villus-like organization) and bioengineered epithelial-stromal model comprising organoid-derived intestinal epithelial cells (IECs), primary intestinal fibroblasts, and a basement membrane matrix. Using this model, they have uncovered fibroblasts enhancing the directed and persistent migration of intestinal epithelial cells (IECs). They used scRNAseq to carefully analyse the stromal cell populations present in their co-cultures of primary mouse intestinal subepithelial fibroblasts and organoid-derived intestinal mouse epithelial cells. They observed that this reflected well the stromal cell-type composition as well as the paracrine activity previously reported for these cells in tissue. Using a clever system with Matrigel and an elastomeric barrier, the authors were able to induce non-epithelial gaps in different scenarios (IECs alone or with fibroblasts or with conditioned media) and observe the wound-closure as well as the presence of specific cell types. They observed that the epithelial monolayers showed significant gap closure when in direct contact with fibroblasts compared to controls. Interestingly, the enhanced efficiency of epithelial migration and gap closure, in the presence of fibroblasts, was independent of PGE₂-EP4 signaling and was not due to differences in cell proliferation. Instead, the imaging revealed that the fibroblasts were in direct contact with the epithelium. The authors observed that in the absence of fibroblasts the migration properties of cells in the villus and the crypt regions were dramatically different and the fibroblast presence was necessary to efficiently synchronize these to support gap closure. In addition, the presence of fibroblasts enhanced the directionality of the epithelial cell migration. Detailed imaging and image analyses revealed that gap closure involved activation of the fibroblasts and co-ordinated coalignment of IECs and fibroblasts. They also explored matrix deposition of the fibroblasts during the process and found that they deposited aligned ECM fibers that guide epithelial migration. Mere cell-derived matrix (devoid of live fibroblasts) was able to partially recapitulate the fibroblast-coordinated epithelial migration that the fibroblast generated matrix and its alignment are key contributors to the phenotype.

Comments:

This is overall a very interesting and well-written study. The imaging and the image analysis are state-of-the art and the bioengineered model is an exciting advancement over current methods developed by these researchers and others. This study meets all the criteria for a publication in the since that all the experiments seem to be carefully conducted, with appropriate controls and sufficient quantifications and statistics. The claims made by the authors are supported by the data. This is currently suitable to be published as a method/protocol and as a descriptive study uncovering interesting cross-talk and co-dependencies of epithelial and stromal cells during injury repair. There are of course aspects that could improve the study further like more mechanistic insight into the underpinnings of the direct epithelia-fibroblast interaction and its involvement in the directed IEC migration. However, these may be topics to investigate in a future study.

Significance

The strengths of the study are the highly in vivo relevant model system that is amendable to imaging and detailed image analysis of distinct cell populations. This may be adapted by others in in the field and has the potential to transform the way cell dynamics in the intestinal epithelium are visualized and investigated in vitro

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Reply to the reviewers

Manuscript number: RC-2025-03319

Corresponding author(s): Pedro Milanez-Almeida

1. General Statements

We thank the reviewers for their careful and constructive evaluation. We agree that the original manuscript did not communicate the conceptual scope, novelty, or limitations of the framework as clearly as it should have. In response, we substantially revised both the presentation and the supporting analyses.

The central revision reframes tinydenseR around a common landmark-by-sample fuzzy density matrix derived from UMAP-based cell–landmark connection strengths. This representation supports four downstream analysis modes: (1) landmark-level differential density modeling, (2) supervised quantitative sample embedding via partial-effect principal component projection (pePC), (3) density-contrast-aligned feature exploration via graph-diffused partial least squares decomposition (plsD), and (4) connection-strength-weighted pseudobulk differential expression. A dedicated algorithm overview ("The tinydenseR Algorithm") and revised Figure 1 make this structure explicit, and the revised manuscript clarifies which components are novel and which remain conventional once subsets are defined.

To strengthen empirical support, we expanded synthetic and permutation benchmarks, added a landmark- versus cell-level integration comparison, updated miloR benchmarking to use graph refinement, and included analysis of the publicly available COMBAT COVID-19 PBMC dataset. The Methods now correct the terminology for UMAP-derived weights (connection strengths, not probabilities), make the landmark allocation rule explicit, and clarify assumptions underlying the density matrix construction.

We do not claim that the revision resolves every benchmarking or sensitivity question raised. The goal was to make the claims more precise, the framework more transparent, and the empirical evidence more directly aligned with the revised conceptual framing.

2. Point-by-point description of the revisions

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

Overall, this manuscript presents a landmark-based strategy for scaling sample-level differential abundance and differential expression analyses to atlas-sized single-cell datasets by summarizing cells through fuzzy cell-landmark memberships and then applying standard sample-level modeling. The approach is promising for computational efficiency, but several key methodological claims and design choices would benefit from clearer justification and stronger empirical validation.

We appreciate the reviewer's careful summary and recognition of the promise of landmark-based strategies for atlas-scale analysis. The specific concerns are addressed point by point below; the revision addresses them through expanded benchmarking, clearer methodological justification, and more precise scoping of the framework's contributions and limitations.

The manuscript's main methodological novelty appears to be computational/scalable representation learning via landmarking and fuzzy cell-landmark densities. However, for differential expression within cell states, the inferential procedure is standard pseudo-bulk + limma/voom and still relies on discrete subset definitions (clusters/cell types, or landmark bins) and downstream annotation for biological interpretation. The authors should clarify that "clustering-independent" primarily applies to the DA representation/testing, and strengthen evidence that landmark-level subsets provide materially different biological resolution than simply clustering a subsample.

Response:

This comment raises a central question about the scope of "clustering independence" in the framework. We want to be direct: the revised manuscript does not include a dedicated head-to-head benchmark comparing tinydenseR landmark-level subsets with a "cluster a subsample" workflow. We recognize this as a limitation of the current revision.

What the revision does instead is twofold. First, it sharpens the conceptual distinction. A subsampled clustering still imposes a hard partition and remains sensitive to the choice of clustering algorithm, graph construction, and resolution parameter. The landmark-density framework avoids that dependence: the same continuous representation supports differential density modeling, pePC, plsD, and pseudobulk DE without requiring a rigid partition at any stage. We added a sentence in the Introduction noting that structure-aware approaches can better preserve data geometry, rare populations, and local neighborhood structure than naive random subsampling.

Second, the revision strengthens empirical support within the landmark-density framework itself. The synthetic benchmarks demonstrate recovery of simulated trajectory-associated density shifts, abundance perturbations, and activation-associated expression changes directly in the landmark-density space. The real-data applications now present findings through landmark-level density contrasts, pePC, and plsD, with results interpreted as consistent with prior biological knowledge and published reports.

We also clarify in the revised manuscript that the pseudobulk aggregation itself now derives subsets from the fuzzy landmark topology rather than from a rigid partition, even though the formal gene-level testing remains conventional once a subset has been specified. Thus, clustering independence applies not only to density inference but also to effect-specific sample embedding and exploratory feature interpretation.

We therefore frame the contribution as a conceptual and empirical argument for the clustering-free workflow, while acknowledging that a direct empirical comparison with a cluster-a-subsample alternative has not been performed in this revision.

The method treats UMAP fuzzy graph weights as "connection probabilities" and uses their sums to estimate sample-level abundance around each landmark. Please clarify (i) how sensitive the density matrix is to the UMAP membership construction (e.g., choice of parameters, the per-cell membership mass constraint), and (ii) why this is an appropriate abundance surrogate in the context of sample-level inference.

Response:

This is an important comment about both the interpretation and parameter-dependence of the UMAP-derived fuzzy graph. We revised the manuscript on both fronts.

First, we no longer refer to the UMAP fuzzy graph weights as "connection probabilities." The revised Methods (Step 4) now define the directed neighborhood memberships, the local connectivity and scaling terms, and the symmetrized UMAP fuzzy-union weight explicitly, describing the resulting quantities as fuzzy graph connection strengths / affinities rather than calibrated probabilities.

Second, we now state explicitly that the cell–landmark weights depend on the choice of nearest-landmark count, the per-cell membership-mass constraint, and the local scaling parameters. These choices are held fixed within each analysis, and the resulting landmark-by-sample matrix should be interpreted as a relative measure of enrichment/depletion around landmark neighborhoods rather than as a physical cell count. We did not add a dedicated sensitivity benchmark across UMAP hyperparameters in this revision; given the scope of the other benchmarking additions, we judged this to be better addressed as a focused follow-up study and have noted the dependence on these construction choices explicitly in the Methods. We also note that the consistent behavior of the framework across the diverse datasets analyzed in this work—spanning synthetic, cytometry, and multiple scRNA-seq settings—provides empirical evidence of robustness to parameter choice, as stated in the revised Methods.

Third, we clarify why summing connection strengths is an appropriate abundance surrogate for sample-level inference. In the revised Methods, the unnormalized quantity around each landmark is defined as the sum of cell–landmark fuzzy weights within a sample, followed by sample-size normalization and log-transformation. The text now explains this both operationally (a continuous measure of how much cell mass from a given sample concentrates near a landmark neighborhood) and conceptually (a soft-assignment abundance surrogate internally consistent with the manifold-based representation used throughout the framework).

These revisions address the concern by making two points explicit: (i) the UMAP-derived quantities are fuzzy graph connection strengths rather than calibrated probabilities, and (ii) their sums serve as a continuous, size-normalized abundance surrogate aligned with the landmark-based representation on which downstream inference is performed.

The landmark selection step caps landmarks at 10% of cells per sample (and an overall cap of 5,000 landmarks by default), but the rationale for these thresholds is not clearly justified. Additionally, interaction between the per-sample cap and the global 5,000 landmark cap: when the global cap is binding, how are landmarks redistributed across samples, and does this induce unequal representation across samples with different cell yields?

Response:

We agree that the rationale for the default landmark caps and the interaction between the per-sample and global limits should be stated more explicitly. We revised Methods Step 2 (Landmark Selection) accordingly.

The revised manuscript states that the default caps balance approximate proportional representation across samples with bounded computation. The target number of landmarks is defined from the per-sample sampling proportion (p = 0.1 by default) together with the overall cap of 5,000 landmarks, so that landmark sampling remains approximately proportional to sample cell yield unless the global budget becomes limiting.

We also clarify how the per-sample and global caps interact. When the global cap is binding, each sample is subject to the same per-sample upper bound given by an equal-share maximum of the global target, while smaller samples remain limited by their own proportional cap:

where is the number of cells in sample , is the sampling proportion, , and is the number of samples. This means that no single high-yield sample can dominate the landmark set, while smaller samples contribute only up to their own proportional allocation.

The revised manuscript also notes the consequence for unequal sample yields: because small samples remain limited by , the total number of selected landmarks can be less than the nominal global budget if many samples are small. We therefore frame the rule as a transparent compromise that limits over-representation of high-yield samples while preserving simple approximately proportional design. For additional transparency, is recorded in the metadata for inspection, users can adjust p to match replicate structure and heterogeneity, and the software warns when sample cell yields differ by more than 10-fold.

Reviewer #1 (Significance (Required)):

This manuscript introduces a practical landmark-based framework that makes sample-level differential abundance and expression analyses feasible at atlas scale by summarizing large cell collections through a reduced set of representative cells and fuzzy cell-landmark memberships, then leveraging well-established sample-level linear modeling. The main strengths are its emphasis on scalability, a clear engineering workflow that can be applied across large studies, and a unified representation that can support multiple downstream analyses. The main limitations are that key inferential components remain conventional once subsets are defined, biological interpretation still relies on clustering/label transfer and downstream annotation, and several core design choices (e.g., treating UMAP fuzzy weights as "probabilities" and the default landmark caps) would benefit from stronger justification and sensitivity analyses to support the paper's broader claims about cluster-independence and biological resolution.

Response:

We appreciate this balanced assessment. The revised manuscript addresses these concerns through the changes detailed in our preceding responses: the framework is now presented around the common landmark-density representation, with explicit scoping of which components are novel (the density matrix, pePC) and which remain conventional (pseudobulk DE after subset selection). The UMAP-derived weights are described as connection strengths rather than probabilities, the landmark caps are justified more explicitly, and the empirical support has been expanded through synthetic, permutation, integration, and real-data analyses.

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

The authors describe a new computational framework for the analysis of single-cell RNA-seq data in multiple domains that uses probabilistic cluster assignment for downstream differential expression and abundance analysis. They show that their method outperforms similar methods in certain tasks, and provide computational performance studies to show that this is tractable on large scale RNA-seq datasets.

I congratulate the authors on a well written and interesting manuscript, and the development of what seems like quite a comprehensive analysis package. I particularly appreciate the effort to demonstrate computational performance on large datasets (and of course the great name!). Nevertheless, I have a few minor comments that I think would enhance the presentation and impact of the paper.

We are grateful for Reviewer 2's generous assessment and constructive comments, which helped us improve the presentation, terminology, and readability of the manuscript. The responses below address each point in detail.

From the introduction, it's a little hard to determine what exactly tinydenseR is doing, what the underlying philosophy is, and what the key innovations are. This is especially apparent as the paper then launches straight into the results. The methods section is very comprehensive, however without a 'guide' through this that bridges the gap between the very high level description and the implementation details, a reader could end up getting stuck. So my suggestion would be to add a couple of paragraphs to the introduction that provide this, such that the reader would only need to consult the methods for the real implementation details.

Response:

We agree that the original manuscript moved too quickly from high-level motivation into application results without providing enough conceptual guidance.

We addressed this in two complementary ways. First, we sharpened the framing in the final paragraph of the Introduction, which now describes tinydenseR as a "fuzzy set-based, technology-agnostic framework for sample-level modeling and quantitative embedding" built around a shared landmark-based representation. Second, we added a dedicated Results subsection, "The tinydenseR Algorithm," that walks the reader through the core elements of the framework—the fuzzy density matrix, differential density analysis, pePC, plsD and pseudobulk DE—before the application sections. This overview was not present in the original version and now functions as the conceptual bridge between the high-level framing and the full Methods that the reviewer requested. We also revised Figure 1 so that the workflow schematic makes these components visually explicit, with the density matrix shown as the common representation from which all four downstream analysis modes are derived.

We thus addressed the reviewer's underlying point somewhat differently from the exact suggestion of adding multiple new Introduction paragraphs: the revised manuscript combines a more explicit Introduction paragraph with a dedicated algorithm overview at the start of the Results and an expanded workflow schematic.

It seems that the probabilities that you get from the fuzzy cluster assignment aren't necessarily well calibrated. After the Benjamini-Hochberg correction this might end up not being a issue, so it would be good to see that the FDR that you mention in line 431 is indeed roughly how many discoveries are made under the null hypothesis for some indicative configurations, and whether this deviates significantly from the expectation.

Response:

We agree that the UMAP-derived fuzzy weights should not be interpreted as calibrated probabilities for statistical inference. The revised Methods (Step 4) now describe these quantities as affinities / connection strengths used to construct a continuous abundance surrogate, not calibrated probabilities for statistical modeling.

To address the concern empirically, we added permutation-based null-distribution analyses across the synthetic benchmark settings (Fig. S4). These analyses report the number of discoveries at q We note that the swfdr-based q-values are plug-in estimates of per-feature FDR, and do not provide a formal guarantee that the full rejection set at q ≤ α is globally FDR-controlled in the BH sense (this is now stated in Methods Step 5). The permutation results are therefore presented as evidence that, in the benchmark settings considered, the method does not produce substantial spurious discovery under arbitrary relabeling, rather than as a proof of exact calibration under all null configurations.

The rest of my comments are minor and only related to the presentation:

l71 (and elsewhere): A bit more detail about these datasets would be nice (what the trajectories are, etc, rather than just the configuration).

The revised manuscript adds substantially more detail for the synthetic trajectory, DA, and DE datasets in both the Results and the dedicated Synthetic Data Methods subsections.

l73: The language is a little different between this description and the figures, so it's a little hard to keep track of the correspondence.

The revised manuscript aligns the synthetic sections more explicitly with the figures: trajectory is now Fig. 1, simulated DA is Fig. S1, and simulated DE is Fig. S2, with corresponding figure legends rewritten in the same language.

Fig S2 (and others): I know that these are supplemental figures, but they're quite dense and hard to read (both conceptually and in terms of the font size). For something supporting a direct claim in the paper, it would be nice to have one or two plots in the main body of the paper that summarise all of the evidence in these denser supplementary plots.

The revised manuscript adds a stronger main-text overview in Figure 1 and the new "The tinydenseR Algorithm" subsection. The DA/DE benchmark panels remain in the Supplementary Figures, but the revised main-text overview and workflow schematic now guide the reader more explicitly through the supporting evidence.

l106: This is a little confusing to read (not clear whether these are single and double knock outs or just wild type and double knock out).

The revised text now states explicitly: WT for HRAS and NRAS versus H/NRAS double knockout (KO).

l162: In general it would be nice to link this back to some of the choices made in tinydenseR compare to other techniques.

The revised Discussion now includes explicit comparison to MetaCell / SEACells, to unsupervised sample-representation methods such as PILOT, MrVI, and scPoli, and to the cell type and feature interpretation tools Augur and TRADE.

l175: 'Fuzzy' density matrix is not really defined anywhere

The new Results overview explicitly defines the landmark-by-sample density matrix and explains that entries reflect cell-landmark affinity rather than hard membership.

l427: BH -> Benjamini-Hochberg

Corrected; thank you.

Eq 5: Missing a bracket I think

Corrected; thank you.

Fig 2b: A log x axis might be better here.

Figure 2 has been substantially revised, whereby percentages of cells per cluster are not presented anymore. So, the original presentation concern is no longer directly applicable.

Fig 2c,d,e: Some of the y axis ticks here in particular here look a little broken

Corrected; thank you.

Fig S5: DA -> differential abundance, DE -> Differential expression. A guide to what exactly to look at in this figure would also be nice.

We revised Figure S4 (previously Fig. S5) and its legend to make the figure easier to interpret. DA is now defined as differential abundance and DE as differential expression, and we clarify that the key features to inspect are the number of discoveries at q

Figure S7: A brief description of the cell types would be nice somewhere.

Figure S10 (previously Figure S7) has been substantially revised, whereby cell types are not included in the comparison due to the clustering/cell type label-independence structure in the revised manuscript. So, the original presentation concern is no longer directly applicable.

Reviewer #2 (Significance (Required)):

Recently there has been a movement to try and go beyond simple cell type annotation, and here the authors present a consistent and scalable framework for this in R. This work develops new strategies to incorporate existing techniques into scRNA-seq analysis pipelines, whilst maintaining computational scalability.

This work will be particularly interesting to those performing analyses dependent on cell type identification in the R ecosystem, and is demonstrated to be capable of handling the large datasets of modern scRNA-Seq studies.

Although there not much conceptually novel, the implementation appears to be robust, and the scope of applicability is very broad. As such this work will be of broad interest, from those doing basic science on cell lines, to those analysing data from in vivo or human clinical trials.

My background is in bioinformatics, physics, and statistics.

Response:

We appreciate this assessment and agree that the original version did not make the conceptual contributions sufficiently visible. The revised manuscript now distinguishes more clearly between the novel components—the common landmark-by-sample density representation and the contrast-specific supervised embedding (pePC)—and the conventional components (pseudobulk DE after subset selection). We hope the revision better conveys both the practical scalability and the specific methodological contributions, while being transparent about which downstream steps remain standard.

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

Summary: The authors present an R package for landmark-based analysis of multi-sample single-cell genomics datasets, demonstrating its utility through applications to both simulated and clinical data.

Major:

The current benchmarking does not sufficiently establish the advantages of the proposed method over existing alternatives. Most notably, comparisons with metacell-based approaches are absent, despite these representing the most conceptually similar class of methods. The presented benchmark on differential abundance analysis benchmark lacks a scenario with known ground truth, making it impossible to assess false discovery rate control. Additionally, the comparison with miloR should employ graph-based distance approximations, which substantially improve runtime and memory usage (https://www.biorxiv.org/content/10.1101/2023.11.08.566176v1.full). We recognize that exhaustive benchmarking across all possible scenarios is neither feasible nor necessary. However, the current comparisons should be expanded to clarify the specific strengths and limitations of this approach relative to existing methods. This would help readers assess when the proposed tool offers a meaningful advantage over established alternatives.

Response:

We appreciate this careful benchmarking critique. We want to address the metacell comparison directly: we did not add a head-to-head benchmark against metacell-based approaches in this revision. We recognize this as a limitation, and we explain below why we focused the empirical revision on other comparisons.

Metacell methods (MetaCell, SEACells) aggregate similar cells into group-level representations that serve as compressed versions of the single-cell data. tinydenseR addresses a related but distinct modeling objective: it constructs a per-sample density distribution over a shared set of landmarks rather than a single compressed cell-by-gene representation. The downstream analysis modes (differential density, pePC, plsD) operate on this sample-level density matrix, not on aggregated expression profiles. A meaningful comparison would therefore require defining a shared evaluation task, and the most natural such tasks for tinydenseR—sample-level density modeling, contrast-specific embedding—are not standard outputs of metacell frameworks. We have added this conceptual positioning to the Discussion so that readers can assess the relationship between the approaches.

For comparisons more directly aligned with the inferential claims of the framework, the revised manuscript includes synthetic DA and DE scenarios with known ground truth, permutation-based null analyses (Fig. S4), and expanded computational and methodological benchmarking against diffcyt, miloR, Seurat, and cell-level Harmony integration. The miloR benchmarking workflow was updated to use refinement_scheme = "graph," as stated in the Methods and Figure 3 legend and the Material and Methods. Even with graph refinement, miloR remained substantially slower than tinydenseR in our benchmarking setting.

We agree that broader benchmarking across all neighboring method classes remains valuable future work, and we have stated this in the revised manuscript.

It is unclear whether performing integration at the landmark level yields representations comparable to those obtained through cell-level integration. A systematic comparison between landmark-level and cell-level integration would help establish that the compression step does not introduce meaningful loss of biological signal.

Response:

In the revised manuscript, we added a dedicated landmark-level versus cell-level integration benchmark using the Luecken et al. Immune_ALL_human dataset (33,506 cells; 10 batches; 16 annotated cell types). We directly compared tinydenseR landmark-level integration (Harmony on landmarks followed by Symphony projection) against cell-level Harmony on all cells, evaluating integration quality using six metrics: three biological-conservation metrics (MCC for cell-type label transfer, cell-type ASW, graph connectivity) and three batch-mixing metrics (ASW by batch, kBET, batch entropy) (Fig. S5).

Landmark-level integration matched or slightly exceeded cell-level Harmony on four of six metrics, including all three biological-conservation metrics. Cell-level Harmony performed better on the two neighborhood-based batch-mixing metrics, indicating that compression to landmarks did not measurably impair preservation of major biological structure in this dataset, although some reduction in local batch mixing remained.

The landmark-based representation provides a per-sample summarized view that could lend itself to broader applications beyond cell state identification. For example, computing sample-level embeddings from the landmark matrix could enable systematic exploration of similarities and differences across large cohorts. Demonstrating such applications would strengthen the case for this framework's utility and help distinguish it from existing alternatives.

Response:

The revised manuscript demonstrates this broader utility across multiple datasets. The landmark-by-sample density matrix now supports both unsupervised sample embedding (PCA and diffusion-map trajectory) and supervised quantitative embedding via pePC, as described in the new "The tinydenseR Algorithm" subsection and Methods Step 6.

Sample-level embeddings are shown in the synthetic DA/DE benchmarks (Figs. S1–S2), the xenograft treatment comparison (Fig. S6c), the COMBAT COVID-19 analysis (Fig. S7d), the longitudinal NIZ985 clinical-trial dataset (Fig. S10d), and multiple compartments and time points of the PHE885 study (Figs. S12c, S13c, Fig. 2c). Across these examples, the embeddings quantify cohort structure, separate effects of interest from nuisance variation, and summarize the fraction of total variance attributable to modeled contrasts. We agree that this broader utility helps distinguish the framework from alternatives, and we have revised the manuscript accordingly.

Minor:

The authors repeatedly describe their method as "agnostic to technology," but it is unclear what specific advantage this confers. In practice, most methods operating on embeddings and k-nearest neighbor graphs are similarly technology-agnostic. This claim would benefit from either clarification of the specific sense in which this property is distinctive, or a demonstration involving joint analysis of data generated across different technologies.

Response:

The reviewer is right that most methods operating on embeddings and kNN graphs are, in principle, technology-agnostic. Our use of the term is more specific and practical: the same end-to-end framework—from landmark construction through density modeling, embedding, and feature interpretation—is implemented out of the box in tinydenseR for both scRNA-seq and flow/mass/spectral cytometry, with modality-appropriate preprocessing but a shared downstream workflow. The revised Methods now list the supported input formats (Seurat, SingleCellExperiment, H5AnnData, BPCells, dgCMatrix, DelayedMatrix, cytoset) to make this concrete.

We do not demonstrate joint analysis across different technologies in this manuscript, and we have therefore added a note in the Discussion that extending toward joint cross-technology analysis is a natural next step.

The method description in the main text is insufficient to guide the reader through the subsequent applications. Starting with a more detailed overview of the key steps and assumptions underlying the approach would help readers interpret the results presented in later sections.

We agree that the original version did not provide enough methodological guidance before the applications. The revised manuscript adds a dedicated Results subsection, "The tinydenseR Algorithm," that introduces the key steps and assumptions of the framework before the application sections. We also revised Figure 1 and expanded the relevant Methods sections so that the conceptual overview in the main text is clearly connected to the implementation details used in the later applications.

Reviewer #3 (Significance (Required)):

While the tool addresses a relevant need in the field, the underlying summarization approach is conceptually similar to established methods for multi-sample single-cell analysis, including those based on metacells (https://pubmed.ncbi.nlm.nih.gov/31604482/, https://pubmed.ncbi.nlm.nih.gov/35440087/, https://pubmed.ncbi.nlm.nih.gov/35963997/, https://pubmed.ncbi.nlm.nih.gov/36973557/) or data downsampling/sketching (https://pubmed.ncbi.nlm.nih.gov/31176620/). Given the limited conceptual novelty relative to these existing frameworks, the significance of this contribution is difficult to assess without more extensive benchmarking against comparable methods.

Response:

We appreciate this perspective. As discussed in our response to the benchmarking comment above, the revised manuscript positions tinydenseR explicitly as a sample-level landmark-density modeling framework rather than a compression or sketching strategy. The key distinction is that the downstream analyses operate on a per-sample density distribution over landmarks, not on aggregated expression profiles, which is why the empirical revision focused on benchmarks directly aligned with these inferential and computational claims. The Discussion now includes explicit positioning relative to metacell and sketching approaches, and we agree that broader cross-method benchmarking is valuable future work.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors present an R package for landmark-based analysis of multi-sample single-cell genomics datasets, demonstrating its utility through applications to both simulated and clinical data.

Major:

The current benchmarking does not sufficiently establish the advantages of the proposed method over existing alternatives. Most notably, comparisons with metacell-based approaches are absent, despite these representing the most conceptually similar class of methods. The presented benchmark on differential abundance analysis benchmark lacks a scenario with known ground truth, making it impossible to assess false discovery rate control. Additionally, the comparison with miloR should employ graph-based distance approximations, which substantially improve runtime and memory usage (https://www.biorxiv.org/content/10.1101/2023.11.08.566176v1.full). We recognize that exhaustive benchmarking across all possible scenarios is neither feasible nor necessary. However, the current comparisons should be expanded to clarify the specific strengths and limitations of this approach relative to existing methods. This would help readers assess when the proposed tool offers a meaningful advantage over established alternatives. It is unclear whether performing integration at the landmark level yields representations comparable to those obtained through cell-level integration. A systematic comparison between landmark-level and cell-level integration would help establish that the compression step does not introduce meaningful loss of biological signal. The landmark-based representation provides a per-sample summarized view that could lend itself to broader applications beyond cell state identification. For example, computing sample-level embeddings from the landmark matrix could enable systematic exploration of similarities and differences across large cohorts. Demonstrating such applications would strengthen the case for this framework's utility and help distinguish it from existing alternatives.

Minor:

The authors repeatedly describe their method as "agnostic to technology," but it is unclear what specific advantage this confers. In practice, most methods operating on embeddings and k-nearest neighbor graphs are similarly technology-agnostic. This claim would benefit from either clarification of the specific sense in which this property is distinctive, or a demonstration involving joint analysis of data generated across different technologies. The method description in the main text is insufficient to guide the reader through the subsequent applications. Starting with a more detailed overview of the key steps and assumptions underlying the approach would help readers interpret the results presented in later sections.

Significance

While the tool addresses a relevant need in the field, the underlying summarization approach is conceptually similar to established methods for multi-sample single-cell analysis, including those based on metacells (https://pubmed.ncbi.nlm.nih.gov/31604482/, https://pubmed.ncbi.nlm.nih.gov/35440087/, https://pubmed.ncbi.nlm.nih.gov/35963997/, https://pubmed.ncbi.nlm.nih.gov/36973557/) or data downsampling/sketching (https://pubmed.ncbi.nlm.nih.gov/31176620/). Given the limited conceptual novelty relative to these existing frameworks, the significance of this contribution is difficult to assess without more extensive benchmarking against comparable methods.

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Referee #2

Evidence, reproducibility and clarity

The authors describe a new computational framework for the analysis of single-cell RNA-seq data in multiple domains that uses probabilistic cluster assignment for downstream differential expression and abundance analysis. They show that their method outperforms similar methods in certain tasks, and provide computational performance studies to show that this is tractable on large scale RNA-seq datasets.

I congratulate the authors on a well written and interesting manuscript, and the development of what seems like quite a comprehensive analysis package. I particularly appreciate the effort to demonstrate computational performance on large datasets (and of course the great name!). Nevertheless, I have a few minor comments that I think would enhance the presentation and impact of the paper.

From the introduction, it's a little hard to determine what exactly tinydenseR is doing, what the underlying philosophy is, and what the key innovations are. This is especially apparent as the paper then launches straight into the results. The methods section is very comprehensive, however without a 'guide' through this that bridges the gap between the very high level description and the implementation details, a reader could end up getting stuck. So my suggestion would be to add a couple of paragraphs to the introduction that provide this, such that the reader would only need to consult the methods for the real implementation details.

It seems that the probabilities that you get from the fuzzy cluster assignment aren't necessarily well calibrated. After the Benjamini-Hochberg correction this might end up not being a issue, so it would be good to see that the FDR that you mention in line 431 is indeed roughly how many discoveries are made under the null hypothesis for some indicative configurations, and whether this deviates significantly from the expectation.

The rest of my comments are minor and only related to the presentation:

• l71 (and elsewhere): A bit more detail about these datasets would be nice (what the trajectories are, etc, rather than just the configuration).

• l73: The language is a little different between this description and the figures, so it's a little hard to keep track of the correspondence.

• Fig S2 (and others): I know that these are supplemental figures, but they're quite dense and hard to read (both conceptually and in terms of the font size). For something supporting a direct claim in the paper, it would be nice to have one or two plots in the main body of the paper that summarise all of the evidence in these denser supplementary plots.

• l106: This is a little confusing to read (not clear whether these are single and double knock outs or just wild type and double knock out).

• l162: In general it would be nice to link this back to some of the choices made in tinydenseR compare to other techniques.

• l175: 'Fuzzy' density matrix is not really defined anywhere

• l427: BH -> Benjamini-Hochberg

• Eq 5: Missing a bracket I think

• Fig 2b: A log x axis might be better here.

• Fig 2c,d,e: Some of the y axis ticks here in particular here look a little broken

• Fig S5: DA -> differential abundance, DE -> Differential expression. A guide to what exactly to look at in this figure would also be nice.

• Figure S7: A brief description of the cell types would be nice somewhere.

Significance

Recently there has been a movement to try and go beyond simple cell type annotation, and here the authors present a consistent and scalable framework for this in R. This work develops new strategies to incorporate existing techniques into scRNA-seq analysis pipelines, whilst maintaining computational scalability.

This work will be particularly interesting to those performing analyses dependent on cell type identification in the R ecosystem, and is demonstrated to be capable of handling the large datasets of modern scRNA-Seq studies.

Although there not much conceptually novel, the implementation appears to be robust, and the scope of applicability is very broad. As such this work will be of broad interest, from those doing basic science on cell lines, to those analysing data from in vivo or human clinical trials.

My background is in bioinformatics, physics, and statistics.

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Referee #1

Evidence, reproducibility and clarity

1) Overall, this manuscript presents a landmark-based strategy for scaling sample-level differential abundance and differential expression analyses to atlas-sized single-cell datasets by summarizing cells through fuzzy cell-landmark memberships and then applying standard sample-level modeling. The approach is promising for computational efficiency, but several key methodological claims and design choices would benefit from clearer justification and stronger empirical validation.

2) The manuscript's main methodological novelty appears to be computational/scalable representation learning via landmarking and fuzzy cell-landmark densities. However, for differential expression within cell states, the inferential procedure is standard pseudo-bulk + limma/voom and still relies on discrete subset definitions (clusters/cell types, or landmark bins) and downstream annotation for biological interpretation. The authors should clarify that "clustering-independent" primarily applies to the DA representation/testing, and strengthen evidence that landmark-level subsets provide materially different biological resolution than simply clustering a subsample.

3) The method treats UMAP fuzzy graph weights as "connection probabilities" and uses their sums to estimate sample-level abundance around each landmark. Please clarify (i) how sensitive the density matrix is to the UMAP membership construction (e.g., choice of parameters, the per-cell membership mass constraint), and (ii) why this is an appropriate abundance surrogate in the context of sample-level inference.

4) The landmark selection step caps landmarks at 10% of cells per sample (and an overall cap of 5,000 landmarks by default), but the rationale for these thresholds is not clearly justified. Additionally, interaction between the per-sample cap and the global 5,000 landmark cap: when the global cap is binding, how are landmarks redistributed across samples, and does this induce unequal representation across samples with different cell yields?

Significance

This manuscript introduces a practical landmark-based framework that makes sample-level differential abundance and expression analyses feasible at atlas scale by summarizing large cell collections through a reduced set of representative cells and fuzzy cell-landmark memberships, then leveraging well-established sample-level linear modeling. The main strengths are its emphasis on scalability, a clear engineering workflow that can be applied across large studies, and a unified representation that can support multiple downstream analyses. The main limitations are that key inferential components remain conventional once subsets are defined, biological interpretation still relies on clustering/label transfer and downstream annotation, and several core design choices (e.g., treating UMAP fuzzy weights as "probabilities" and the default landmark caps) would benefit from stronger justification and sensitivity analyses to support the paper's broader claims about cluster-independence and biological resolution.