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Reply to the reviewers

1. General Statements

We express our gratitude to the reviewers for their time and insightful comments, which have significantly contributed to the enhancement of our manuscript. We believe that the thoughtful critiques and suggestions have substantially improved the overall quality of our work. The changes made in the revised manuscript were highlighted in red. Below, we provide a point-by-point response to each comment, addressing the concerns raised by the reviewers.

2. Point-by-point description of the revisions

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

*Summary: *

*In the current study, Li et al investigated how TGF-beta signaling is controlled by protein abundances. Computational modeling and experiments indicated that the abundance of TGFBR1 and TGFBR2 affects the signaling, and those with lower abundance affect the signaling more, resembling Liebig's law of the minimum. Specifically, they showed that by using multiple cell lines with a different abundance of receptors, modulation of expression of the less abundant receptor impacts the signaling, which is measured by SMAD2 nuclear-to-cytosol ratio and/or relative phospho-SMAD2 level. Also, by using a light-induced interaction system, they showed that the signaling is dependent on the concentration of receptor complex when both receptors are expressed at similar amounts. *

*Major comments: *

*Computational predictions support the authors' idea. The computation and the experiments are well-documented. And it would gain substantially if the authors fill the gap between the predictions and the experiments as follows. *

*In Figure 4, the authors showed that perturbation on receptors with lower expression levels in each cell line changes the phospho-SMAD2 level. Although the data looks consistent with their claim, the result is only qualitative. The authors established a computational model in the former sections, thus it would be of great interest to assess if the experimental results quantitatively match the computational prediction. *

Response: The reviewer suggests that our work could benefit from a quantitative comparison between computational predictions and experimental data shown in Figure 4. We appreciate this suggestion. Given the challenges in obtaining precise quantification of TGFBR1 protein due to antibody issues (see the response to comment #2 from reviewer 2), a direct quantitative comparison between model predictions and experimental results is difficult. Our model predictions about the control principle with Liebig's law of the minimum should be interpreted qualitatively, rather than a strict quantitative law. We have explicitly indicated in the revised manuscript that our siRNA knockdown experiments are to qualitatively test our model predictions.

*In Figure 5, the authors computationally predicted that the expression level of receptors is correlated with SMAD2 N2C levels 1 hour after stimulation, and the strength of negative feedback with SMAD2 N2C levels 8 hours after stimulation. Because the authors employed iRFP-SMAD2 system, the prediction could be verified experimentally, at least the prediction on SMAD2 N2C 1 hour after stimulation could be checked. (In a sense, this is partially verified by the data in Figure 7, where both receptors are expressed at similar levels). It would gain substantially if the authors could verify the computational prediction in Figure 6. Since the authors stated in the introduction that "The same TGF-beta ligand can initiate different signaling responses depending on the cellular context, but the underlying control principle remains unclear...Together, these results revealed an effect of the minimum control in the TGF-beta pathway, which may be an important principle of control in signaling pathways with context-dependent outputs.", experimental verification of the prediction done in Figures 4-6 will be very important. Or the authors should stress that these points are only predicted by computational models. *

__Response: __The reviewer recommends verifying the model predictions in Figure 6 experimentally, particularly regarding SMAD2 N2C levels 1 hour after stimulation. We appreciate this valuable suggestion, which was also raised by reviewer 2. In response, we conducted experiments as recommended by reviewer #2, in which imbalanced expression of TGFBR1 and TGFBR2 was achieved by transfecting optoTGFBR1 or optoTGFBR2 plasmids into optoTGFBRs-HeLa cells, which initially expressed similar levels of both receptors. Western blot analysis confirmed the desired imbalance (Figure S13).

Consistent with the model predictions (Figure 6), the strong correlation between SMAD2 N2C fold change response at 1h and optoTGFBR2-tdTomato expression levels persisted in single cells when optoTGFBR1 was overexpressed (Figure 8A). Conversely, the high correlation between nuclear SMAD2 signaling and optoTGFBR2-tdTomato expression levels vanished at single cell level when optoTGFBR2 was overexpressed (Figure 8B). These experimental results validate our model predictions, confirming that the SMAD2 signaling is determined by the low abundance TGF-beta receptor in single cells. Incorporating these experimental validations enhances the quantitative support for our model predictions and clarifies the relationship between TGF-beta receptor abundance and signaling outcomes in single cells.

*As written in the below "Significance" section, the result is, in a sense, obvious. It should be stated that because the study utilized a slightly high concentration of TGF-beta in the experiments, it might be natural that the low-abundance receptor becomes a bottleneck of the signaling. It would gain to assess how receptor abundance affects signaling with the stimulation of lower concentrations of TGF-beta, or to examine the computational model if the low abundance of a receptor becomes a bottleneck of signaling because of saturation. Also, it is highly recommended to discuss the physiological implication of the current study, taking into account the experimental conditions used. *

Response: We appreciate the reviewer's insightful comments regarding the concentration of TGF-beta used in our experiments and the potential influence on the model predictions. In our experiments and model simulations, we utilized 100 pM TGF-beta, equivalent to 2.5 ng/mL (not 4.4 ng/mL as calculated by the reviewer). This concentration is a widely used dose in TGF-beta signaling studies. The reviewer's suggestion to explore how varying TGF-beta concentrations might influence the minimum control concept prompted us to extend our computational simulations. We used the extended model to perform simulations with lower TGF-beta concentrations (25 pM, equivalent to 0.625 ng/mL, and 10 pM, equivalent to 0.25 ng/mL). The results, depicted in Figure S7 of the revised manuscript, reaffirm that even at lower TGF-beta stimulations, a low abundance of a TGF-beta receptor acts as a bottleneck for SMAD2 signaling.

Following the reviewer’s suggestion, we have incorporated additional paragraphs to discuss the physiological implications and potential limitations of our study (Page 16-17 in the Main text).

It is pertinent to note that while the concept of TGF-beta signaling response being dictated by the minimum abundance of TGF-beta receptors may seem intuitive or even obvious, theoretical and experimental validations are crucial. As demonstrated in Figure S1B, our new simulation results from the minimal model illustrate similar response profiles when a high binding affinity (K1) is set for ligand-receptor interactions (Figure S1A). However, with a small binding affinity (K1), the minimal model indicates that TGF-beta signal response remains proportional to the product of TGFBR1 and TGFBR2 abundance and can be sensitive to the change of high abundance receptor in some region (Figure S1B). This highlights that the observed response patterns aligning with Liebig's law of the minimum depend on the binding affinity of ligand-receptor interactions in our minimal model. Consequently, the intuitive idea about Liebig's law of the minimum is not necessarily true theoretically. Moreover, given the non-linearity of the TGF-beta network, this complexity introduces an additional layer of uncertainty regarding the applicability of the minimum control principle to TGF-beta responses. This uncertainty led us to develop an extended model, with parameter values either experimentally measured or estimated from time course experimental data. The extended model predicted a similar minimum control principle at the TGF-beta receptor level, inspiring us to validate this prediction through diverse experiments. While we acknowledge the intuitive nature of our findings, we believe it is important for the field to prove this expectation, as emphasized by reviewer 4.

Reviewer #1 (Significance (Required)):

*TGF-beta signaling is one of the most rigorously studied pathways both computationally and experimentally. As written in the introduction of the manuscript, it is still unknown how the variability of responses arises not only between cell types but also differences among cells of single cell type. Studies showed that protein abundance accounts at least partly for a source of cell variability in TGF-beta signaling. While former studies examined the variability in SMAD protein abundance, the uniqueness of this study is that it focused on the abundance of TGF-beta receptors. *

*Given that both TGFBR1 and TGFBR2 are involved in the signaling, however, it's not difficult to imagine that a less abundant receptor affects the signaling more than the other, and serves as a bottleneck for the signaling. Specifically, because a slightly high concentration (100pM = 4.4 ng/mL of TGF-beta; other studies used much lower conc., e.g. 0, 0.03, 0.04, 0.07, and 2.4 ng/mL in Frick et al, PNAS, 2017, and 0, 1, 2.5, 5, 25, and 100 pM in Strasen et al, Mol Syst Biol, 2017) is used throughout the experiments to check cell-cell variability and the effect of receptor abundance in the current study, the formation of the receptor-ligand complex may be quite fast and be saturated at the level where the receptor with lower abundance is exhausted. In the reviewer's humble opinion, the authors' statement that this is Liebig's law of the minimum sounds a bit exaggerated. *

Nevertheless, the study is of some value because it utilized both computational and experimental analysis to show it is indeed the case. Of note, the current study showed that the variability in the different proteins leads to the variability in different time points, namely, the variability in the receptor abundance leads to the variability 1 hour after stimulation, while that in negative feedback strength leads to the variability 8 hours after stimulation. If the authors fill a small gap between their computational analysis and experimental verification, the study will be of interest to the specialist in the field.

__Response: __We are grateful for the valuable feedback provided by the reviewer. The concerns related to the TGF-beta dose have been thoroughly addressed in our responses to previous comments. Regarding the observation that the term "Liebig's law of the minimum" may sound a bit exaggerated, we acknowledge this consideration. We have refined the title to "Liebig’s Law of the Minimum in the TGF-β/SMAD Pathway," specifying its relevance to SMAD signaling exclusively, as non-SMAD signaling was not within the scope of this study. We appreciate the reviewer's constructive feedback and hope these adjustments enhance the specificity and accuracy of our manuscript.

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

Li et al. present an interesting and intuitive concept for the sensitivity and heterogeneity of biological networks: When two or more proteins form a functional complex, it is the limiting component with the lowest concentration that is most sensitive to perturbations and whose fluctuations dictate cell-to-cell variability of complex function. The authors apply this concept to the TGFb pathway and discuss sensitivity of SMAD signaling towards TGFb receptor I and II fluctuations. The paper is clearly written and convincing, but some improvements in the experimental validation would be beneficial as detailed further below.

1) The authors claim that the ratio of TGFb receptor I and II is very different across cell lines (Fig. 1) and use this observation for the validation of their model in Fig. 4. However, the relative expression TGFb receptor levels are purely based on RNAseq data which does not necessarily imply similar behavior at the protein level, especially on the cell surface. To address this issue, the authors should ideally provide absolute Western blot measurements of TGFbRI at the protein level to complement their absolute quantification of TGFbRII (Fig. S2). At the very least they should show that the observed relative expression levels of TGFbRI and II at the protein level (Figure S7) are correlated to differences in RNA levels (Fig. 1) using protein quantification. They should also confirm that similar receptor ratios for these receptors at the RNA level are observed in other published RNAseq datasets of the same cell lines (e.g., ENCODE for HepG2 and published RNAseq studies in HaCaT). Furthermore, they might take into account published mass spec datasets for quantifications of TGFbR protein levels.

Response: We appreciate the reviewer's thorough evaluation and constructive suggestions.

(A) Absolute quantification of TGFBR1: We acknowledge the importance of obtaining absolute quantification of TGFBR1 protein similar as what we have done for TGFBR2 protein (Figure S2). Despite significant efforts, our attempts to achieve this were hindered by challenges with available TGFBR1 antibodies and recombinant TGFBR1 proteins. Many commercial antibodies failed negative controls with TGFBR1 knockdown samples, while others validated TGFBR1 antibodies could not recognize the available recombinant TGFBR1 protein standards.

Although many mass spectrometry proteomics data available for different cell lines, it is difficult to convert these MS quantitative values to absolute protein abundance as mentioned in a recent publication (Nusinow et al.,bioRxiv 2020.02.03.932384): “Importantly, these values are all relative values to the other values for that same protein and not absolute values. This means that comparing the levels of different proteins to each other without using something like a correlation to standardize values won’t produce meaningful results.”

We share the reviewer's concern and fully agree that obtaining this absolute quantification is crucial. However, at the present stage, technical limitations prevent us from providing this information for TGFBR1. We commit to pursuing this aspect when feasible in the future.

(B) Validation of relative TGF-beta receptor expression ratios: Following the reviewer's suggestion, we conducted additional analyses to validate the relative expression ratios of TGFBR1 and TGFBR2 using different RNA-Seq databases. The results, presented in Table S1, demonstrate consistent imbalances in TGFBR1-to-TGFBR2 ratios across HepG2 and RH30 cell lines from various data sources, reinforcing the reliability of our observations.

(C) Correlation between RNA and protein expression: We appreciate the reviewer highlighting the challenges associated with correlating RNA and protein expression. Indeed, the correlations between RNA and protein levels vary widely, and direct comparisons can be challenging. To address this, we referenced a recent study (Nusinow et al., Cell 2020, 180:387), which reported that the protein data of TGFBR1 and TGFBR2 were highly correlated with the corresponding RNA data from the same cell line (Spearman’s correlation: 0.672 for TGFBR1, 0.771 for TGFBR2) based on quantitative proteomics and RNA expression data from 375 cancer cell lines.

2) Figure 4: To better judge the reproducibility of the knockdown titration, it would be good to show the different siRNA concentrations as a color code- Alternatively, TGFBR expression could be plotted as a function of the siRNA concentration in a Supplemental Figure, showing the effects of individual replicates.

Response: We thank the reviewer for the suggestion to enhance the clarity of the knockdown titration data. In response, we have now presented the quantified experimental data from three replicates with different colors in Figure 4. Additionally, we have created Figure S9 that plots the expression levels of relative TGFBR1 and TGFBR2 as a function of siRNA concentration, providing a more detailed view of the effects across individual replicates.

3) The simulations in Figs. 5 and 6 show that SMAD signaling fluctuations are mainly determined by cell-to-cell variability of receptor levels when using the SMAD nucleocytoplasmic ratio as a readout, and this is especially true for early time points. For downstream cellular responses, the absolute concentration of phosphorylated SMAD (complexes) in the nucleus is likely more relevant. Based on the authors work and evidence from the literature, I expect that this quantity will likely be heavily be influenced by receptor levels as well, but fluctuations in SMAD expression will play an important role as well. The authors should discuss this issue, and clarify that normalized quantities like SMAD N2C and pSMAD/SMAD mostly characterize receptor-level fluctuations while filtering SMAD fluctuations.

__Response: __We acknowledge the importance of discussing the relevance of different readouts in our study. In the revised manuscript, we have incorporated a discussion addressing this issue. Specifically, we highlight that while the SMAD nucleocytoplasmic ratio is sensitive to cell-to-cell variability in low abundance receptor levels, the absolute concentration of phosphorylated SMAD in the nucleus may be more relevant for downstream cellular responses (e.g.: gene expression). We have cited the work by Lucarelli et al, which demonstrated that variations in SMAD abundance could modulate the balance of different SMAD complexes, thereby regulating heterogeneous gene expression in diverse cell types (Lucarelli et al., Cell Systems 2018).

4) The single-cell measurements in Fig. 7 are interesting, but can only partially be seen as a direct validation of the model predictions, as it seems expected that varying the total input by introducing co-fluctuations in both receptors heavily influence the SMAD level. Wouldn't it be possible to design more specific validation experiments, in which the receptor co-expression construct (Fig. 7C) is used for baseline optoTGFBR expression and combined with an individual expression construct for one of the opto-receptors? This way, the authors could establish different regimes, in which one of the two receptors becomes dominant, and the impact fluctuations could be analyzed in a larger receptor expression space. Of course, a full validation of all possible scenarios is not necessary, but it would, for instance, be valuable to see whether the strong dependency of SMAD signaling of TGFBR2 levels vanishes when TGFBR2 is expressed at a higher level than TGFBR1.

Response: We appreciate the insightful comments and suggestions provided by the reviewer. Based on these recommendations, we have conducted additional experiments to further validate our model predictions. Reviewer 1 also raised this point, we quote our aforementioned response here: “consistent with the model predictions (Figure 6), the strong correlation between SMAD2 N2C fold change response at 1h and optoTGFBR2-tdTomato expression levels persisted in single cells when optoTGFBR1 was overexpressed (Figure 8A). Conversely, the high correlation between nuclear SMAD2 signaling and optoTGFBR2 expression levels vanished at single cell level when optoTGFBR2 was overexpressed (Figure 8B). These experimental results validate our model predictions, confirming that the SMAD2 signaling is determined by the low abundance TGF-beta receptor in single cells. Incorporating these experimental validations enhances the quantitative support for our model predictions and clarifies the relationship between TGF-beta receptor abundance and signaling outcomes in single cells.”

**Referees cross-commenting**

Comments from R2: I agree with most comments of the other reviewers, and highlight the most important overlaps with my comments below.

I agree with R1 that the model validation in Fig. 7 is incomplete and think that this will be a key point to improve the quality of the manuscript (see also my reviewer comment 4)

In line with R3 and R4, I think that the SMAD N/C simulations do not necessarily imply effects on TGFb target gene expression, cell fate decisions or human pathologies. The significance of the results for cellular behavior should be discussed (see also my comment 3)

__Response: __We are grateful for the reviewer's thoughtful comments. These comments have been now addressed (see our responses to the corresponding comments).

Reviewer #2 (Significance (Required)):

The manuscript presents an interesting and intuitive concept for the sensitivity and heterogeneity of biological networks. The authors apply this concept to the TGFb pathway and discuss sensitivity of SMAD signaling towards TGFb receptor I and II fluctuations.

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

*Summary: *

*This is an interesting study that examines the output of the TGF-Beta pathway and how abundance/dosage can determine the signaling response in single cells across multiple cell types. The study is primarily mathematical. The focus is on the Type 1 and 2 TGF-Beta receptors driving nuclear SMAD2 expression. The authors observe that SMAD2 phosphorylation is sensitive to variations in the lower levels of either receptor but robust at variations of high abundance of the receptor reflected through SiRNA experiments shown in Figure 4. Their conclusion is that the feature is consistent with Liebig's law of the minimum- where in this case- a low abundance of the receptor serves as the rate-limiting step in signaling for this pathway. *

*Major comments: *

*- While the data as presented are interesting, it is unclear as to whether the abundance regulates biological function. SMAD2 phosphorylation is shown with some nuclear translocation. However, TGF-Beta target gene activation is not shown, and this needs to be completed. *

Response: We appreciate the reviewer's constructive comment. We have conducted new experiments and included quantitative real-time PCR data in the revised manuscript to evaluate the impact of TGFBR1 and TGFBR2 knockdown on the expression of TGF-beta target genes, such as SMAD7, PAI1, and JUNB. The results, presented in Figure S11, demonstrate differential sensitivity of these genes to the downregulation of TGFBR1 and TGFBR2 in various cell lines (HaCaT, HepG2, and RH30). Specifically, the expression of SMAD7, PAI1, and JUNB is sensitive to TGFBR2 knockdown in RH30 cells, while it is sensitive to TGFBR1 knockdown in HepG2 cells. HaCaT cells, expressing similar levels of both receptors, show comparable sensitivities to reductions in both TGFBR1 and TGFBR2. These findings provide additional insights into the regulatory role of TGF-beta receptor abundance on downstream target gene activation, complementing our study's focus on SMAD2 phosphorylation and nuclear translocation.

*- In addition, it is unclear as to what happens to SMAD3 and SMAD4 which are expressed endogenously in this setting. How are these other TGF-Beta signaling molecules addressed by these observations? *

__Response: __Thank you for bringing up this important point. In our study, the expression levels of endogenous SMAD2 and SMAD4 were found to be similar across HaCaT, RH30, and HepG2 cells. However, SMAD3 expression was notably lower in RH30 and HepG2 compared to HaCaT cells. The central conclusion of our study is based on the observed common control principle, which hinges on the relative expression levels of TGFBR1 and TGFBR2. Consequently, the applicability of this principle is more pertinent when comparing signal responses within the same cell type.

We acknowledge the relevance of endogenous SMAD proteins, and in the revised manuscript, we have expanded our discussion on how differences in SMAD protein expression levels and potential mutations (page 16 in main text), as observed in certain cancers, could influence the formation of homo- and hetero-oligomeric SMAD complexes. These considerations contribute to a more comprehensive understanding of downstream gene expression responses, as discussed in the work of Lucarelli et al. (Cell Systems 2018).

*-Specific biological readouts- cell differentiation etc. are not examined and would need to be provided and discussed. Therefore, the claims put forward while interesting require additional experiments examining SMAD2 target gene activation and biological readouts. *

__Response: __We appreciate this valuable suggestion. While we acknowledge the importance of exploring long-term biological responses, including cell differentiation, it is crucial to note that specific biological readouts are not solely dependent on SMAD signaling; they also involve other non-SMAD signaling pathways. Additionally, these responses are highly cell type-specific. Undertaking extensive investigations into these responses would extend beyond the current scope of our work. Nevertheless, we have discussed this topic in the revised manuscript (page 16 in main text).

Following the reviewers’ suggestion on examining TGF-beta target genes, we have performed experiments examining the expression of SMAD7, PAI1, and JUNB with respect to the changes of TGFBR1 and TGFBR2, respectively (see our response to the first major comment of this reviewer).

*- Lastly, statistical analyses are not provided and would need to be provided. For instance, in Figure 4, how many experiments were replicated and statistical analysis performed for this Figure? *

__Response: __In addressing this concern, we conducted three siRNA knockdown titration experiments for each cell line, as detailed in the figure legend. Due to batch effects, different percentages of TGF-beta receptors were knocked down in different experiments using the same concentration of siRNA. To transparently present the data, we utilized a scatter plot. Following the suggestion from reviewer 2, we have further enhanced the clarity of our data presentation by labeling the results of different experiments with a color code. In addition, we have performed statistical analysis of TGF-β receptor fold-change effects leading to a 50% reduction in the P-Smad2 response compared to that in the non-targeting siRNA control group (EC50) during siRNA knockdown experiments (Figure S10). The results of this analysis unveil significant differences in the sensitivities of pSMAD2 responses to variations in TGFBR1 and TGFBR2 within RH30 and HepG2 cells.

Reviewer #3 (Significance (Required)):

*- Conceptually this is an important study because dosage is a prominent issue in TGF-Beta signaling. For instance, in my field of expertise- mouse models of TGF-beta signaling e.g. SMAD2 knockouts- the cancer phenotypes are evident in haploid animals. Yet how and why dosage plays such a large role in tumorigenesis remains unclear. *

__Response: __We sincerely appreciate your recognition of the conceptual importance of our study in addressing the dosage-related complexities of TGF-beta signaling. Your insights into dosage effects in mouse models, particularly in haploid animals, highlight the relevance of our work underlying tumorigenesis. We have incorporated relevant citations and expanded our discussion in the revised manuscript, providing additional context to the importance of dosage in tumorigenesis (page 18 in main text).

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

Summary: In this study, Li and co-workers combined computational modeling and experimental analysis to study the dependence of the output of the TGF-beta pathway on the abundance of signaling molecules in the pathway, mainly the most upstream regulators of SMAD2, TGFbeta type I and type II receptors. They showed by a combination of biochemical studies (mainly pSmad2 WB and type I/II receptor expression profiling) in HaCaT and HeLa cells as well as stable optogenetical receptor variants expressed by those cell lines, that TGF-beta receptor abundance influences signaling outputs using the concept of Liebigs law of the minimum, meaning that the output-modifying factor is the signaling protein that is most limited, to determine signaling responses across cell types and in single cells.

*Major comments: *

The study is very interesting, the combination of biochemistry and computational modeling to better understand the compexity of the TGFbeta pathway is very much required in the field and should stimulate others to further expand this approach.

__Response: __Thank you for the positive evaluation of this work.

*However, the authors must further explain that the model depicted here to explain pathway kinetics and dynamics lacks multiple crossroads and feedbacks and is until now oversimplified in the manuscript. They have mentioned receptor internalization and recycling, nuclear import and export of SMAD protein, and the feedback regulations e.g. by SMADs regulating receptor expression. Beyond, there is non- SMAD signaling (Derynck et al.; SMAD Linker regulation, deRobertis et al.), different receptor oligomerization modes (Ehrlich/Henis et al.) and heteromeric receptor complexes of TGFbeta receptors known (Hill et al.), that further diversify beyond these mentioned mechanisms. It is understandable that the mathematical model cannot include those considerations to date, however, they must be further explained and commented on to allow that this model can be expanded in the future. *

Response: We acknowledge that there are multiple crossroads and feedbacks that exist in the TGF-beta signaling pathway that have not been explicitly incorporated into our model. We appreciate the reviewer's understanding that current model cannot include these considerations and his/her suggestions for potential future extensions. In the revised manuscript, we have mentioned one of the limitations of our model: non-Smad signaling and crosstalk with other signaling pathways were not considered for simplicity. We have also discussed how to expand this model by including these regulations when more quantitative data are available in the future (page 16-17 in main text).

*A myriad of research labs focus on these intricate fine tuning ot the TGFbeta pathway by those mechanisms which makes the difference between "good" TGFbeta signaling and "bad" TGFbeta signaling in different context and this complexity must be acknowledged by more introduction and discussion. *

Response: In the revised manuscript, we have added an introduction and discussion about the dual role of TGF-beta signaling (page 4 and page 18 in main text).

*The model here will be important to explain *

*A: the mode of heterooligomeric TGFbeta/BMP receptor assemblies as e.g. found in pathological conditions and *

B: Can maybe explain the formation of mixed SMAD complexes as activated by lateral signaling comprising TGFbeta *and BMP receptors once one receptor is of lower abundance to form a high affinity complex. *

*It is therefore required to comment on these aspects at multiple points in the manuscript. *

*It is very important that the visual model used in this manuscript depicts on the possibility, that a TGFbeta type I receptor can team up with e.g. another TGFbeta type I receptor together with two TGFbeta type II receptors but also with an activin type II receptor or that a BMP type I receptor (e.g. ALK1) can form heterooligomeric complexes with ALK5 (TGFbeta type I). *

__Response: __Thank you for this comment. We cited the relevant work (Ramachandran et al, eLife 2018; Szilagyi et al, BMC Biology 2022) and added a discussion about the complexity of the mode of heterooligomeric TGFbeta/BMP receptor assemblies and its effect on the induction of mixed SMAD complexes (page 17 in the main text).

*While the use of optogenetical TGFbeta receptor biosensors is highly interesting, their mode of oligomerization is not yet fully described. It is not known if those biosensors behave like wt receptors in terms of oligomerization and ligand binding. This should be mentioned somewehere. For this reason, the authors should also consider to draw the TGFbeta receptor complex in the cartoons with more detail towards the heterooligomeric assembly that is standard to the field. *

__Response: __The reviewer is correct that the optogenetic TGF-beta receptors might behave differently from the natural TGF-beta receptor system in terms of ligand binding. We have added this point in the Discussion part to highlight the potential difference between the optogenetic TGF-beta systems and the wild-type system (page 16 in the main text).

*While the general finding is not surprising (manipulating the receptor with the lowest abundancy has the biggest impact on signaling output) the methods and models used here are very important to the field to proof that this expectation is actually true and can be experimentally addressed by a combination of bioinformatics and biochemistry. The model developed will be valuable to expand to much more complex and interesting questions in TGFbeta signaling and possibly also BMP signaling e.g. in pathological context (see below). *

*Minor comments: *

*The authors should discuss their findings in the context of: *

• non-Smad signaling outputs (similar or different to the observations on pSMAD2)*
• What do these findings mean for e.g. human pathologies, where type I or type II receptor expression is altered? *
• Can those findings integrate into the "switch" in TGFbeta signaling? *
• How do these findings translate towards BMP SMAD 1/5/9 signaling? * Response: First, we sincerely appreciate the reviewer’s recognition that our work is very important to the field in proving that manipulating the receptor with the lowest abundance has the biggest impact on signaling output. The reviewer’s suggestions about discussing our work in the context of non-Smad signaling, BMP SMAD1/5/9 branch, and the relevance to the dual role of TGF-beta signaling are all constructive. We have incorporated these suggestions and discussed them in the revised manuscript (page 17 in the main text).

Reviewer #4 (Significance (Required)):

*The manuscript is novel and interesting, partiular the combination of bioinformatical and biochemical approaches. The use of optogenetics is state-of-art while some more care should be given to interpretation of results with optogenetical TGfbeta receptor biosensors, is is not known if they really behave similar in terms of receptor oligomerization and signaling. Also it is not shown how their interactome in terms of effector proteins looks like that can potentially influence SMAD signaling output (e.g. Phosphathases to SMADs known to interact with wt receptors). *

*The models drawn need to depict more accurately on the nature of type I and type II receptor complexes (heterotetrameric) and high affinity towards the ligand. The current versions are too oversimplified at this stage. The pathway crosstalks and feedbacks need to be more visible, in order for non experts to not draw too simple conclusions from the visual representations presented in this MS. Particularly the work by Hill and co-workers on receptor oligomerization and SMAD shuttling and feedback need to be included. *

Overall, the manuscript is very significant to the field.

__Response: __We would like to thank the reviewer again for his/her positive evaluation of the novelty and significance of our work. We have taken the reviewer's comments into consideration and made revisions to the manuscript. We now provide more information on the limitations of our current model and the optogenetic TGF-beta receptor biosensors in the Discussion section. We have also included more details about the receptor complex nature and the high affinity towards the ligand. The ligand receptor complex in the model is now drawn as heterotetrametric complex (1 ligand dimer with two TGFBR1s and two TGFBR2s). Additionally, we have incorporated information about pathway crosstalks and feedbacks, giving a more comprehensive view for non-experts. The work by Hill and co-workers on receptor oligomerization, SMAD shuttling, and feedback has been included in the revised manuscript to provide a more complete and accurate representation of the current knowledge in the field.

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

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Referee #4

Evidence, reproducibility and clarity

Summary:

In this study, Li and co-workers combined computational modeling and experimental analysis to study the dependence of the output of the TGF-β pathway on the abundance of signaling molecules in the pathway, mainly the most upstream regulators of SMAD2, TGFbeta type I and type II receptors.

They showed by a combination of biochemical studies (mainly pSmad2 WB and type I/II receptor expression profiling) in HaCaT and HeLa cells as well as stable optogenetical receptor variants expressed by those cell lines, that TGF-β receptor abundance influences signaling outputs using the concept of Liebigs law of the minimum, meaning that the output-modifying factor is the signaling protein that is most limited, to determine signaling responses across cell types and in single cells.

Major comments:

The study is very interesting, the combination of biochemistry and computational modeling to better understand the compexity of the TGFbeta pathay is very much required in the field and should stimulate others to further expand this approach.

However, the authors must further explain that the model depicted here to explain pathway kinetics and dynamics lacks multiple crossroads and feedbacks and is until now oversimplified in the manuscript. They have mentioned receptor internalization and recycling, nuclear import and export of SMAD protein, and the feedback regulations e.g. by SMADs regulating receptor expression. Beyond, there is non- SMAD signaling (Derynck et al.; SMAD Linker regulation, deRobertis et al.), different receptor oligomerization modes (Ehrlich/Henis et al.) and heteromeric receptor complexes of TGFbeta receptors known (Hill et al.), that further diversify beyond these mentioned mechanisms. It is understandable that the mathematical model can not include those considerations to date, however, they must be further explained and commented on to allow that this model can be expanded in the future. A myriad of research labs focus on these intricate fine tuning ot the TGFbeta pathway by those mechanisms which makes the difference between "good" TGFbeta signaling and "bad" TGFbeta signaling in different context and this complexity must be acknowledged by more introduction and discussion.

The model here will be important to explain

A: the mode of heterooligomeric TGFbeta/BMP receptor assemblies as e.g. found in pathological conditions and

B: Can maybe explain the formation of mixed SMAD complexes as activated by lateral signaling comprising TGFbeta nd BMP receptors once one receptor is of lower abundance to form a high affinity complex.

It is therefore required to comment on these aspects at multiple points in the manuscript.

While the use of optogenetical TGFbeta receptor biosensors is highly interesting, their mode of oligomerization is not yet fully described. It is not known if those biosensors behave like wt receptors in terms of oligomerization and ligand binding. This should be mentioned somewehere.

For this reason, the authors should also consider to draw the TGFbeta receptor complex in the cartoons with more detail towards the heterooligomeric assembly that is standard to the field.

It is very important that the visual model used in this manuscript depicts on the possibility, that a TGFbeta type I receptor can team up with e.g. another TGFbeta type I receptor together with two TGFbeta type II receptors but also with an activin type II receptor or that a BMP type I receptor (e.g. ALK1) can form heterooligomeric complexes with ALK5 (TGFbeta type I).

While the general finding is not surprising (manipulationg the receptor with the lowest abundancy has the biggest impact on signaling output) the methods and models used here are verxy important to the field to proof that this expactation is actually true and can be experimentally adressed by a combination of bioinformatics and biochemistry. The model developed will be valuable to expand to much more complex and interesting questions in TGFbeta signaling and possibly also BMP signaling e.g. in pathological context (see below).

Minor comments:

The authors should discuss their findings in the context of: 1. non- Smad signaling outputs (similar or different to the observations on pSMAD2) 2. What do these findings mean for e.g. human pathologies, where type I or type II receptor expression is altered? 3. Can those findings intergate into the "switch" in TGFbeta signaling? 4. How do these findings translate towards BMP SMAD 1/5/9 signaling?

Significance

The manuscript is novel and interesting, partiular the combination of bioinformatical and biochemical approaches. The use of optogenetics is state-of-art while some more care should be given to interpretation of results with optogenetical TGfbeta receptor biosensors, is is not known if they really behave similar in terms of receptor oligomerization and signaling. Also it is not shown how their interactome in terms of effector proteins looks like that can potentially influence SMAD signaling output (e.g. Phosphathases to SMADs known to interact with wt receptors).

The models drawn need to depict more accurately on the nature of type I and type II receptor complexes (heterotetrameric) and high affinity towards the ligand. The current versions are too oversimplified at this stage. The pathway crosstalks and feedbacks need to be more visible, in order for non experts to not draw too simple conclusions from the visual representations presented in this MS. Particularly the work by Hill and co-workers on receptor oligomerization and SMAD shuttling and feedback need to be included.

Overall, the manuscript is very significant to the field.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This is an interesting study that examines the output of the TGF-Beta pathway and how abundance/dosage can determine the signaling response in single cells across multiple cell types. The study is primarily mathematical. The focus is on the Type 1 and 2 TGF-Beta receptors driving nuclear SMAD2 expression. The authors observe that SMAD2 phosphorylation is sensitive to variations in the lower levels of either receptor but robust at variations of high abundance of the receptor reflected through SiRNA experiments shown in Figure 4. Their conclusion is that the feature is consistent with Liebig's law of the minimum- where in this case- a low abundance of the receptor serves as the rate-limiting step in signaling for this pathway.

Major comments:

• While the data as presented are interesting, it is unclear as to whether the abundance regulates biological function. SMAD2 phosphorylation is shown with some nuclear translocation. However, TGF-Beta target gene activation is not shown, and this needs to be completed.
• In addition, it is unclear as to what happens to SMAD3 and SMAD4 which are expressed endogenously in this setting. How are these other TGF-Beta signaling molecules addressed by these observations?
• Specific biological readouts- cell differentiation etc. are not examined and would need to be provided and discussed.
• Therefore, the claims put forward while interesting require additional experiments examining SMAD2 target gene activation and biological readouts.
• Lastly, statistical analyses are not provided and would need to be provided. For instance in Figure 4, how many experiments were replicated and statistical analysis performed for this Figure?

Significance

• Conceptually this is an important study because dosage is a prominent issue in TGF-Beta signaling.
• For instance, in my field of expertise- mouse models of TGF-beta signaling e.g. SMAD2 knockouts- the cancer phenotypes are evident in haploid animals. Yet how and why dosage plays such a large role in tumorigenesis remains unclear.

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Referee #2

Evidence, reproducibility and clarity

Li et al. present an interesting and intuitive concept for the sensitivity and heterogeneity of biological networks: When two or more proteins form a functional complex, it is the limiting component with the lowest concentration that is most sensitive to perturbations and whose fluctuations dictate cell-to-cell variability of complex function. The authors apply this concept to the TGFb pathway and discuss sensitivity of SMAD signaling towards TGFb receptor I and II fluctuations. The paper is clearly written and convincing, but some improvements in the experimental validation would be beneficial as detailed further below.

1. The authors claim that the ratio of TGFb receptor I and II is very different across cell lines (Fig. 1) and use this observation for the validation of their model in Fig. 4. However, the relative expression TGFb receptor levels are purely based on RNAseq data which does not necessarily imply similar behavior at the protein level, especially on the cell surface. To address this issue, the authors should ideally provide absolute Western blot measurements of TGFbRI at the protein level to complement their absolute quantification of TGFbRII (Fig. S2). At the very least they should show that the observed relative expression levels of TGFbRI and II at the protein level (Figure S7) are correlated to differences in RNA levels (Fig. 1) using protein quantification. They should also confirm that similar receptor ratios for these receptors at the RNA level are observed in other published RNAseq datasets of the same cell lines(e.g., ENCODE for HepG2 and published RNAseq studies in HaCaT). Furthermore, they might take into account published mass spec datasets for quantifications of TGFbR protein levels.
2. Figure 4: To better judge the reproducibility of the knockdown titration, it would be good to show the different siRNA concentrations as a color code- Alternatively, TGFBR expression could be plotted as a function of the siRNA concentration in a Supplemental Figure, showing the effects of individual replicates.
3. The simulations in Figs. 5 and 6 show that SMAD signaling fluctuations are mainly determined by cell-to-cell variability of receptor levels when using the SMAD nucleocytoplasmic ratio as a readout, and this is especially true for early time points. For downstream cellular responses, the absolute concentration of phosphorylated SMAD (complexes) in the nucleus is likely more relevant. Based on the authors work and evidence from the literature, I expect that this quantity will likely be heavily be influenced by receptor levels as well, but fluctuations in SMAD expression will play an important role as well. The authors should discuss this issue, and clarify that normalized quantitites like SMAD N2C and pSMAD/SMAD mostly characterize receptor-level fluctuations while filtering SMAD fluctuations.
4. The single-cell measurements in Fig. 7 are interesting, but can only partially be seen as a direct validation of the model predictions, as it seems expected that varying the total input by introducing co-fluctuations in both receptors heavily influence the SMAD level. Wouldn't it be possible to design more specific validation experiments, in which the receptor co-expression construct (Fig. 7C) is used for baseline optoTGFBR expression and combined with an individual expression construct for one of the opto-receptors? This way, the authors could establish different regimes, in which one of the two receptors becomes dominant, and the impact fluctuations could be analyzed in a larger receptor expression space. Of course, a full validation of all possible scenarios is not necessary, but it would, for instance, be valuable to see whether the strong dependency of SMAD signaling of TGFBR2 levels vanishes when TGFBR2 is expressed at a higher level than TGFBR1.

Referees cross-commenting

Comments from R2: I agree with most comments of the other reviewers, and highlight the most important overlaps with my comments below.

I agree with R1 that the model validation in Fig. 7 is incomplete and think that this will be a key point to improve the quality of the manuscript (see also my reviewer comment 4)

In line with R3 and R4, I think that the SMAD N/C simulations do not necessarily imply effects on TGFb target gene expression, cell fate decisions or human pathologies. The significance of the results for cellular behavior should be discussed (see also my comment 3)

Significance

The manuscript presents an interesting and intuitive concept for the sensitivity and heterogeneity of biological networks. The authors apply this concept to the TGFb pathway and discuss sensitivity of SMAD signaling towards TGFb receptor I and II fluctuations.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the current study, Li et al investigated how TGF-beta signaling is controlled by protein abundances. Computational modeling and experiments indicated that the abundance of TGFBR1 and TGFBR2 affects the signaling, and those with lower abundance affect the signaling more, resembling Liebig's law of the minimum. Specifically, they showed that by using multiple cell lines with a different abundance of receptors, modulation of expression of the less abundant receptor impacts the signaling, which is measured by SMAD2 nuclear-to-cytosol ratio and/or relative phospho-SMAD2 level. Also, by using a light-induced interaction system, they showed that the signaling is dependent on the concentration of receptor complex when both receptors are expressed at similar amounts.

Major comments:

Computational predictions support the authors' idea. The computation and the experiments are well-documented. And it would gain substantially if the authors fill the gap between the predictions and the experiments as follows.

In Figure 4, the authors showed that perturbation on receptors with lower expression levels in each cell line changes the phospho-SMAD2 level. Although the data looks consistent with their claim, the result is only qualitative. The authors established a computational model in the former sections, thus it would be of great interest to assess if the experimental results quantitatively match the computational prediction.

In Figure 5, the authors computationally predicted that the expression level of receptors is correlated with SMAD2 N2C levels 1 hour after stimulation, and the strength of negative feedback with SMAD2 N2C levels 8 hours after stimulation. Because the authors employed iRFP-SMAD2 system, the prediction could be verified experimentally, at least the prediction on SMAD2 N2C 1 hour after stimulation could be checked. (In a sense, this is partially verified by the data in Figure 7, where both receptors are expressed at similar levels). It would gain substantially if the authors could verify the computational prediction in Figure 6.

Since the authors stated in the introduction that "The same TGF-β ligand can initiate different signaling responses depending on the cellular context, but the underlying control principle remains unclear...Together, these results revealed an effect of the minimum control in the TGF-β pathway, which may be an important principle of control in signaling pathways with context-dependent outputs.", experimental verification of the prediction done in Figures 4-6 will be very important. Or the authors should stress that these points are only predicted by computational models.

As written in the below "Significance" section, the result is, in a sense, obvious. It should be stated that because the study utilized a slightly high concentration of TGF-beta in the experiments, it might be natural that the low-abundance receptor becomes a bottleneck of the signaling. It would gain to assess how receptor abundance affects signaling with the stimulation of lower concentrations of TGF-beta, or to examine the computational model if the low abundance of a receptor becomes a bottleneck of signaling because of saturation. Also, it is highly recommended to discuss the physiological implication of the current study, taking into account the experimental conditions used.

Significance

TGF-beta signaling is one of the most rigorously studied pathways both computationally and experimentally. As written in the introduction of the manuscript, it is still unknown how the variability of responses arises not only between cell types but also differences among cells of single cell type. Studies showed that protein abundance accounts at least partly for a source of cell variability in TGF-beta signaling.

While former studies examined the variability in SMAD protein abundance, the uniqueness of this study is that it focused on the abundance of TGF-beta receptors.

Given that both TGFBR1 and TGFBR2 are involved in the signaling, however, it's not difficult to imagine that a less abundant receptor affects the signaling more than the other, and serves as a bottleneck for the signaling. Specifically, because a slightly high concentration (100pM = 4.4 ng/mL of TGF-beta; other studies used much lower conc., e.g. 0, 0.03, 0.04, 0.07, and 2.4 ng/mL in Frick et al, PNAS, 2017, and 0, 1, 2.5, 5, 25, and 100 pM in Strasen et al, Mol Syst Biol, 2017) is used throughout the experiments to check cell-cell variability and the effect of receptor abundance in the current study, the formation of the receptor-ligand complex may be quite fast and be saturated at the level where the receptor with lower abundance is exhausted. In the reviewer's humble opinion, the authors' statement that this is Liebig's law of the minimum sounds a bit exaggerated.

Nevertheless, the study is of some value because it utilized both computational and experimental analysis to show it is indeed the case. Of note, the current study showed that the variability in the different proteins leads to the variability in different time points, namely, the variability in the receptor abundance leads to the variability 1 hour after stimulation, while that in negative feedback strength leads to the variability 8 hours after stimulation. If the authors fill a small gap between their computational analysis and experimental verification, the study will be of interest to the specialist in the field.

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Reply to the reviewers

Reviewer #1

We thank this Reviewer for the time spent assessing our manuscript, and for suggesting approaches to strengthen the robustness of the differences (e.g., TL vs FL) reported in our results. We have carefully addressed each point raised by this and other reviewers, providing new analyses and data - see list below. Indeed, these analyses combined helped us to make our main results reproducible, corroborating the main findings and refining the message of the manuscript.

New analyses/data added:

1. *Effect of batch due to different lanes - comparison of DEGs (TL/FL) obtained when samples in different lanes are tested individually (new Figure S15). *
2. Effect of batch correction on our results - comparison of the DEGs (TL/FL) obtained with and without batch removal (new Figure S15).
3. Sensitivity of our enrichment results for GWAS significance – we performed the enrichment of GWAS genes using different GWAS thresholds, 10-6, 10-7, 5x10-8 (new Figure S14).
4. Expression analysis of GRIN2A and SLC12A5 in Allen Brain Atlas data and qPCR results of GRIN2A and SLC12A5 in patients with frontal and temporal lobe traumatic injury (new Figure S12, Table S3).
5. Comparison of the DEGs (TL/FL) with DEGs (autism/Ctrl) obtained from single cell RNA seq (new Figure S16, Table S7).
6. Comparison of the results using the GWAS genes derived from Trubetskoy et al. with our gene lists (new Figure S17).

7. Description of the data quality (Figure S2) Major points:

8. The main limitation of the work is the small starting sample size. The authors studied 1 frontal lobe sample and 2 temporal lobe samples. Although this information was in Table S3 it would be good to include upfront in the Methods. snRNA-seq was generated on the 10x platform. It would be helpful to know if the 10x step and sequencing was performed as one batch, or as individual batches. Similarly, were the sample libraries all sequenced on the same lane, or different lanes. The authors do not state in the Methods how many nuclei they were targeting and this should be included. Sample pre-processing was well described and standard. We now provide additional details about the sequencing step (nuclei, sample pre-processing, etc.) in the revised manuscript (see Methods, and text below). The potential batch effect of the lane is discussed and addressed in the next point.

‘10X Genomics uses a microfluidic system for cell sorting. Cells and enzymes, combined with Gel Beads, enter the oil phase to form GEMs. The resulting sample libraries were sequenced on separate lanes. To enhance sequencing depth, the primary target number of nuclei for the two samples from TL is set at 10,000, considering an RNA integrity number (RIN) of 6.5. In contrast, for the sample from FL, the target is set at 20,000 nuclei due to a higher RIN of 8.1.’

In relation to Batch correction - as with any batch correction method, it is unclear whether the correction is adjusting for biological differences or technical. Since this is a study of the differences between FL and TL, would it not be more appropriate not to correct for batch, particularly as the samples were analysed individually - particularly if batch effects were carefully controlled for in the initial study design. The authors should test whether the results are robust to batch correction or not.

Since the samples are sequenced by different lanes of 10X platform we can’t exclude potential batch effects. To address this, we corrected the batch by CCA (canonical correlation analysis) which enhanced the clustering and the UMAP visualization, which is now less affected by batch-specific variations.

Moreover, in an attempt to account for the sample size limitation, we employed 3 approaches to confirm the main transcriptional differences between the 2 regions, and that these are “robust” to batch correction, as is shown in new Figure S15: (1) Comparison of the gene expression differences (2 TL vs 1FL) with and without removing batches (new Figure S15. a, c); (2) The results obtained by comparing the differences between each individual TL sample (processed in different lanes) and FL sample are contrasted with the results after batch removal (new__ Figure S15. b, d__); (3) To confirm a limited effect of lane, we provide analysis of the expression similarity of three samples which demonstrates, consistently for each major cell type and neuronal sub-types, a strong correlation between the two TL samples (form different lanes) as compared with FL (new Figure S15. e).

As shown in panel a, c, below, the majority of DEGs (2TL vs FL) identified with batch effects largely overlap with the DEGs (2TL vs FL) without considering batch effects for both major cell types and neuronal sub-types. In panel b, d, we show that the majority of DEGs with batch correction (2TL vs FL) overlap with the individual DEGs found in each TL vs FL comparison. In panel e, we show that the transcriptomic profiles of 2 TL exhibit higher similarity compared with the sample from FL. Overall, based on these analyses we concluded that our results are robust to batch correction.

In addition, we highlight that, differently from other tissues, it is very difficult to obtain the “fresh” human samples of brain cortex, which most likely provides different transcriptome information than the more commonly used post-mortem brain samples. These analyses offered another evidence supporting the differences between TL and FL, which complement (and align with) the comparative analyses using the data from Allen Brain Atlas (see Figure S9, original results).

Figure S15. Comparison of biological (gene expression) differences in each major cell type and neuron-subtype between the 2 regions with and without batch effect removal. ____a, c. Comparison of the DEGs (2 TL vs 1FL) with and without removing batches (a, up-regulated in TL; c, up-regulated in FL). b, d. Comparison of the DEGs (2TL vs FL) following the removal of batch effects with the DEGs calculated by individual TL vs FL samples. __e. __Expression correlation between each sample (without batch correction for lane), showing higher transcriptional similarity within the same tissue type than across tissues, consistently in major cell-types and neuronal subtypes.

3.Differential gene expression analyses between the FL and TL was undertaken using edgeR. It is unclear if this was performed on aggregated counts or not - i.e., sum of counts per gene per cell type. If it was, then with such a small sample size (1 frontal lobe and 2 temporal lobe samples), it is unclear how well edgeR will perform. Similarly, if the DE analysis was performed using individual gene per cell counts, then there is a type 2 error risk due to pseudoreplication. It is reassuring that the primary results were replicated in a second dataset. Moreover, the downstream analyses (functional enrichment analysis, heritability enrichment analysis etc) are designed to cope with noisy data so I'm happy with the broad conclusions.

We acknowledge the reviewer’s point, and here we specify that edgeR performs differential expression analysis at the level of individual genes across individual cells, and we performed DE analysis for each cell type. We and others consider edgeR a robust tool for analyzing RNA-Seq data; edgeR has been extensively benchmarked alongside other widely used statistical methods, e.g., edgeR-LRT and edgeR-QLF which showed high performance1. Another study about different tools for differential expression in single cell data demonstrated that edgeR (and others) has usually higher precision, larger than 0.9, yielding lower false positive2. Therefore, based on previous formal assessments showing the robustness of edgeR, we select this approach for DE analysis.

Moreover, it has been previously documented that edgeR can be used also to analyses small samples due to several inherent features. First, edgeR uses an empirical Bayes framework to estimate dispersion, which is a measure of the biological variability in gene expression. This approach uses information across genes, helping to stabilize the variance estimates even when sample sizes are small. This makes edgeR more robust in cases with a limited number of replicates. Second, edgeR accounts for overdispersion, which can effectively handle small sample sizes and provide more accurate statistical tests. In the revised manuscript, we now discuss the advantages of edgeR in Methods, in particular for edgeR performance on small sample size in single cell RNA seq.

It is unclear if this was performed on aggregated counts or not - i.e., sum of counts per gene per cell type

We specify that edgeR performs differential expression analysis at the level of individual genes across individual cells, and we performed DE analysis for each cell type. This is now indicated in Methods.

*4.To calculate the enrichment of "genetic risk" associated with psychiatric disorders, the authors used a hypergeometric test for the overlap between cell type specific genes and the GWAS variant-mapped genes for each disease, which is widely used to evaluate the enrichment of genetic risk genes. To identified GWAS variant mapped genes the authors used a GWAS SNP threshold of To test the sensitivity of the enrichment analysis, we selected the GWAS genes with each threshold respectively: 10-6, 10-7, 5x10-8. The new results are largely consistent with those obtained using a P-value of 10-5. Susceptibility genes for neuropsychiatric disorders are enriched for expression in neuronal cell types for each P-value. With respect to neuronal subtypes, we found stronger enrichment in INH than in EX sub-clusters, with INH PVALB, SST and EX L5 being the neuronal sub-clusters mostly enriched for expression of GWAS genes (new __Figure S14).

Figure S14 Cell type for expression of neuropsychiatric disorder associated GWAS genes with each threshold respectively: 10-6, 10-7, 5x10-8. a-c. adjusted P-value of enrichment in each 7 major cell type. d-f. adjusted P-value of enrichment in each neuron subtype.

Moreover, the Reviewer suggests using an alternative tool, FUMA, which requires the whole set of SNP GWAS associations. While these can be available for single diseases and GWAS data (assuming the authors made all data available, and assuming one obtains approval by the consortia managing the GWAS data), unfortunately these SNPs data are not available for several diseases in the NHGRI-EBI GWAS catalog, which provides only SNPs with a max P=10-5. Since in our study we wanted to consider GWAS data from 7 neuropsychiatric diseases, we pragmatically opted for obtaining data from NHGRI-EBI GWAS catalog rather than seeking GWAS SNP data from individual studies.

We also acknowledge the limitations for the variant to gene mapping (revised Discussion, page 17, line 17), and we also highlight that several other studies rely on the variant to gene mapping from NHGRI-EBI GWAS catalog for enrichment analyses3-5. There are also studies that investigate the enrichment of mapped genes (from NHGRI-EBI GWAS catalog) in different cell types using the hypergeometric test 6-7, as we do in our study. Therefore, the methods used in our manuscript are consistent with approaches adopted in previously published studies. Perhaps more importantly, in the revised manuscript, we replicated the main GWAS enticement results (e.g., in INH neurons and in PVLAB from the temporal lobe) in the Brain Allen Atlas datasets, which shows that, despite these limitations of variant to gene mapping, our main enrichment results are replicable. We discussed these limitations in our paper (see Discussion, page 17, line 6).

However, where individual genes are mentioned then the authors may wish to confirm the results from edgeR for a few selected genes with a second technique such as qPCR. For example, GRIN2A and SLC12A5.

To address this point, first, we check the expression of the 2 genes using the data from Allen Brain Atlas data, which show significantly high expression in TL (new Figure S12. b, and below). In addition, we carried out new qPCR analysis, and found the mRNA expression levels of GRIN2A and SLC2A5 in patients with traumatic brain injury in the temporal lobe region were higher than those in patients with frontal lobe injury (new Figure S12. c).

Figure S12. b. Expression level of GRIN2A and SLC12A5 in 2 regions using Brain Allen Atlas. ***P-value-ΔΔCt method. Significance was determined through T-test (two-tailed). qPCR for each TL or FL sample was repeated 3 times.

Reviewer #2

We thank this Reviewer for the time spent evaluating our manuscript. In the revised manuscript we have now included several new analyses and data that allowed us to replicate and strengthen our main findings, and especially we considered the psychoactive drug target genes using the whole psychoactive drugs DB. We believe these new data helped us to refine the message and overall improve reproducibility of the main findings presented. We have carefully addressed each point raised by this and other reviewers, by providing revisions and explanations, and adding new data to our manuscript, as follows:

New analyses/data added:

1. *Effect of batch due to different lanes - comparison of DEGs (TL/FL) obtained when samples in different lanes are tested individually (new Figure S15). *
2. Effect of batch correction on our results - comparison of the DEGs (TL/FL) obtained with and without batch removal (new Figure S15).
3. Sensitivity of our enrichment results for GWAS significance – we performed the enrichment of GWAS genes using different GWAS thresholds, 10-6, 10-7, 5x10-8 (new Figure S14).
4. Expression analysis of GRIN2A and SLC12A5 in Allen Brain Atlas data and qPCR results of GRIN2A and SLC12A5 in patients with frontal and temporal lobe traumatic injury (new Figure S12, Table S3).
5. Comparison of the DEGs (TL/FL) with DEGs (autism/Ctrl) obtained from single cell RNA seq (new Figure S16, Table S7).
6. Comparison of the results using the GWAS genes derived from Trubetskoy et al. with our gene lists (new Figure S17).
7. Description of the data quality (Figure S2) 1.The manuscript is unfortunately lacking (supplemental) figures showing the preprocessing, batch effect correction, and cell type annotation of single nucleus RNAseq data. Although this part is described in the methods in detail, it is hard to judge if these parts were done properly if data is not shown in any of the figures. Regarding the batch effect correction, it reads as if the batch effects have been removed for both brain regions separately. This potentially introduces a bias between brain regions that hugely questions the later performed analysis of differential expression analysis in FL vs TL. In any case, this analysis is not convincing since it has been performed on n=3 vs. n=3 samples and is thus tremendously underpowered.

We thank the reviewer for the suggestions. First, we added the cell type annotation process for the major cell type by showing the expression of known markers in Figure S2. f. To show the validity of our cell classification, we calculated the significance of overlap with major cell type markers derived from known study in Figure S2. e. __We also provide the distribution of nUMI, nGenes, percentage of mitochondrial genes after quality control in Figure S2. b __to show the large number of cells contributing to the overall quality and depth of the scRNA-seq dataset despite the small number of individual samples.

Figure S2. Description of snRNA-seq data. b. Distribution of nUMI, nGenes, percentage of mitochondrial genes after QC. e. Significance of overlap with major cell type markers derived from known study. f. Expression of known markers for each cell type.

Since the samples are sequenced by different lanes of 10X platform, therefore, we can’t exclude potential batch effects. To account for this potential batch effect, we corrected the batch by doing CCA (canonical correlation analysis) which enhanced the clustering and the UMAP visualization more biologically meaningful and less driven by batch-specific variations.

Moreover, in an attempt to account for the sample size limitation, we employed 3 approaches to confirm the main transcriptional differences between the 2 regions, and that these are “robust” to batch correction, as is shown in new Figure S15 (see next page): (1) Comparison of the gene expression differences (2 TL vs 1FL) with and without removing batches (new Figure S15. a, c); (2) The results obtained by comparing the differences between each individual TL sample (processed in different lanes) and FL sample are contrasted with the results after batch removal (new Figure S15. b, d); (3) To confirm a limited effect of lane, analysis of the expression similarity of three samples demonstrates, consistently for each major cell type and neuronal sub-types, a strong correlation between the two TL samples (form different lanes) as compared with FL (new__ Figure S15. e__).

As shown in panel a, c, below, the majority of DEGs (2TL vs FL) identified with batch effects largely overlap with the DEGs (2TL vs FL) without considering batch effects for both major cell types and neuronal sub-types. In panel b, d, we show that the majority of DEGs with batch correction (2TL vs FL) overlap with the individual DEGs found in each TL vs FL comparison. In panel e, we identified that the transcriptomic of 2 TL exhibit higher similarity compared with the sample from FL.

Overall, based on these analyses we concluded that the results are robust to batch correction.

Figure S15. Comparison of biological (gene expression) differences in each major cell type and neuron-subtype between the 2 regions with and without batch effect removal. a, c. Comparison of the DEGs (2 TL vs 1FL) with and without removing batches (a, up-regulated in TL; c, up-regulated in FL). b, d. Comparison of the DEGs (2TL vs FL) following the removal of batch effects with the DEGs calculated by individual TL vs FL samples. __e. __Expression correlation between each sample (without batch correction for lane), showing higher transcriptional similarity within the same tissue type than across tissues, consistently in major cell-types and neuronal subtypes.

In addition, we highlight that, differently from other tissues, it is very difficult to obtain the “fresh” human samples of brain cortex, which most likely provides different transcriptome information than the more commonly used post-mortem brain samples. These analyses offered another evidence supporting the differences between TL and FL, which complement (and align with) the comparative analyses using the data from Allen Brain Atlas (Figure S9, original results).

2.Furthermore, the way that the authors treat GWAS data for disease does not seem to follow best practices. For schizophrenia, last year the largest GWAS so far was published (Trubetskoy et al, Nature, 2022) with very careful prioritization of genes. The authors should re-analyze their data using the gene list from this paper (and similar from other disorders) rather than the gene list that they came up with using their approach. The approach to select genes from different GWAS introduced seems highly arbitrary and leaves the reader unsure about statistical rigor.

We have carefully considered the suggestion regarding the treatment of GWAS data, particularly with respect to the gene list derived from the recent schizophrenia GWAS by Trubetskoy et al. (Nature, 2022). In this paper, the author mainly identified 120 genes (106 protein-coding) that are likely to underpin associations with schizophrenia which implicate fundamental processes related to neuronal function including synaptic organization, differentiation and transmission.

With respect to our study, first, we found there is significant overlap between prioritized genes in Trubetskoy et al’ study and GWAS genes included in our study. We showed the P value for overlap significance below, and listed the 27 genes. Among the prioritized genes, GRIN2A is also identified to be important in neuropsychiatric disorder, which is also confirmed to differ between the 2 regions and dysregulated in disease brain.

Enrichment of genes obtained from the prioritized schizophrenia-associated genes in Trubetskoy et al. Significant overlap (P=0.013, hypergeometric test) between schizophrenia-associated genes (120 prioritized genes from Trubetskoy et al.) and our GWAS genes (from GWAS catalogue).

Second, we conducted a supplementary analysis focused on the 120 genes prioritized by Trubetskoy et al, as shown below. We found the 120 prioritized genes in this paper are significantly enriched in excitatory and inhibitory neurons (panel b, below), aligning with our main findings conducted by schizophrenia related genes in our previous GWAS gene lists. Within the neuronal subcluster, we found a significant enrichment in L4, LAMP5 and PVALB cells (panel c); L4 and PVALB are largely consistent with our previous results (shown in Figure 3. c). Furthermore, we also found the 120 schizophrenia-associated genes are highly significantly enriched in DEGs (TL/FL) in VIP and PVALB subtypes (panel d).

b-c. Enrichment of 120 prioritized schizophrenia-associated genes in major cell types and neuronal subtypes. d. For each cell type, the enrichment of 120 genes is calculated with respect to the set of DEGs (TL/FL). Approach used for enrichment analysis is hypergeometric test (significance level, P-valueThese results suggest that while new gene lists from larger GWAS studies (e.g., Trubetskoy et al) come up regularly, the lists of GWAS genes prioritized in our enrichment analysis has some overlap with the newest GWAS. We agree that including more (larger) GWAS studies will strengthen the manuscript, but based on the analyses above, we believe our GWAS enrichment results are robust. In the revised manuscript, the new analysis including the detailed comparison with schizophrenia GWAS by Trubetskoy et al. (Nature, 2022) are reported in new Figure S17.

To improve on the GWAS enrichment analysis, we carried out additional sensitivity analyses to support our GWAS enticement results. We selected additional thresholds to evaluate the robustness of our results to the choice of gene lists to test the sensitivity of the enrichment analysis, we selected the thresholds: 10-6, 10-7, 5x10-8. The new results are largely consistent with those obtained using P-value of 10-5. Susceptibility genes for neuropsychiatric disorders are enriched for expression in neuronal cell types for each P-value. With respect to neuronal subtypes, we found stronger enrichment in INH than in EX sub-clusters, with INH PVALB, SST and EX L5 being the neuronal sub-clusters mostly enriched for expression of GWAS genes. These results are reported in new Figure S14.

Figure S14. Enrichment of cell type expression of neuropsychiatric disorder-associated GWAS genes for different GWAS-thresholds. a-c. Adjusted P-value of enrichment in each 7 major cell type. d-f. Adjusted P-value of enrichment in each neuron subtype.

3.Similarly, the choice of data set for disease-related differentially expressed genes is unclear as much larger (two orders of magnitude) published data sets exist for many of the disorders. For three of those DEG analyses performed on bulk RNAseq data, for the remaining two the DEG list of papers is used directly -making a comparison complicated. One would have to run DEG analysis in a standardized way for all 5 datasets/ disorders. It would be good to also indicate the respective sample size in Fig. 5a. (On a different note, the OCD publication is Piantadosi et al. 2021, not Sean C.et.al..) In addition, the authors matched brain regions to their regions of interest (frontal and temporal lobe) as shown in Fig. 5a. Still, they vary across disorders, which makes it hard to compare their findings across disorders and does not allow for a general statement about frontal vs. temporal lobe. ____To generalize for any of those psychiatric disorders I would recommend including more RNA-seq studies of the same disorder. Nowadays there are getting more and more case-control single nuclei studies on such disorders published. The authors could also include those by transforming them to pseudo bulk datasets and running their DEG analysis with edgeR as documented.

We acknowledge there might be a bias introduced by using the DEGs from the original paper directly. In addition, there is a general limitation affecting all bulk-RNA studies in complex tissues with different anatomical structures (e.g., kidney, brain, etc.), which form a great part of the publicly available data sources. In brain research, it is also more difficult to collect fresh human brain samples from patients with psychiatric disorders, which poses additional tissue availability constraints. Despite these limitations, we argue that bulk-RNA studies in anatomically complex tissues, and the DEGs reported therein, can be useful for GWAS enrichment analysis and not all DEGs are due to spurious or artificial signals. Furthermore, due to the lower sequencing depth inherent in single-cell RNA sequencing compared to bulk RNA sequencing, we set up to contrast our findings with results found by bulk-RNA seq.

We agree with the Reviewer that “One would have to run DEG analysis in a standardized way for all 5 datasets/ disorders”, however this approach assumes that the raw data are directly available and/or that the authors are keen to share the raw data. Both these assumptions are – unfortunately – not valid in many cases. (In several instances, we did contact authors to have access to raw data, with no success). Furthermore, when a commonly shared gene set in the DE genes is identified when using “heterogenous DE gene lists”, this might suggest a strongest convergence, or a convergence that is “robust” despite the differences between the heterogeneous DE lists (from authors or newly generated by us). Therefore, despite the limitations, our approach was motivated by practical considerations.

In addition, the brain region differences can be more prevalent and have a larger impact for specific psychiatric disorders. In our manuscript, for MDD we specially looked at only the BA8/9 which come from dorsolateral prefrontal cortex. Regarding OCD, BP, and MDD, several studies showed that there are no significant functional differences clinically observed between the orbitofrontal cortex and dorsolateral prefrontal cortex (Schoenbaum G, Setlow B. Integrating orbitofrontal cortex into prefrontal theory: common processing themes across species and subdivisions. Learning & Memory, 20018. Golkar A, Lonsdorf T B, Olsson A, et al. Distinct contributions of the dorsolateral prefrontal and orbitofrontal cortex during emotion regulation. PloS one, 20129). In the case of ASD, Brodmann area 41, 42, 22 refers to a subdivision of the cytoarchitecturally defined temporal region of cerebral cortex, exhibiting similar functionality to the temporal gyrus. Therefore, ASD and SCHI may arise from specific regions within the temporal lobe, while OCD, MDD, and BP may be associated with regions within the frontal lobe.

To address the Reviewer’s point more directly - we carried out additional analyses to investigate the effect of this factor on our main results. One of our aims was to understand how regional gene expression differences (TL/FL) in PVALB neurons are associated with gene dysregulation in the brain of neuropsychiatric disease patients. We have now extended these analyses to a separate dataset, and tested whether the dysregulated genes in neuropsychiatric disease are expressed mainly in TL and FL using single cell data from Brain Allen Atlas (4 patients, each with 6 brain regions profiled). The new results are shown in new Figure S11 b-f (and reported in the next page).

Briefly, we found that the percentage of dysregulated genes in SCHI, BP, OCD, and MDD that are expressed in MTG (SCHI: 75%, BP: 81%, OCD: 68%, MDD: 71%) and CgG (SCHI: 77%, BP: 80%, OCD: 60%, MDD: 77%) is higher compared with those in all other regions included in Brain Allen Atlas dataset. The percentage of ASD dysregulated genes expressed in the 6 regions from Brain Allen Atlas are quite similar. This analysis suggests that, despite the potential impact of heterogeneity of regions, the DEGs in psychiatric conditions are typically expressed at higher level in MTG (TL) and CgG (FL) compared with other regions, therefore highlighting the potential role of these two regions in psychiatric conditions. Therefore, we believe that despite the heterogeneity of regions included in the published RNA-seq studies, the strongest signal of enrichment for DEGs is detected consistently in TL and FL, i.e., in the 2 brain regions where the DEGs are also most highly expressed compared with other regions. These new data, reported in a new Figure S11 of the revised manuscript, provide additional evidence to support our main conclusions.

Due to the difficulties obtaining the human sample of psychiatric disorders causing limited public data resource, we found one study about molecular changes of ASD revealed by single cell RNA seq coming from Velmeshev et al. Science. 2019; 364(6441):685-689 (PMID: 31097668), including 22 ASD samples and 19 control samples. We compared the DEGs (TL/FL) with the DEGs (ASD/Ctrl), and report the results in new Figure S16. Briefly, the results show that except LAMP5, Endo, and L4, ASD-associated dysregulated genes significantly overlap with DEGs between FL and TL in several cell types, especially in VIP and astrocytes. While PVALB is not the most apparent cluster reflecting regional differences contributing to ASD, we found a moderate association (R2 =0.11, P=0.04) between changes in TL/FL and those in ASD/Ctrl brain. These findings suggest that gene expression differences between the 2 regions may contribute to ASD disorder, providing additional evidence to support our main conclusions.

Figure S16. Overlap of genes dysregulated in ASD and genes differentially expressed between TL and FL in each major cell type and neural subtype. Venn diagram plots in a-m showing the number of overlapped genes. Dot plot in each panel shows the relationship between the log2FC(TL/FL) [our study] and log2FC(ASD/Ctrl) [Velmeshev et al. Science. 2019 study]. Significance of the overlap: *0.001-0.01, **0.0001-0.001, ***0.00001-0.0001, ****4.For cell type enrichment of disease signal based on GWAS signal several carefully controlled studies exist using more sophisticated statistical methods (Skene et al., Nature Genetics, 2018, Bryois et al., et al. Nature Genetics 2020, MJ Zhang et al Nature Genetics 2022 to mention a few). I applaud that the authors aim to go beyond this basic characterization but I think it is worrisome that by using less sophisticated (and importantly less controlled) statistical and genetic approaches they reach a different signal -and then they go on and analyze this signal. It is potentially interesting they reach a different conclusion, but they need to provide a careful statistical analysis to explain how the chosen method is superior or at least different to previous efforts.

The Reviewer suggests the use of alternative approaches to link GWAS variants to genes, like MAGMA, LDSC, FUMA to improve the gene mapping from GWAS signals, and are better than the gene mapping based on proximity alone. While these approaches can provide some advantages, most of these methods do require the whole set of SNP GWAS associations, including non-significant associations. While these can be available for single diseases and specific GWAS data (assuming the authors made all data available, and assuming one obtains approval by the consortia managing the GWAS data) these SNPs are not available for several diseases in the NHGRI-EBI GWAS catalog, which provides only SNPs with a max P=10-5. Since in our study we considered GWAS data from 7 neuropsychiatric diseases, we (pragmatically) opted for obtaining data from NHGRI-EBI GWAS catalog rather than seeking GWAS SNP data from individual studies.

We now acknowledge the limitations for the variant to gene mapping (revised Discussion, page 17, line 17), and we also report that several other studies rely on the variant to gene mapping from NHGRI-EBI GWAS catalog for enrichment analyses4-6. There are also studies that investigate the enrichment of mapped genes (from NHGRI-EBI GWAS catalog) in different cell types using the hypergeometric test 7-8, as we do in our study. Perhaps more importantly, in the revised manuscript, we replicated the main GWAS enticement results (e.g., in INH neurons and in PVLAB from the temporal lobe) in the Brain Allen Atlas datasets, which shows that, despite these limitations of variant to gene mapping, our main enrichment results are replicable.

(Other comments)

- only n=3, ~45 000 cells making it hard to generalize

- no supplementary figures for the methods (i.e. preprocessing, cell type annotations), thus hard to judge if done properly if they do not show any data - much higher level of transparency needed

- The methods part is not clear, in general, it is only descriptive, with no equations

- Unconvincing determination of DEGs for each disorder

- DEGs and pathways based on n1=1 vs n2=2 feals handwavy

- DEG analysis and cell type annotation are mixed up and it is unclear how DEGs were determined

While we acknowledge the limitation of sample size in our study, we also emphasize again the challenges in of availability of fresh human sample, which provide more transcriptomic information than postern sample. Despite the small number of individual samples, the large number of cells (~45,000) contributes to the overall quality and depth of the scRNA-seq dataset. Hence, our study provides a foundational perspective on the gene expression between the frontal lobe (FL) and temporal lobe (TL), and valuable data source for further investigations.

With respect to the additional description of the data processing and cell annotation process, in the revised manuscript we now elucidate the cell type annotation process by showing the expression of some known markers in new Figure S2. f, the significance of overlap with major cell type markers derived from known study in new Figure S2. e, the distribution of nUMI, nGenes, percentage of mitochondrial genes after quality control in new __Figure S2. b. __

To strengthen the differential gene expression analysis, we replicated our main findings through SMART RNA-seq from Brain Allen Atlas including the DEGs identified in our study (Figure S9).

More technical details are provided in the revised manuscript, as detailed below:

In the revised Methods section – (1) Differential expression analysis in FL vs TL and pathway enrichment analysis, we added more details about how the DEGs are identified and how this is robust to batch correction. (2) Replication analyses in human Brain Allen Atlas, we provide more details about how we replicated the DEGs using Allen Brain Atlas dataset. (3) Enrichment of neuropsychiatric disease GWAS genes in brain cell clusters, we now added more methodological details about the enrichment analysis.

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Reviewer #3

We thank the Reviewer for his/her overall positive comments. In the revised manuscript we have now included several new analyses requested by this and other reviewers (see list below), which allowed us to replicate and strengthen our main findings. We also add details of the method used in this paper. We believe these new analyses and data helped us to improve reproducibility and strengthen the main findings presented in our manuscript.

New analyses/data added:

1. *Effect of batch due to different lanes - comparison of DEGs (TL/FL) obtained when samples in different lanes are tested individually (new Figure S15). *
2. Effect of batch correction on our results - comparison of the DEGs (TL/FL) obtained with and without batch removal (new Figure S15).
3. Sensitivity of our enrichment results for GWAS significance – we performed the enrichment of GWAS genes using different GWAS thresholds, 10-6, 10-7, 5x10-8 (new Figure S14).
4. Expression analysis of GRIN2A and SLC12A5 in Allen Brain Atlas data and qPCR results of GRIN2A and SLC12A5 in patients with frontal and temporal lobe traumatic injury (new Figure S12, Table S3).
5. Comparison of the DEGs (TL/FL) with DEGs (autism/Ctrl) obtained from single cell RNA seq (new Figure S16, Table S7).
6. Comparison of the results using the GWAS genes derived from Trubetskoy et al. with our gene lists (new Figure S17).
7. Description of the data quality (Figure S2) 1.The authors integrated the brain snRNA-seq data with GWAS data to annotate the cell type specific expression, which is one of the key points for this analysis, however a more detailed description of the method is lacking.

We have made changes to the text to improve and clarify this aspect. In the revised Methods section, we now specify: “To calculate the enrichment of genetic risk associated with psychiatric disorders, we used a hypergeometric test for the overlap between cell type specific genes (DEGs between one cell with other cell types, log2FC>0.5, adjusted.P __2.The authors found a set of genes which is associated with psychiatric disorders and specific cell types, for example inhibitory neurons are the most vulnerable cell type to genetic susceptibility through their analysis. The correlation of each cell type and each psychiatric disorders can be discussed.*__

We thank the Reviewer for this suggestion; we have now added more details discussing the relationship between other cell types with psychiatric disorders other than PVALB-neuron in this part – see Discussion in the revised manuscript, where we added: “Astrocyte, OPC are also associated with psychiatric disorders, and play essential roles in maintaining brain homeostasis, regulating synaptic transmission, and supporting neuronal function. Astrocytes also contribute to maintaining the integrity of the blood-brain barrier (BBB) and interact closely with neurons. Disruptions in this communication impact neural circuitry, which is relevant to many psychiatric disorders. OPCs generate oligodendrocytes, producing myelin crucial for signal conduction and brain structural integrity, which potentially impacts brain connectivity and communication between brain regions. Among neuronal subtypes, our data suggest that disruption of specific biological process in PVALB, SST and L5 neurons may contribute to neuropsychiatric disorders. PVALB cells are believed to activate pyramidal neurons only if the signal from excitatory neurons is sufficient and optimize the signaling in both EX and INH72. SST neurons gate excitatory input onto pyramidal neurons within cortical microcircuits, mainly coming from L5 layer of excitatory neuron which is involve in motor control, decision-making, and information transfer between the cortex and subcortical structures73. These signaling processes, when dysregulated, have been implicated in psychiatric diseases74. The relationship between psychiatric disorders and other layers of the cerebral cortex is still under investigation. *L2-3 neurons handle local processing, relevant to conditions like schizophrenia and autism. L6 neurons in thalamocortical circuits are crucial for sensory processing and information relay, involving sensory perception abnormalities.” *

3.The authors have found a group of interesting genes, such as GRIN2A, DGKI, and SHISA9 and confirmed them with the Allen Brain Atlases. Experimental validation would be helpful to confirm such findings.

In our manuscript, we emphasized that GRIN2A and SLC12A5 (both implicated in schizophrenia and bipolar disorder) were significantly upregulated in TL PVALB neurons and in psychiatric disease patients’ brain. To address this point, first, we check the expression of the 2 genes using the data from Allen Brain Atlas data, which showed significantly high expression in TL (new Figure S12. b). By means of new qPCR analysis in primary TL/FL samples, we found the mRNA expression levels of GRIN2A and SLC2A5 in patients with traumatic brain injury in the temporal lobe region were higher than those in patients with frontal lobe injury (new Figure S12. c).

Figure S12. b. Expression level of GRIN2A and SLC12A5 in 2 regions using Brain Allen Atlas. ***P-value-ΔΔCt method. Significance was determined through T-test (two-tailed). qPCR for each TL or FL sample was repeated 3 times.

Lastly, we want to highlight that since we believe in “Data Democratization” and sharing our data resources, upon publication, we will make all our data (including the single cell in “fresh” (surgically resected) brain tissue samples) and corresponding detailed results available to the scientific community.

We believe our study (which is focused on psychiatric diseases) will prompt other groups to use our single cell data and to dig deep into the role of temporal and frontal lobes in other neurogenerative diseases.

__ __

References

1. Squair, J.W., Gautier, M., Kathe, C. et al. Confronting false discoveries in single-cell differential expression. Nat Commun 12, 5692 (2021).
2. Wang, T., Li, B., Nelson, C.E. et al. Comparative analysis of differential gene expression analysis tools for single-cell RNA sequencing data. BMC Bioinformatics 20, 40 (2019).
3. Bhattacherjee A, Djekidel MN, Chen R, Chen W, Tuesta LM, Zhang Y. Cell type-specific transcriptional programs in mouse prefrontal cortex during adolescence and addiction. Nat Commun. 2019 Sep 13;10(1):4169.
4. Grubman A, Chew G, Ouyang JF, Sun G, Choo XY, McLean C, Simmons RK, Buckberry S, Vargas-Landin DB, Poppe D, Pflueger J, Lister R, Rackham OJL, Petretto E, Polo JM. A single-cell atlas of entorhinal cortex from individuals with Alzheimer's disease reveals cell-type-specific gene expression regulation. Nat Neurosci. 2019 Dec;22(12):2087-2097
5. Przytycki, P.F., Pollard, K.S. CellWalker integrates single-cell and bulk data to resolve regulatory elements across cell types in complex tissues. Genome Biol 22, 61 (2021).
6. Swindell, William R., et al. "RNA-Seq analysis of IL-1B and IL-36 responses in epidermal keratinocytes identifies a shared MyD88-dependent gene signature." Frontiers in immunology 9 (2018): 80.
7. Geirsdottir, Laufey, Eyal David, Hadas Keren-Shaul, Assaf Weiner, Stefan Cornelius Bohlen, Jana Neuber, Adam Balic et al. "Cross-species single-cell analysis reveals divergence of the primate microglia program." Cell 179, no. 7 (2019): 1609-1622.
8. Schoenbaum G, Setlow B. Integrating orbitofrontal cortex into prefrontal theory: common processing themes across species and subdivisions[J]. Learning & Memory, 2001, 8(3): 134-147.
9. Golkar A, Lonsdorf T B, Olsson A, et al. Distinct contributions of the dorsolateral prefrontal and orbitofrontal cortex during emotion regulation[J]. PloS one, 2012, 7(11): e48107

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Referee #3

Evidence, reproducibility and clarity

In the manuscript "Decoding frontotemporal and cell type-specific vulnerabilities to neuropsychiatric disorders and psychoactive drugs", the authors integrated brain with no history of neuropsychiatric disorder snRNA-seq data with public GWAS data among 7 psychiatric disorders to explore the heterogeneity between temporal lobe (TL) and frontal lobe (FL), the genetic risk factors and potential drug responsible genes. Multiple bioinformatics technics have been used in the manuscript. The authors found critical pathways and key genes that are related to the psychiatric disorders and GWAS genes enriched cells such as PVALB cells, which can help the understanding in the field. Overall, the manuscript is well written and organized, but there are some issues need to be addressed.

1. The authors integrated the brain snRNA-seq data with GWAS data to annotate the cell type specific expression, which is one of the key points for this analysis, however a more detailed description of the method is lacking.
2. The authors found a set of genes which is associated with psychiatric disorders and specific cell types, for example inhibitory neurons are the most vulnerable cell type to genetic susceptibility through their analysis. The correlation of each cell type and each psychiatric disorders can be discussed.
3. The authors have found a group of interesting genes, such as GRIN2A, DGKI, and SHISA9 and confirmed them with the Allen Brain Atlases. Experimental validation would be helpful to confirm such findings.

Significance

Strength: this manuscript is strong in bioinformatics analysis. Limitation: wet-lab validation of some of the findings would be helpful.

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Referee #2

Evidence, reproducibility and clarity

Paper review: Decoding frontotemporal and cell type-specific vulnerabilities to neuropsychiatric disorders and psychoactive drugs

In their manuscript with the title Decoding frontotemporal and cell type-specific vulnerabilities to neuropsychiatric disorders and psychoactive drugs, the authors describe their work on integrating snRNAseq data from "fresh" human frontal and temporal lobe of three healthy donors with genetic risk factors of 7 psychiatric disorders, bulk RNAseq data from healthy and disease human cortex/ DEG lists from previous studies for 5of the psychiatric disorders, and gene targets for commonly prescribed psychoactive drugs. The authors claim that PVALB neurons in the temporal lobe are most vulnerable to genetic risk factors and even more to psychoactive drugs for psychiatric diseases and suggest GRIN2A and SLC12A5 as the genes that most contribute to their vulnerability.

According to my overall impression, the paper has major problems in terms of quality, clarity, and statistical power. I do not recommend publishing this manuscript in its current form.

The manuscript is unfortunately lacking (supplemental) figures showing the preprocessing, batch effect correction, and cell type annotation of single nucleus RNAseq data. Although this part is described in the methods in detail, it is hard to judge if these parts were done properly if data is not shown in any of the figures. Regarding the batch effect correction, it reads as if the batch effects have been removed for both brain regions separately. This potentially introduces a bias between brain regions that hugely questions the later performed analysis of differential expression analysis in FL vs TL. In any case, this analysis is not convincing since it has been performed on n=3 vs. n=3 samples and is thus tremendously underpowered.

Furthermore, the way that the authors treat GWAS data for disease does not seem to follow best practices. For schizophrenia, last year the largest GWAS so far was published (Trubetskoy et al, Nature, 2022) with very careful prioritization of genes. The authors should re-analyze their data using the gene list from this paper (and similar from other disorders) rather than the gene list that they came up with using their approach. The approach to select genes from different GWAS introduced seems highly arbitrary and leaves the reader unsure about statistical rigor. Similarly, the choice of data set for disease-related differentially expressed genes is unclear as much larger (two orders of magnitude) published data sets exist for many of the disorders. For three of those DEG analyses performed on bulk RNAseq data, for the remaining two the DEG list of papers is used directly -making a comparison complicated. One would have to run DEG analysis in a standardized way for all 5 datasets/ disorders. It would be good to also indicate the respective sample size in Fig. 5a. (On a different note, the OCD publication is Piantadosi et al. 2021, not Sean C.et.al..) In addition, the authors matched brain regions to their regions of interest (frontal and temporal lobe) as shown in Fig. 5a. Still, they vary across disorders, which makes it hard to compare their findings across disorders and does not allow for a general statement about frontal vs. temporal lobe. To generalize for any of those psychiatric disorders I would recommend including more RNAseq studies of the same disorder. Nowadays there are getting more and more case-control single nuclei studies on such disorders published. The authors could also include those by transforming them to pseudo bulk datasets and running their DEG analysis with edgeR as documented. For cell type enrichment of disease signal based on GWAS signal several carefully controlled studies exist using more sophisticated statistical methods (Skene et al., Nature Genetics, 2018, Bryois et al., et al. Nature Genetics 2020, MJ Zhang et al Nature Genetics 2022 to mention a few). I applaud that the authors aim to go beyond this basic characterization but I think it is worrisome that by using less sophisticated (and importantly less controlled) statistical and genetic approaches they reach a different signal -and then they go on and analyze this signal. It is potentially interesting that they reach a different conclusion, but they need to provide a careful statistical analysis to explain how the chosen method is superior or at least different to previous efforts.

Plus:

• Flash-frozen human tissue with little post-mortem delay
• TL and FL comparison: interesting
• Multiple comparison corrections
• Replication analysis included The drug target genes angle is interesting

Minus:

• only n=3, ~45 000 cells making it hard to generalize
• no supplementary figures for the methods (i.e. preprocessing, cell type annotations), thus hard to judge if done properly if they do not show any data - much higher level of transparency needed
• The methods part is not clear, in general, it is only descriptive, with no equations
• Unconvincing determination of DEGs for each disorder
• DEGs and pathways based on n1=1 vs n2=2 feals handwavy
• DEG analysis and cell type annotation are mixed up and it is unclear how DEGs were determined

Unclear:

• Is the background dataset used for enrichment of genetic risk calculation different for each region and cell type? If so? How is this a fair comparison?
• Which subset of GWAS genes is used for Gene co-expression networks

Significance

Mainly weaknesses

Advancement provided by the study remains modest due to low confidence in the findings. Potentially interesting approach but needs to utilize state-of-the-art methodology and data sets. A typical audience would be journals targeting molecular/biological psychiatry

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Referee #1

Evidence, reproducibility and clarity

The authors integrated snRNA-seq analysis with genetic risk and drug-specific signatures to investigate brain regional differences in risk for neuropsychiatric disease and drug response. To replicate the main findings, the authors also analyzed single nuclei data from the Brain Allen Atlas. Overall, the manuscript is very well written. The methods are comprehensive, clear and well-wrtten which is very welcome. The authors have undertaken a large number of bioinformatic investigations using appropriate methodology and careful design.<br /> The main limitation of the work is the small starting sample size. The authors studied 1 frontal lobe sample and 2 temporal lobe samples. Atlhough this information was in Table S3 it would be good to include upfront in the Methods. snRNA-seq was generated on the 10x platform. It would be helpful to know if the 10x step and sequencing was performed as one batch, or as individual batches. Similarly, were the sample libraries all sequenced on the same lane, or different lanes. The authors do not state in the Methods how many nuclei they were targeting and this should be included. Sample pre-processing was well described and standard. In relation to Batch correction - as with any batch correction method, it is unclear whether the correction is adjusting for biological differences or technical. Since this is a study of the differences between FL and TL, would it not be more appropriate not to correct for batch, particularly as the samples were analysed individually - particularly if batch effects were carefully controlled for in the initial study design. The authors should test whether the results are robust to batch correction or not. Differential gene expression analyses between the FL and TL was undertaken using edgeR. It is unclear if this was performed on aggregated counts or not - i.e., sum of counts per gene per cell type. If it was, then with such a small sample size (1 frontal lobe and 2 temporal lobe samples), it is unclear how well edgeR will perform. Similarly, if the DE analysis was performed using individual gene per cell counts, then there is a type 2 error risk due to pseudoreplication. It is reassuring that the primary results were replicated in a second dataset. Moreover, the downstream analyses (functional enrichment analysis, heritability enrichment analysis etc) are designed to cope with noisy data so I'm happy with the broad conclusions. However, where individual genes are mentioned then the authors may wish to confirm the results from edgeR for a few selected genes with a second technique such as qPCR. For example, GRIN2A and SLC12A5. To calculate the enrichment of "genetic risk" associated with psychiatric disorders, the authors used a hypergeometric test for the overlap between cell type specific genes and the GWAS variant-mapped genes for each disease, which is widely used to evaluate the enrichment of genetic risk genes. To identified GWAS variant mapped genes the authors used a GWAS SNP threshold of <10-5, and mapped SNPs to genes using the GWAS DB. The background set of genes is appropriate as is the statistical method. Given the small sample size however, I think it would be helpful to see a sensitivity analysis of the results that (a) uses different GWAS thresholds e.g., 10-6, 10-7, 5x10-8 and (b) uses an alternative SNP to gene mapping tool such as FUMA. Overall, whilst well written, the manuscript as a whole feels overly long. I think it could be improved by a more stringent focus on the most important biological and translational findings.

Significance

Overall, the manuscript is very well written. The methods are comprehensive, clear and well-wrtten which is very welcome. The authors have undertaken a large number of bioinformatic investigations using appropriate methodology and careful design.

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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:

Oxytocin (OXT) is a neuro-hypophysial hormone and exerts its effects through binding to the oxytocin receptor (OXTR). OXTR is expressed by various types of cells, including leukocytes and gastrointestinal cells. Previous studies demonstrated that OXT alleviates experimental colitis and regulates anti-inflammatory response. The authors' group reported that conditional deletion of OXTR in macrophages and dendritic cells exacerbated dextran sulfate sodium (DSS)-induced colitis. In the present study, they aimed to uncover the essential function of OXT signaling in colonic carcinogenesis and colitis by using intestinal epithelium cell (IEC)-specific OXTR knockout (KO) mice. IEC-specific KO mice exhibited markedly increased susceptibility to DSS-induced colitis and Azoxymethane (AOM)/DSS-induced colitis-associated colorectal cancer (CAC) compared to wild-type mice. Mechanistically, OXTR depletion in IECs impaired the inner mucus of the colon epithelium. Furthermore, oxytocin was found to regulate MUC2 maturation through B3GNT7-mediated fucosylation. In human colitis and CAC colon samples, there was a positive correlation between B3GNT7 expression and OXTR expression. Moreover, the administration of oxytocin significantly alleviated tumor burden. These results suggested oxytocin's promising potential as an effective therapeutic intervention for individuals affected by colitis and CAC.

Major comments:

1. Figure 1: The expression levels of many genes are altered in cancer cells. It is unclear whether decreased OXTR expression is the cause or the consequence of CAC in both human cases and mouse experiments. In Figure 1B, the background staining on the control tissue is very high. On the CAC tissue section, the staining appears uneven and OXTR staining appears high where the background is high. Thus, the result is not convincing.
2. OXTR is expressed by many types of cells, including leukocytes, and OXTR expressed by leukocytes is reported to have an anti-inflammatory activity (Mehdi et al., Front Immunol, 2022, 13:864007. doi: 10.3389/fimmu.2022.864007). In this study, the importance of OXTR expressed by leukocytes is not considered.
3. Oxytocin is usually administered by injection. It is unclear how it was administered. Oral administration is probably not effective. There is also no description about the source of oxytocin.
4. The effects of oxytocin could be different between males and females. It might be interesting to present data of males and females separately and comment on the finding. It was previously shown that OT plasma levels (pg / ml, mean {plus minus} SD) were significantly higher in women than in men (4.53 {plus minus} 1.18 vs 1.53 {plus minus} 1.19, p ˂ 0.001), and such differences might be related to behaviors, attitudes, as well as susceptibility to stress response, resilience and social emotions specific of women and men (Marazziti et al., Clin. Pract. Epidemiol. Ment. Health. 2019; 15: 58-63). Male mice are more susceptible to DSS-induced colitis and this could be due to different oxytocin levels.
5. Figure S3: Is the antibody directed to sugar? In the absence of OXTR, MUC2 is almost absent. It is hard to believe that the expression/production of MUC2 is almost completely dependent on oxytocin.
6. Figure 5: The authors indicated that reduced fucosylation was due to the decreased B3GNT7 expression. Addition of L-fucose may not result in increased fucosylation.
7. The effects of fucose supplementation was studied using a colitis model, whereas the effects of oxytocin supplementation was studied using a colon cancer model. Thus, the effects by these two agents cannot be compared.
8. Figure 6: Oxytocin treatment could activate OXTR expressed on both leukocytes and epithelial cells. There is no comment on this subject.
9. Figure 6I: A few mice died after 20 days. Is it correct? What does "day 0" mean in this figure?
10. Figure 7B: Again, the result is not convincing. Leukocytes are reported to express OXTR and many leukocytes are in the colon tissues, especially in colitis tissue. But, they are not positive.
11. Figure 7M: It is good to have a summary figure; however, it appears not accurate. There is no data showing the floxed mice have "Tolerant immune response" and KO mice have "dysregulated immune response".
12. The authors' group previously reported that OT activated IECs to release prostaglandin E2 that was required for the repair of intestinal epithelium after injury (Ref. 11 in this manuscript). What happened to this mechanism?

Minor comments:

1. Mice: There is no reference for the floxed mice. It would be also helpful to add the strain number.
2. Figure 1D: What was the expression level "1"? There is only a small difference between 6.4 (Control) and 6.1 (AOM/DSS).
3. Figure 1J: What caused the increase in spleen weight? Is this a marker for increased inflammatory responses or cancer cell growth?
4. Figure 1K: What was the meaning of the increased expression of each cytokine?
5. Figure 1L: The photos are too small to see the detail.
6. Figure 1M: What was the end point?
7. Page 3: "OXTR Deficiency in IEC Facilitates CAC Depends on Inflammation" This is not a sentence.
8. Figure 2A and I: "% weight loss" were less then 1%. Is it correct?
9. Figure 2N: Hard to see any differences. Too small.
10. Fig 5K: Labels are not complete.
11. Figure 5: Silver color is used for lines and columns but difficult to see.
12. It is unclear at which time point samples were prepared.

Significance

General assessment:

The role of OXT and its receptor OXTR in DSS-induced colitis was previously reported by using systemic or myeloid cell-specific OXTR KO mice. Here, the authors used IEC-specific OXTR KO mice and found that OXTR expressed by IEC cells plays an important role in inflammation-associated colitis and CAC by promoting the post-transcriptional modification of MUC2 via B3GNT7. This is a strength. The major imitation is that they used only IEC-specific KO mice and the relative importance of OXTR on IECs is unclear. In addition, important information necessary to understand the results is missing throughout the manuscript. There are other questions as listed in the comments.

Advance:

Interaction of OXT and OXTR has been demonstrated to protect mice from inflammation-associated colitis. This study went one step further by demonstrating that OXTR expressed by IEC cells plays a protective role in inflammation-associated colitis and CAC by promoting the post-transcriptional modification of MUC2 via B3GNT7.

Audience:

Basic research and translational/clinical.

Field of expertise:

The reviewer is expertized in the field of "cancer and inflammation" but not in "MUC2" or "glycosylation". Keywords: inflammation, chemokines, leukocyte trafficking, tumor microenvironment.

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Referee #2

Evidence, reproducibility and clarity

Summary: In their paper "Oxytocin alleviated colitis and colitis-associated colorectal tumorigenesis by targeting fucosylated MUC2" the authors describe the contribution of oxytocin (OXT) to colonic mucus formation, and its protective contribution to colitis and colon cancer. The authors also describe the mechanism by which OXT execute its alleviating effects on the colon mucus; enhanced B3GNT7-mediated fucosylation. The findings are demonstrated in cell cultures, various mice models, and samples from human patients.

Major comments:

1. A conceptually confusing issue in this work is whether a decrease in OXTR expression is a predisposition, or a result of colonic illness. On one hand, the experiments with OXTR KO mice and cultured cells suggest that pre-existing lower levels of the receptor sensitize the tissue. However, in the AOM/DSS model the control mice present normal OXTR levels whereas mice that received AOM/DSS had lower expression, suggesting that changes in OXTR levels are not a predisposition but a result of the treatment/illness. Additionally, when tissue from CAC patients were analyzed, decreased levels of OXTR were found in sites of wounds but not in adjacent healthy tissue, implying that this decrease is not a genetic treat but a result of external cue. This inconsistency must be sorted out and clearly demonstrated.
2. The study describes a new regulatory pathway for colonic mucin 2, and colon related conditions. Why did the author choose to generate mice lacking OXTR in the entire intestine (small+large) and not a large-intestine specific deficiency? And is there any way to demonstrate that the absence of OXTR in the small intestine does not interfere with the results presented here?
3. The commonly used fixative for mucus and secreted mucins is Carnoy fixative (can be found in many of Hannson G.C and in Johansson M.E.V papers, and many other papers describing colon staining), while the use of formaldehyde and glutaraldehyde is less preservative for mucus layer. This raises a concern regarding the data obtained from aldehyde-fixed mucus samples.
4. The authors found that mice lacking OXTR have lowered levels of B3GNT7, which leads to a decrease in mucin 2 fucosylation and to further damage in the colon. What is the mechanism by which supplementation with L-fucose alleviates these outcomes given that the enzyme that regulates the addition of the fucose to mucin 2 is downregulated?

Minor comments:

1. Some IHC images don't show comparable or similar areas. Specifically, Figure 1 B, Figure 7 F, I.
2. There is a discrepancy between the dosage of DSS used to induce chronic colitis in the text (2%) and in the methods (2.2%). In addition, the difference between concentrations of DSS used to induce chronic and acute colitis (2.2% vs. 2.5%, respectively) is significantly smaller than what is reported in many other papers using these models.
3. In Figure 2 A, I, Y-axis labeling doesn't seem right (compare with Figure 5 G). It looks like the decimal point is a mistake.
4. All Western blots presented in this study lack the molecular weight of the proteins. In many cases it would have been more convincing to see a larger portion of the membrane.
5. Mucin 2 in a large protein (more than 5000 amino acids in human mucin 2), and many disulfide bonds. The authors do not mention if any reducing or denaturing agents were added to the lysis buffers, and whether any other special conditions were employed to separate this huge globular protein on SDS-PAGE gel.
6. The following sentence should be revised: " To examine the effects of fucosylation regulated by OXT on LS174T cells and colonic organoids, we found that..."

Significance

Though the concept of OXT-mediated suppression of colon cancer has been reported (For example: PMID: 34528509, and 31920487), the regulatory pathway by which it exerts its alleviating effect, and all the mechanistic components described in this paper, were not known before. This pathway may be a potential target for therapeutic intervention in various colonic diseases. Moreover, additional mucins may be regulated by OXT in a similar manner, which can extend the importance of these findings to other organs and disease-conditions. This type of findings is of interest to the broad audience of general cell biology as well as to GI clinicians. However, as stated in my comments there are some major issues with the hypothesis, the way data is presented, and in key methods that fundamentally limits my ability to evaluate this paper.

Key words for my field of expertise: Disulfide catalysis, Golgi, mucin

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Referee #1

Evidence, reproducibility and clarity

Summary

In this study, Wang and colleagues present data linking oxytocin signaling to protection against colitis and colitis associated cancer development. To this end, they utilize a Villin-Cre line to specifically remove OXTR only from intestinal epithelia and make use of AOM and/or DSS treatment to induce colitis, colorectal cancer or CAC. OXTRdeltaIEC mice consistently develop worse symptoms and more severe colitis/CAC compared to non-Cre expressing littermates, which appears to be associated with defects in the mucus layer. Using RNA-Seq, they identify the glycosyltransferase B3GNT7 as a differentially expressed gene. Due to its role in O-linked glycosylation, they investigate whether B3GNT7 is involved in mucin production and are able to show that OXT-induced upregulation of MUC2 protein is abolished when B3GNT7 is knocked down. In vivo, co-treatment with oxytocin reduces experimental CAC, which is an interesting that OXT may present a potential treatment option in CAC. The study is quite interesting in that it provides a potential treatment option where the mucus layer, which is often disturbed in IBD, can be impacted in a positive way. Still, there are some things missing to really be able to interpret the full picture and these should be experimentally addressed.

Major comments

• The staining for OXTR in Fig 1B is very strong (especially as others have reported that they were not able to demonstrate OXTR in human samples, Ohlsson et al. PMID: 16678285) - it would be beneficial to confirm OXTR distribution in steady state in mice, especially as you have a great negative control were OXTR staining should be absent from the IECs. Given the observations further in the study, I would also be very curious to see whether OXTR expression is specific to goblet cells, so co-staining with Muc2 would be interesting to include in later figures. The information for the OXTR antibody is also missing from the supplementary methods.
• Fig 1D, Fig S2 - is this whole colon RNA or specifically epithelial cells? This can have major impact on observed expression levels as the relative amounts of epithelial vs. other cell types can drastically change, thereby falsely giving the impression that expression levels in the epithelial cells change, so this really needs to be analyzed in purified epithelial cells. In Fig S2 there is significant OXTR expression remaining in the deltaIEC mice, so this suggests to me that non-IEC cell types are also included.
• The interpretation of the study would benefit from including some steady state/untreated data for the OXTRdIEC mice. For example in Fig 2 the researchers report increased spleen size, increased cytokines etc upon CRC in these mice, but it is important to also show steady state data as these parameters may already be significantly increased in basal conditions in these OXTR deficient mice (especially seeing as Fig 3 claims that under basal conditions the mucus layer is extensively damaged you would expect some phenotype in these mice).
• Special care needs to be taken to preserve the mucus layer during fixation, and from the methods it is not clear whether the authors have taken these technical difficulties into account. Only PFA fixation is mentioned, but it is well-established that the golden standard for imaging the mucus layer is to fix tissues in water-free Carnoy's fixative, as the mucus layer tends to collapse using formaldehyde (see also Johansson & Hansson, PMID: 22259139).
• In Fig 5, the message and conclusions become a bit more fuzzy. Overall fucosylation is measured, but it is unclear whether MUC2 itself is increasingly fucosylated due to OXTR signaling, or that this represents more global changes in the secretory pathway that eventually lead to more efficient MUC2 production. Perhaps an IP using fucose-specific lectin combined with western blotting for MUC2 may be an option to demonstrate whether MUC2 itself becomes increasingly fucosylated due to OXTR signaling?
• The title broadly claims that OXT "alleviates" colitis and CAC through MUC2 fucosylation and Fig 6 indeed shows that OXT treatment affects the outcome of mice in a CAC model, which is very promising, but it also loses the link with the mechanistic insights surrounding MUC2 fucosylation in previous figures. To really definitively make the claim in the title, it's important to investigate whether these OXT treated mice indeed have restored B3GNT7 levels and a thicker mucus layer after AOS/DSS regimen compared to non-OXT treated mice (as one would expect based on the in vitro data using LS174T cells and organoids). Studying the effect of OXT treatment in the regular DSS colitis model would also provide additional support for this claim.
• Optional as I am not a specialist in OXT signaling: I would assume that there are quite some differences between males and females when it comes to OXT and OXTR. Have the authors ever observed differences in staining pattern or expression levels between males and females? The methods state that all groups are sex matched, but I wonder if it may be necessary to include gender as a variable in the analysis?

Minor comments

• I would suggest to include another reference in the introduction and/or discussion, as MUC2 deficient mice are also known to develop colorectal cancer (Velcich et al. PMID: 11872843) and this serves as additional support for why it is important to discover how we can positively impact the mucin layer in IBD patients.
• In Fig 1A GEO data is reanalyzed, but it's not immediately clear what the original samples were (i.e. colon biopsies). At first glance, the figure itself adds to this confusion with the titles 'hypothalamus' and 'hypophysis' - it's not very clear that these labels indicate synthesis location of the respective hormone and not the tissue where expression was measured.
• Fig 1C - I could not find in the methods what software was used for these quantifications.
• Fig 1C - N=5 is mentioned in the figure legend and there are 10 datapoints in each group. Were 2 biopsies quantified per patient then? Please state this more clearly.
• Fig 3A, B and all other western blots - please include molecular weight indications in the figure
• Several figures use light grey bars and datapoints, but this color was very hard to see after printing the manuscript.
• The conclusion statement for Fig 3 should be revisited, as the expression of Muc2 mRNA is not affected at all by OXTR genotype (Fig S2F). Conclusion should make it clear that specifically (mature) protein levels are affected.
• Fig 4A-D - would be nice to include the full list of DE genes in supplement, it's an important resource. For example, there are other factors known that influence the mucus layer (such as AGR2), so I would be interested to see how these are behaving in the knockout mice.
• In Fig 4 H-J it would be informative to show the MUC2 mRNA expression level in these cultures as this could provide support for the mice data - i.e. do the cultures also display normal MUC2 mRNA levels, with a specific defect in the mucin maturation (as appears to be the case in mice)?
• Fig S3H-K - this figure and the validation of the siRNA is not mentioned in the main text
• It is interesting that L-fucose seems to partly reverse the effect of DSS, but I wonder whether mechanistically this is explained by restoration of B3GNT7 expression?
• Please check the accession codes for the reanalyzed datasets, figure legends mention two accessions, while the Data availability statement mentions three accessions.
• The number of repeats for each experiment is a bit unclear. It is now buried in the statistics statement in the methods, but it may be more clear if it is included in each figure legend.

Significance

This study shows a -for me- quite unexpected link between oxytocin and protection against colitis and colitis-associated cancer development. Disturbances in the mucin layer are a very common phenomenon in IBD and colitis and there has been a great interest in this in the scientific community for quite some years (Johansson, PMID: 25025717, Yao et al. PMID: 34902790, and many others). Current IBD treatment options are generally aimed at reducing inflammation, but this does not necessarily restore the mucin layer quality. It is therefore quite interesting to see that this is apparently heavily influenced by oxytocin (which already has applications in human medicine), and this provides significant advance to our current fundamental understanding of mucin barrier regulation.

As mentioned in the comments, the study can be further improved. To me, a more detailed investigation into the steady state phenotype of these mice, and a more detailed confirmation of where the oxytocin receptor is expressed is necessary to fully put the results into a broader framework. Also Fig 6, where the actual interventional effect of oxytocin is evaluated, no longer demonstrates whether this indeed happens through the same mechanism as outlined in the previous figures and this should be developed more.

I expect this study to be of interest primarily to a basic research audience, though I assume that a more clinical audience would be intrigued by the findings as well.

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Reply to the reviewers

__Points raised by both reviewers in their cross-comments __

1. “emphasizing the acute nature of the study is important as well as the use of only male rats” RESPONSE: Thank you for pointing this out. It has been clarified throughout the manuscript, including the abstract, limitations section, and conclusions.

“The need for improvement of the presentation cannot be stressed enough”.

RESPONSE: The manuscript has undergone extensive revisions to enhance the clarity of data presentation and discussion, and to highlight its novelty in comparison to our prior studies. We have reduced the use of technical terminology and abbreviations, and when they do appear, they are explained with their first use and in the new Glossary section. The manuscript has been better organized, ensuring a logical flow of data and conclusions.

Reviewer #1

Major comments

“the extensive statistical analysis done for the gene expression would require assistance unless the in-house expertise already existed. If these are in place the work could be reproduced with the details provided.”

RESPONSE: Terms and abbreviations used in statistical and correlation analyses are thoroughly explained in the text and in the newly added Glossary section in the revised manuscript to the extent acceptable in a biological paper.

All statistical codes are accessible in the public GitHub repository at https://github.com/YaromirKo/biostatistics-nms. These codes may be utilized for the purpose of replicating studies.

Minor comments

“It is not clear how the genes that were studied here were picked. It is clearly stated what groups the genes fall into and their relevance to the study but it isn't clear how these were decided upon. Clarifying this would be helpful.”

RESPONSE: There is currently no consensus regarding the classification of genes as related to neuroplasticity. In particular, there is no agreement on lists of genes consistently associated with neuroplasticity across studies, and providers of mRNA analysis platforms do not offer panels of neuroplasticity-related genes. Most companies, such as Thermofisher, Illumina, and Nanostring, provide "Neurological" or "Neuropathology Research" panels that contain genes related to neuroplasticity. However, these panels are not specifically designed for targeted analysis of neuroplasticity-related genes.

The gene selection is arbitrary, and the chosen genes may vary across different studies depending on their objectives. In the present study, genes were selected based on several significant works having determined that these genes were likely related to neuroplasticity. Each gene's selection is justified by citing these works in the "Materials and Methods" section and we made every effort to avoid any bias. We do not assert that the gene set is all-encompassing. This matter is addressed in the Limitations section of the revised manuscript.

“It is not always clear what had been done in the previous work and what is completely new in this work, that could be addressed better.”

RESPONSE: Thank you for emphasizing that. It has been thoroughly addressed in the revised manuscript. While our previous study has discovered a left-sided neuroendocrine system, the current work delves into its organizational principles, which are equally crucial. We have shown that this system is bipartite and mirror asymmetric, and that its left and right counterparts can be targeted differently by pharmacological means. Additionally, we have revealed the left-right side-specific gene regulatory networks that operate in the neuroendocrine system and which activities are laterally coordinated by this system along the neuraxis.

“The text and figures are quite complex and require thorough reading the knowledge of the background to understand, therefore not making this work for a general audience.”

“Given the complexity of the work the reading of the results is quite dense and difficult to maneuver unless you have some prior understanding. My suggestion would be to try to simplify this but I wouldn't know exactly how to go about this.”

RESPONSE: We appreciate the Reviewer’s comments here, and agree that this is a complex work. We have endeavored to find a balance between a comprehensive presentation of the methods and results while also providing a level of simplification that will allow the reader who is not versed in this field to still appreciate this work. However, because of the nature of the experimental designs and of the findings that we report, we believe it to be important to provide a comprehensive explanation of the work and results. We believe that we have struck a balance between simplification and comprehensiveness with this revision. We have simplified the presentation of the results, their statistical analysis, and the analysis of gene regulatory networks for easier understanding. We also provide detailed explanations of technical terms in the newly added Glossary section. Please also refer to our response to point 2.

We believe that the revised manuscript has a level of complexity in data presentation and density similar to that of most combined physiological and molecular studies, complemented with advanced statistical and bioinformatics analysis. See please, for example papers published in Plos Biology (doi.org/10.1371/journal.pbio.3002328; doi.org/10.1371/journal.pbio.3002282; doi.org/10.1371/journal.pbio.3001465) and eLIFE (doi.org/10.7554/eLife.85756; https://doi.org/10.7554/eLife.90511.1).

General assessment

“The limitation would be understanding exactly what was done before and how this work expands on that, often it required the reader to look up references and prior work.”

RESPONSE: The introduction and discussion have been modified accordingly in order to comply with this comment. We have clarified how this study expands upon our previous work. In addition, please see the response to Comment 5 that also addresses this issue.

“The audience would be rather specialized, although it does gear towards clinical translation, this aspect could be highlighted better in the introduction and discussion.”

RESPONSE: Clinical aspects of the findings have been further highlighted in the revised manuscript. In the introduction, we note that the discovered phenomenon could contribute to asymmetrical neurological deficits following stroke and TBI. In the discussion section, we examine mechanical similarities between hindlimb asymmetry in rats and spastic dystonia in patients and hypothesize that the rat asymmetries may model this human neuropathology. In the concluding remarks, we state that it is crucial to examine the balance between neural and endocrine pathways in their contribution to neurological impairments, and to establish pharmacological approaches targeting the neuroendocrine system to restore the disturbed neurohormonal equilibrium.

“Those interested in brain injury/neurodegeneration as well as how signaling of motor control could be affected by not just damage to electrical descending motor tracts but to neuroendocrine signaling would be the specific audience.”

RESPONSE: We agree that the experts in neurotrauma, stroke and motor control may be interested in this study. However, the left-right side-specific neuroendocrine signaling may be a general biological phenomenon essential for regulation of lateralized brain functions, and, in a broader biological perspective, regulation of the body plan along the left-right axis.

Furthermore, the study presents what, to the best of our knowledge, is the first evidence for the existence of the left and right side-specific gene regulatory networks in the CNS. They operate in the neuroendocrine system and its peripheral target, and are coordinated across them via the humoral pathway. This is a novel molecular dimension in asymmetric organization of the generally mirror-symmetric CNS.

We are confident that experts in the establishment of the body plan and functional and molecular brain asymmetries will be interested in the concept formulated in this study.

Reviewer #2

Major comments:

“It should be made clear in the introduction that an acute complete cervical SCI is used and the discussion should be extended to include advantages and disadvantages of the used model and the alternatives.”

RESPONSE: Thank you for your suggestions. The introduction and discussion have been supplemented with the requested information. Specifically, we have noted that hindlimb postural asymmetry, a proxy model for neurological deficits, has enabled the discovery and characterization of the left-right side-specific neuroendocrine system. It is a binary model with two qualitatively different responses generated on either the left or right side. On the other hand, it cannot be used to analyze awake animals, and knowledge of its mechanisms is limited. A role for the neuroendocrine phenomenon in the persistent left-right specific biological and pathophysiological processes requires further investigation. This can be addressed by analyzing the effects of unilateral TBI in subchronic experiments with awake animals whose spinal cords are completely transected to disable neural pathways. The methodology could involve an integrated evaluation of hindlimb function during body weight-supported stepping, utilizing behavioral, electrophysiological, and biomechanical measures.

“A similar concern poses the use of pentobarbital and the interpretation of the results of the deafferentation. Were timing of the application and dosage strictly controlled between the different groups? It's effects on somatosensory afferent transmission through presynaptic inhibition are a concern.”

RESPONSE: Thank you for the remark. We have paid special attention to this issue. The rats were deeply anesthetized with the same dose and timing of anesthesia. These parameters were thoroughly controlled in all of the experiments. The depth of pentobarbital anesthesia was characterized by a barely perceptible corneal reflex and a lack of overall muscle tone. Of note, the side and magnitude of postural asymmetry do not apparently depend on anesthesia and its type; the asymmetry was virtually the same after brain injury in rats under deep pentobarbital or isoflurane anesthesia (this study and Lukoyanov et al., 2021; Watanabe et al., 2020; Watanabe et al., 2021; Zhang et al., 2020) and also in decerebrate unanesthetized rats (Zhang et al., 2020). Similar left-right differences were observed in the rats with left and right brain injury which were deafferentated 3 days later, and then analyzed under isoflurane anesthesia (Zhang et al., 2020). This is discussed in the revised manuscript.

Furthermore, no nociceptive stimulation was applied and tactile stimulation was negligible in the course of the asymmetry analysis; the legs were stretched by pulling the threads glued to nails of the toes. The application of lidocaine to the toes, which were pulled during stretching, had no impact on the formation of asymmetry. After all, the stretch and postural limb reflexes are immediately abolished and remain so for several days, and markedly decreased under anesthesia as it was firmly established in many studies. As these reflexes likely do not play a role in the formation of the asymmetric hindlimb posture, their afferent mechanisms could not be a cause of variations in our experiments.

In summary, three main arguments speak against an interference of pentobarbital with asymmetry formation in rats after rhizotomy. First, a similar asymmetry phenomenon developed in pentobarbital anesthetized rats, isoflurane anesthetized rats, and decerebrate un-anesthetized rats. Second, in rats that underwent rhizotomy, the primary sensory nerve fibers were entirely severed. Thus, the hypothetical link between pentobarbital's impact on asymmetry through its effect on presynaptic inhibition could be eliminated. Third, although there may be some variability in the depth of anesthesia among animals, the probability of such strong and statistically significant differences in the effects of brain injury and deafferentation arising from bias in the depth of anesthesia among groups of animals likely to be negligible.

*“Only two test for the asymmetry of spinal processing were used and the two tests are likely measuring very similar phenomena (tonic flexor over activation). Additional reflex tests could shed light onto underlying mechanisms.” *

RESPONSE: We agree. In previous studies, we also analyzed asymmetry in withdrawal reflexes between the left and right hindlimbs as an indicator of the effects of brain injury (Lukoyanov et al., 2021; Watanabe et al., 2021; Zhang et al., 2020). In the present study, we do not focus on the neurophysiological mechanisms of postural asymmetry. We instead prioritize characterizing the phenomenology and organizational principle of the left-right side-specific neuroendocrine system using the postural asymmetry model as a "black box" and as a robust and reliable readout.

Of note, there are several other equally important issues that remain to be addressed, including the identification of signaling pathways from the injured cortex to the hypothalamic-pituitary system, the identification of signaling molecules in the blood that convey information about the side of the brain injury, and the dissection of encoding and decoding mechanisms in the hypothalamus and spinal cord, respectively. No single study could investigate all of these mechanisms.

Minor comments:

“Figure 3 shows only the magnitude of the postural asymmetry in response to the different opioid receptor antagonists, yet the directionality is of interest, especially in case of the control animals. Pre2 values are missing too.”

RESPONSE: We appreciate the reviewer's comment and apologize for any errors in our previous version. The legend for Figure 3 has been revised and simplified. It is unnecessary to include PAS (Postural Asymmetry Size) in addition to MPA as the direction of PAS in all animals in each group was the same. This is stated in the revised manuscript's Legend for Figure 3. MPA was used to compare the left and right UBI groups, which had positive and negative PAS values, respectively. This comparison could not be carried out with PAS.

“Too many abbreviations are used which makes the text and figures very difficult to read at times.” “Terminology is sometimes inconsistent (e.g., delta vs contrast).”

RESPONSE: The manuscript now features a reduced amount of abbreviations. Technical terms and abbreviations are defined upon their first use and are also included in the newly added Glossary section. Corrections have been made to the use of the term "contrast" and its abbreviation "delta" in Figures. Additionally, the term "deltaW" as the left-right difference is no longer utilized within the manuscript.

“The section "correlation patterns in the hypothalamus and spinal cord" was almost impossible for me to understand and could use rephrasing.”

RESPONSE: We apologize for the previous version, and have simplified the presentation of molecular data. We believe that the level of complexity in the revised manuscript's statistics and data presentation is now comparable to that of many other molecular studies featuring system-level analyses; please see also response to Comment # 6 of the first reviewer.

“Only male rats are used.”

RESPONSE: This limitation has been addressed in the Limitation section. It is important to investigate whether identical or distinct neurohormones are responsible for the outcomes of left and right brain injury in male and female rats. However, this requires prior identification of most hypothalamic neurohormones and neuropeptides that regulate the asymmetric processes. Their number may be considerable, given the constellation of left and right gene regulatory networks in the hypothalamus.

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Referee #2

Evidence, reproducibility and clarity

Watanabe et al. build on their previous work to show that the left-right side specific effect of unilateral brain injury after acute complete spinal transection is indeed mediated by side-specific endocrine signaling. This is done by looking at a cervical spinal transection as opposed to a thoracic as in previous work. They further characterize the side-specific humoral hypothalamus-lumbar spinal cord pathways using gene expression patterns, application of opioid receptor antagonists, and dorsal root rhizotomy. Overall the evidence is very convincing and excludes mediation through the sympathetic system in addition to central descending tracts. Curiously the deafferentation, while having an effect on both sides only reversed the postural asymmetry caused by left-sided brain injury, and gene-gene co-expression revealed ipsilateral coordination.

Major comments:

• It is possible that many of the observations in the paper are dependent on the acute state of the spinal cord injury. This is mentioned in the limitations section and it is clear that the presented experiments are important and advance our understanding of this curious phenomenon. Yet, it should be made clear in the introduction that an acute complete cervical SCI is used and the discussion should be extended to include advantages and disadvantages of the used model and the alternatives.
• A similar concern poses the use of pentobarbital and the interpretation of the results of the deafferentation. Were timing of the application and dosage strictly controlled between the different groups? It's effects on somatosensory afferent transmission through presynaptic inhibition are a concern.
• Only two test for the asymmetry of spinal processing were used and the two tests are likely measuring very similar phenomena (tonic flexor over activation). Additional reflex tests could shed light onto underlying mechanisms.
• All major comments shouldn't be seen as a request for additional data but only require discussion.

Minor comments:

• Figure 3 shows only the magnitude of the postural asymmetry in response to the different opioid receptor antagonists, yet the directionality is of interest, especially in case of the control animals. Pre2 values are missing too.
• Too many abbreviations are used which makes the text and figures very difficult to read at times.
• Terminology is sometimes inconsistent (e.g., delta vs contrast).
• The section "correlation patterns in the hypothalamus and spinal cord" was almost impossible for me to understand and could use rephrasing.
• Only male rats are used.

Referees cross-commenting

I agree with reviewer #1's comments; most of them are in line with mine. The need for improvement of the presentation cannot be stressed enough. This is excellent and important work, which makes it even more important to convey it in an accessible way (be clear about prior work and what the novel results add, reduce number of abbreviations, guide the reader in how to interpret the figures, etc.). Otherwise, the audience will be limited.

Significance

General assessment: The manuscript provides clear evidence that there is a side-specific effect of UBI that is mediated by humoral signaling. Specifically, the present work excludes the sympathetic system. This is a very important finding that was missing in previous work. Further characterization of this recently discovered non-neuronal component of UBI is of very high importance as the potential for clinical implications are high.

Advance: The study provides a clear advance of our understanding of side-specific endocrine signaling to the spinal cord.

Audience: This study should be of interest to a wide audience, particularly for neuroscientists and neurologists who deal with the motor system.

My field of expertise: Neural control of locomotion, spinal cord injury, motor control, sensorimotor integration.

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Referee #1

Evidence, reproducibility and clarity

Summary

Watanabe et al. show in "Bipartite left-right sided endocrine system: processing contralateral effects of brain injury" a continuation of previously published work, that hindlimb postural asymmetry (HL-PA) is due to the neuroendocrine signaling and not the cervical parasympathetic pathways in anesthetized spinal C6-C7 fully transected unilateral brain injured (UBI) rats. Further, this differential neuroendocrine control of the left-right side-specific hormonal signaling is affected differently by either right or left unilateral hindlimb sensorimotor cortex brain injuries. However, bilateral deafferentation (L1-S1) showed that only left-side brain injury was altered, indicating differing inputs. Adding to the previous finding that blocking opioid signaling in UBI non-injured spinal rats leads HL-PA, here they demonstrated this finding holds with right-left differences following a spinal transection. Furthering the previous findings of left-right lumbar spinal gene expression differences, this time they found hypothalmus and lumbar spinal cord gene expression differences that were ipsilaterally coordinated and affected by brain injury.

Major comments

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them? Yes, the claims are supported by the data presented in this manuscript.
• Are the data and the methods presented in such a way that they can be reproduced? The data and methods have been presented in a way that could be reproduced, however given the expertise of this laboratory in developing new systems not for purchase it is likely it would take a given expertise to replicate the data. Additionally, the extensive statistical analysis done for the gene expression would require assistance unless the in-house expertise already existed. If these are in place the work could be reproduced with the details provided.
• Are the experiments adequately replicated and statistical analysis adequate? Yes, the experiments have been adequately replicated and statistical analysis to my understanding is adequate.

Minor comments

• Specific experimental issues that are easily addressable. It is not clear how the genes that were studied here were picked. It is clearly stated what groups the genes fall into and their relevance to the study but it isn't clear how these were decided upon. Clarifying this would be helpful.
• Are prior studies referenced appropriately? It is not always clear what had been done in the previous work and what is completely new in this work, that could be addressed better. The references themselves are extensive and well-used throughout the work.
• Are the text and figures clear and accurate? The text and figures are quite complex and require thorough reading the knowledge of the background to understand, therefore not making this work for a general audience.
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? Given the complexity of the work the reading of the results is quite dense and difficult to maneuver unless you have some prior understanding. My suggestion would be to try to simplify this but I wouldn't know exactly how to go about this.

Referees cross-commenting

Reviewer #2 makes a crucial point that emphasizing the acute nature of the study is important as well as the use of only male rats. Otherwise, reviewer #2's comments overlap partially with my own in increasing the accessibility of the work. Neither recommended changes would require new experimental data.

Significance

General assessment:

I would this topic quite intriguing and a novel understanding of motor control. The multiple experiments that were performed that addressed various contingencies of HL-PA may occur after UBI were addressed here (ie. parasympathetic and sensory input). Further experiments expanded on previous findings of the involvement of opioids, the pituitary gland, and spinal gene networks. The limitation would be understanding exactly what was done before and how this work expands on that, often it required the reader to look up references and prior work.

Advance:

Although this is my first encounter with the work, it is a follow-up study on work that was published previously in eLife in 2021. Therefore, given some of the overlap it wouldn't be entirely conceptually new but it would be addressing open questions which arose from that work and further add to our understanding of the mechanism involved in this phenomenon.

Audience:

The audience would be rather specialized, although it does gear towards clinical translation, this aspect could be highlighted better in the introduction and discussion. Those interested in brain injury/ neurodegeneration as well as how signaling of motor control could be affected by not just damage to electrical descending motor tracts but to neuroendocrine signaling would be the specific audience. My expertise is in spinal cord injury, sensorimotor coordination of hindlimbs and gene expression. Although not an expert in brain injury or neuroendocrine signaling, my background allows me to understand the experiments performed here and the relevance of the work.

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Reply to the reviewers

We thank the reviewers for their constructive and detailed reviews. We have been able to resolve all issues raised by the reviewers with additional experiments and changes in the text:

• In response to two of the reviewers we've changed the nomenclature of the residues. As we would like to avoid assigning roles in the naming, we now use 'critical residue 3' and 'critical residue 4', with Cys and His forming critical residue number 1 and 2 respectively.
• We analyzed the role of the negative charge in the fourth critical residue of USP1, by mutating this Asp to Asn to assess the importance of a charged residue in these positions (Supplementary figure 2), resulting in complete loss of activity just like the alanine mutant. We also tested the effect of mutating the third critical residue to Asn in USP1, which causes a minor decrease in activity. This highlights the importance of the highly conserved aspartate (fourth critical residue), and shows that precise residue found in the position is important for catalysis. Additionally, these mutants address potential effects of the ‘holes’ left by the original Ala mutations.
• Importantly, we were able to perform single-turnover assays to expand on our analysis of the precise roles of the critical residues and give more fundamental insight in the defects of the mutants. These assays further elaborate on the variability observed between these USPs. In USP15, these experiments explain the defect in catalysis for the third critical residue mutant and provides insight how a successful nucleophilic attack is combined with defective catalysis (updated Figure 4), which is not observed in the other USPs we tested. In these other USPs, the single turnover experiments reveal that the nucleophilic attack performed by the third and fourth critical residue mutant of USP7 and USP40 happens with low efficiency, even lower efficiency for USP48 and that this ability is lost entirely in USP1.
• We included a number of important textual changes to better explain the choices and variation in USPs tested, highlight prior USP2 data and the implications for drug discovery.
• We updated Ub-PA conjugation assays (updated Figure 4) for better contrast, and repeated the Ub-PA assay for USP1 and USP48 with longer incubation (Supplementary Figure 6). More details are given in the point-by-point response below. All in all, we are convinced that this much improved manuscript is now ready for publication and hope that all reviewers will agree.

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

Summary: The authors study the functional role of two adjacent active site residues as candidates for polarising the catalytic histidine in the "Asn/Asp" box from five phylogenetically unrelated ubiquitin specific proteases (USP1, USP7, USP15, USP40 and USP48). One of these residues is more variable across USPs (Asn, Asp, Ser), whereas the second one is absolutely conserved (Asp). To this end they use alanine mutants in kinetic experiments and test their ability to crosslink to ubiquitin propargyl as a proxy for testing the nucleophilicity of the catalytic cysteine. They then further evaluate the activity of the USP1 mutants in processing PCNA-Ub in RPE1 cells. They find that the role of these two residues differs between the different USPs studied, which is in line with previous work that has shown that in USP7, the amongst USPs less conserved residue takes on the major role of polarising the histidine, whereas in the more distantly related USP2, the absolutely conserved Asp is more important (Zhang W, et al. Contribution of active site residues to substrate hydrolysis by USP2: insights into catalysis by ubiquitin specific proteases. Biochemistry. 2011 50(21):4775-85. doi: 10.1021/bi101958h). This study expands on these findings to evaluate the role of these residues in four other USPs.

Major comments: 1. The authors compare highly diverse USPs; USP1 requires UAF1 for full activity and the complex is used in the study, USP7 requires a C-terminal tail peptide for full activity, USP40 and USP48 belong to the CHN class, whereas USP7, USP15 and USP1 belong to the CHD class of USPs. The rationale for selecting this diverse set of USPs is therefore not clear and makes direct comparisons of the findings more difficult. It is certainly interesting that the previously published differences between USP2 and USP7 with respect to these residues are also found in four other divergent USPs, but for this reason it isn't as "surprising" as the title suggests. The title, omission of background knowledge on USP2 in the abstract and presentation of the findings in a graph that makes direct comparisons (Figure 5) are therefore a bit misleading, which needs addressing.

• We apologize that it seemed as if we had overlooked USP2, for which both critical residues are important, and we agree that our abstract previously focused too much on the perception of the field and its focus on USP7. We have changed the abstract and introduction to highlight the USP2 data for a more balanced perspective.
• The reviewer is correct that the set of USPs is diverse, but we see this as a strength, given that this is the first manuscript in which these residues are analyzed in a comparative side-by-side manner for multiple DUBs. We find that our results are not directly related to the CHN/CHD diversity (i.e. changes in the third catalytic residue), nor apparently to activation by a C-terminal tail (as both USP7 and USP40 have this mechanism). Since these are structurally conserved enzymes with a common fold, we do find the comparison is informative. Furthermore, we felt that it was important to clearly signal the variation in different steps of the mechanism, something which appears to largely remain unnoticed by the field. Figure 5 is helpful in understanding that these changes have multiple dimensions. We agree that it is important to signal the diversity as possible source for these differences and we have added the following sentences to paragraph 3 of the results: “These USPs vary in domain architecture and allosteric regulation, and therefore represent different aspects of the USP family. USP1, USP7 and USP15 both harbor two aspartates as third and fourth critical residue and USP40 and USP48 harbor an asparagine and aspartate as third and fourth critical residue respectively, allowing us to examine the importance of a negative charge in position of the third critical residue.”
• We used the word surprising in the title to indicate the variability we observed in the two dimensions of the mechanism, as indicated in Fig. 5.

The study relies on single alanine mutations, which will inevitably change the hydrogen bonding patterns and the local environment which could impact the conclusion. The authors should verify in kinetic assays at least for USP1, which is the main focus, that Asp to Asn mutants still display the same effects.

• We are thankful for this suggestion. We have made these additional USP1 mutants through insect cell expression and tested these in different assays. As expected, both Asn mutants follow the alanine mutations. The results are reported in Supplementary fig 2BC.

While neither mutant unfolds below 40 degrees, there are clear differences in thermal stability between some of the proteins used in the study (Supp. Fig. 1B). A full table of measured Tms by NanoDSF for all Wt and mutant proteins should be provided so that the reader can evaluate how the results may be impacted by local effects that impact the thermal stability. It is noticeable that USP40 and USP15 mutants in particular display large differences in thermal stability, which could directly affect the results. The authors should clearly discuss these limitations of the study.

• We have added supplemental table S2 to report the melting temperatures. The effect observed for USP15 is addressed in the results: “While both mutants of USP15 have a decreased thermal stability compared to USP15wt, these variants retain stability until 50 °C, indicating that they are still well-folded and suitable for kinetic assays at room temperature.”. For USP40, it is not the actual measured Tm that deviates a lot, but the measured 350/330 ratio, which is addressed in the legend of supplementary figure 1B “Ratios measured (350 mm/330 mm) varied between some of the mutants (Eg. USP40wt), but this did not affect the measured inflection points (Supplementary table 1)”.

  Minor comments: 1. For USP48 and USP40 no published structures are available at present, so it isn't clear whether there are any differences in orientation of the studied residues. An unpublished USP40 structure is referred to but not shown. The general conclusion that structures do not reveal any differences in these residues may therefore not be valid for all the studied USPs. Please revise.

• We apologize if this was not clear. We did however not refer to a USP40 structure, but a USP40 manuscript in preparation that studies biochemistry USP40 activation through activation by its C-terminal tail.

• The existing structures do not show observable differences in the active site residues, nor in the immediate surrounding, and therefore do not give insight which residue is critical for catalysis. We now mention this more explicitly. “It was previously shown that there are no structural differences in the positioning of the catalytic triad and the fourth critical residue between USP2 and USP7, despite their third and fourth critical residues behaving differently (Zhang et al., 2011). We superimposed the currently available crystal structures of USP catalytic domains (Table 1, Figure 1E) and also found only minor differences in the positioning of these two adjacent residues.”
• As the AlphaFold predictions for USP40 and USP48 closely resemble the known structures in Figure 1E, we have added this information as follows : “While the structures of USP40 and USP48 have not been solved, they contain the conserved USP catalytic domain and AlphaFold predictions for USP40 (Uniprot: Q9NVE5) and USP48 (Uniprot: Q86UV5) do not suggest major changes in their catalytic domains."

The introduction of the new terms "critical residue 1 and 2" are confusing and partially disproved by the study itself (replace with e.g. less conserved versus absolutely conserved 3rd triad residue or similar), please revise.

• Thank you, this issue is also mentioned by reviewer 2. We aimed at a solution that would not make inferences on mechanisms. We settled on "critical residue 3" and "critical residue 4", with the active site Cys and His being the first two.

p. 3/4: please add pH information to buffers used in the stability studies. "Previous publication" and "manuscript in preparation" are contradictions.

• pH information has been added.
• Thank you for the comments, we've adjusted the text.

p. 4. Assay buffer for USP1, USP7 and USP48 pH information is missing

• We have corrected the omission.

p. 6: last heading: typo is dispensable

• Typo was corrected.

p. 8: please explain choice of USP1 C90R mutation

• Other mutations tend to increase affinity for free ubiquitin, and in cells this can change ubiquitin homeostasis. The Cys to Arg mutation was shown to avoid this problem in some DUBs. (Morrow et al, Embo Rep 2018 Oct;19(10):e45680. doi: 10.15252/embr.201745680). We have added the reference in both the methods and results sections.

Explain choice of pH range 7-9 studied with regards to anticipated pKas

• We primarily aimed to look at the catalytic cysteine, which needs to be deprotonated in order to allow for catalysis. The sentence on pKas has been removed to avoid confusion. Since the catalytic cysteine in USPs typically has a high pKa, we decided to look at an increased pH to favor partial Cys deprotonation. To that, we have added a reference on USP7, in which it was previously shown USP7 is activated by a higher pH, which holds true for both full-length and its catalytic domain (Faesen et al., (2011). Molecular Cell, 44(1), 147–159. https://doi.org/10.1016/j.molcel.2011.06.034).

Importance of mutagenesis for studying enzymatic mechanisms is clear but limitations also need to be discussed; introduction of local changes etc.. this should be added to the discussion

• We have extended the discussion of limitations as requested. Importantly, the new USP1 asparagine mutants relieve some of the limitations of using alanine substitutions, which we also addressed in this section of the discussion: “While alanine mutations leave open an empty space, or take away the negative charge whenever an aspartate is mutated, mutating both critical residues to asparagine in USP1 did not alleviate the decrease in catalytic competence. Additionally, all single critical residue mutants remained stable and some mutants retaining most of their catalytic competence suggests that these enzymes still function properly.”

  Table 1: linear not lineair

• Thank you. We have made the change.

Table 2: add information for mutant names (exact residue numbers) these data correspond to to improve clarity

• Thank you. We have made the change.

Fig. 1D which structure is shown?

• USP7 (1NBF), we have adjusted the legend.

Fig. 4 bands for USP1/UAF1 D752A and USP15 WT/mutants very faint so difficult to see whether there is crosslinking or not, please comment

• We performed the experiment again and made new figures with better contrast.

Fig.5: please see above for comment about graph and remove or revise.

• We have adjusted the legend to make the diversity more clear: “These five USPs share the conserved USP catalytic domain but vary considerably in domain architecture and allosteric regulation, and therefore represent a part of the diversity found in the USP family.”

Suppl. Table 2: global fit analysis not appropriate for when a poor fit was obtained or where the mutants were barely active (Figs S2, S3). These constants should be removed from the table or more information on the fitting provided. There seems to be some correlation between barely active mutants and the thermal stability, please comment.

• We prefer to do the global fit analysis, as it enables us to share rate constants and get meaningful comparisons. All USP variants were fit simultaneously using the global fit approach where k1 and k-3 rate constants were fixed, k-1 and k3 were shared for all the data sets of the same USP and only k2 was fitted for each data set separately. The quality of the global fit correlates with standard errors of k-1 and k3 rate constants. So, the model we use fits reasonably well with all the data sets all together. Even though a few fitted curves are not aligned well with some of the data for mutants with low activity the value of k2 is still important to report since it gives an approximation of magnitude for the catalytic activity and high standard error reflects the quality of the fit for those specific data sets. In addition, kcat/Km values for all the proteins, including low activity mutants, calculated from global fit approach correlate well with the values calculated from Michaelis-Menten analysis. We clarified this in the legend of supplementary figure 3: “Our kinetic model fits the data well. No fit could be obtained for USP15D880A since no activity was detected. We got relatively poorer fits to USPs with low activity, USP1D752A, USP7D481A). Still, for these low activity USPs the reported Kcat/Km gives an approximation of the magnitude for the catalytic activity and the poorer fit is reflected by their relatively higher standard errors reported in supplementary table 3.”

Suppl. Fig. 1B: See above.

• See comment on 3.

  **Referees cross-commenting**

  reviewers' comments are balanced

  Reviewer #1 (Significance (Required)):

  The study builds on previous work on USP7 and USP2 and while not a conceptual advance, adds to our understanding and knowledge of USP mechanisms. The in cellulo work of probing critical residues in USP1 for processing PCNA-Ub adds a new dimension. However, the limitations of some of the experimental design, stability of mutants and choice of USPs (as outlined above) somewhat hamper the direct comparisons the study makes and previous work needs to be adequately represented (USP2). The work will be of interest to basic researchers and medicinal chemists in particular.

• We very much appreciate the enthusiasm of the reviewer for our cellular validation.

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

  Dr. Sixma is a leading expert in DUB enzymology, especially the enzymology of USP family members. This manuscript is a welcome addition to the field and her body of work to date. Exploring the possibility of redundant or entirely new catalytic residues in USPs is indeed an important venture for differentiating these highly homologous enzymes. The paper is well-written, and the experiments are simplistic and understandable. However, as a whole, the work is not ground-breaking, and the mechanistic explanation of the experimental observation lacks substantiating evidence. The manuscript should be recommended for publication in an appropriate journal after some revision.

  Major comments: - A major concern of the article is about the mechanistic explanation of the role of the second critical residue Asp. The authors proposed two different possible mechanisms, including 1. the residue is flexible to position itself to replace the role of the canonical general base "first" critical residue; 2. Cys/His forms a dyad as seen in other cysteine proteases, and the "second critical residue" Asp participates in the oxyanion hole to stabilize the activated substrate. However, as the authors argue in their discussion, both mechanisms are speculative and have major issues: mechanism #1 requires the catalytic His to flip, and the conformation of the His and "second" critical residue is not optimal for them to form a hydrogen bond directly. The author suggested it may be mediated by a water molecule. However, no such structure has been reported. Mechanism #2 also has the trouble of lacking experimental evidence, and since the tetrahedral oxyanion intermediate is negatively charged, the same negatively charged Asp would be unfavourable. Without mechanistic evidence, the observation of the second (more) critical residue Asp is a very interesting one but beyond that, most of the discussions are speculative. The activity-based labelling experiment using Ub-PA, and the cellular experiments using the mutants only confirmed the observation but can not approve any of these mechanisms.

• Indeed, we do not come with a full mechanistic explanation which explains catalysis in all USPs. Instead, we show that individual USPs have greatly different dependence on their catalytic residue, and thus display important mechanistic distinctions, both for nucleophilic attack and for completion of the reaction. The new Asn mutations do show that negative charge in the 4th critical residue is critical for USP1 function, while the new stopped-flow analysis reveals that USP15 is trapped after the first turnover when the 4th critical residue is lost, and that this is not the case for the other USPs tested.

  • The possibility of substrate trapping in some mutants is of interest. Paragraph 5 of the discussion even mentions this. I think this should be investigated by single-turnover assay techniques.

• We are very thankful for this great suggestion. We performed fast kinetics assays (stopped flow) for all USP wildtype and alanine variants. Together with the Ub-PA labelling experiments these assays shed new light on the ability of these USPs to perform a nucleophilic attack. In terms of substrate trapping, it does indeed turn out that USP15 is inactivated after the first turnover (Figure 4B).

  Minor general concern: - The naming of the Asp/Asn/Ser in the canonical triad is a bit confusing. It is called "the third catalytic residue" and then the "first critical residue" (Intro, last paragraph). This is confusing because, in the catalytic triad, Cys/His are also critical residues. Given the importance of the fourth Asp residue, maybe the authors should come up with a different naming system. One suggestion could be calling the Asp/Asn/Ser the **general base residue** (in the canonical triad terms, Cys is the nucleophile, His is the general acid-base residue, Asp is the general base residue), and the 4th Asp as the "alternative general base residue"?

• Reviewer 1 also did not like the naming. To address the issue we have settled on: "critical residue 3" and "critical residue 4", with the active site Cys and His being the first two. This avoids assigning mechanistic roles to particular residues, but still stresses their importance.

  • The augment at the end of the discussion that this alternative Asp residue could lead to new inhibitors for this difficult class of cysteine proteases is a stretch. The majority, if not all, structurally defined inhibitors of USPs (USP7, USP1, USP14) are allosteric inhibitors that do not target the catalytic triad directly. I doubt the discovery of Asp will change that. The most variability of activity regulation of USPs comes from auxiliary domains of the FL USPs, or cofactor proteins, as the authors' lab has previously demonstrated for many of the USPs, including USP7, USP4, USP1, etc., and there lie more opportunities for new inhibitor discovery.

• We agree that current inhibitors would not make use of these variations, but we feel that our findings could spark an interest in developing new classes that would benefit from the variability. We have adjusted the discussion to make that point more explicitly: “The variety in catalytic mechanisms might allow for development of new types of inhibitors with improved specificities.”

  • Similarly, it is a fancy term to cite of DUBTACs, but I don't see much relevance of this alternative residue applied to DUBTACs. The authors could explore the idea a bit if they decide to cite this.

• Indeed, only if the such new inhibitors can be made. We’ve removed the sentence on DUBTACS.

  Minor comments and grammar: editing is difficult without the inclusion of line numbers. I have attempted to address errors the best I can, considering this.

  • Synopsis: "..., the majority of USPs **does** not..." should be "**do**"

• Correction was made

  • Synopsis: "..., either critical **residues** can..." should be "**residue**"

• Correction was made

  • Intro: "Subsequently a tetrahedral..." should have a comma after subsequently

• Correction was made

  • Intro: 2nd paragraph, line 6, be more specific to be "peptide bond."

• Correction was made

  • Intro: in the 3rd paragraph, the residue numbers of the catalytic residues should be stated.

• The numbers were added

  • Intro: the first line of paragraph 4. The statement is confusing and should be made clearer by simply stating, "The third catalytic residue in USPs is either Asp, Asn, or Ser."

• Correction was made

  • Intro: second last paragraph, be a bit more specific on what "resembles USP15 and USP7" could be "... USP8, another USP whose catalytic triad resembles those of USP15 and USP7" because the domain structure of these FL USPs is very different, only the triad is similar.

• We agree and we apologize for this oversight, we have deleted the sentence on USP8 as it is not relevant in this context.

  • Intro: the last paragraph mentions the loss of function USP15 mutation behaves like wild type and USP1. The term "loss of function" is misleading. If mutation to the canonical 3rd catalytic residue has no effect on activity, then it is not a loss of function mutant. Please specify the alanine mutation.

• We've made this change

  • Intro: last paragraph, "Michaelis Menten," should have a hyphen in between.

• Correction was made

  • Methods: please add a space between values and units; this comes up multiple times throughout the manuscript

• Corrections have been made

  • Methods: all taxonomic names should be italicized, i.e., E. coli

• Correction was made

  • Methods: protein stability section, "**build**-in" should be "**built**-in" (build-in is repeated elsewhere and needs to be fixed)

• Correction was made

  • Methods: structure superposition section, "... bound to ubiquitin were **use** whenever..." should be "...bound to ubiquitin were **used** whenever..."

• Correction was made

  • Methods: pH analysis section, "duplo" should be duplicate

• Correction was made

  • Methods: Expression of USP1 in RPE1 cells section, please briefly state how you determined the expression level of USP1 in transduced RPE1 USP1KO cells when selecting clones with comparable levels to RPE1 wt cells

• We have added an extended description on how we selected these single clones. “To select clones with similar USP1 levels compared to endogenous, single clones were incubated with 1 µg/ml doxycycline for 44 hours and were lysed using RIPA buffer (1% NP40, 1% sodium deoxycholate, 0.1% SDS, 0.15 M NaCl, 0.01 M sodium phosphate pH 7.5, 2 mM EDTA), containing cOmplete™, EDTA-free Protease Inhibitor Cocktail (Roche, 11873580001), 1 mM 2-chloroacetamide and 0.25 U/µl benzonase (SC-202391, Santa Cruz Biotechnology). Total protein concentration in the lysate was determined using a BCA assay (23227, Thermo Scientific) so that equal amounts could be loaded on gel. Samples were loaded on 4-12% Bolt gels (NW04127, Thermo Scientific), and run for 40 minutes at 180 V in MOPS running buffer (B0001, Thermo Scientific). Proteins were transferred to nitrocellulose membrane (10600002, Amersham Protran 0.45 NC nitrocellulose). Membranes were stained with a USP1 antibody (14346-1-AP, Proteintech). After incubation with HRP coupled secondary antibody the blots were imaged using a Bio-Rad Chemidoc XRS+. Using Bio-Rad ImageLab 5.1 software, USP1 levels were quantified by measuring the volume intensities of each USP1 band for each clone and compared this to endogenous USP1 levels in RPE1 cells. Clones with comparable expression levels were selected and used for further experiments.”

  • Methods: tCoffee webserver should be "T-Coffee"

• We realized that multiple sequence alignment was performed using Clustal Omega, not T-Coffee, which has now been corrected. We apologize for this oversight.

  • Methods: MSA. Can the authors provide more details on when doing BLAST, what were the criteria of selecting sequences from the result?

• Details have been added: “Catalytic domains as defined by Uniprot of the resulting human USPs were used for multiple sequence alignment. For USPs with multiple isoforms, the canonical isoform (isoform 1) was selected. In case of the USP17 gene family, USP17L2/DUB3 was selected (Komander et al., 2009). In order to properly align USP1, its inserts were removed from the catalytic domain following (Dharadhar et al., 2021). In order to properly align USP40, a shorter sequence was used (residues 250-480).”

  • Methods: please provide the details for determining the concentration of the enzymes used.

• Details on how we determined the concentrations of enzymes have been added.

  • Methods: Please provide the manufacturers of the Pherastar plate reader and the 384-well plate (please correct from "384 well-plate").

• Info on the manufacturers has been added.

  • Results: In paragraph 1, "lies a **much better** conserved..." you should use "more highly."

• Correction was made

  • Results: paragraph 1, "USP50 does not harbor either of" should be "USP50 harbors neither of"

• We corrected this: “This aspartate is present in all USPs except CYLD and USP50. The latter misses the third critical residue as well and therefore may be inactive.”

  • Supp Fig 2: USP39 does not have glutamate in position of the first critical residue, it is glutamine (Q)

• Correction was made

  • Results: second subsection title **"The first critical residue is dispenUSP1..."** needs to be fixed

• Correction was made as follows: The third critical residue is dispensable in USP1/UAF1, USP15, USP40 and USP48

  • Results: pg. 8 last line "to crosslink", the word crosslink is not proper for the reaction between Ub-PA with USPs. It usually refers to a reactive linker that links two molecules. Words like "conjugate", "conjugation," or "covalent react with", and "activity-based labelling" are probably better choices depending on the context.

• We have corrected this throughout the manuscript.

  • Figure 1: figure legend describing B, C, and D are mixed up.

• Correction was made

  • Results: In paragraph 9, the statement that your data on 5 USPs is representative of most of the 57 members in that the third catalytic is dispensable is not a sound statement for the small sample size. I think more emphasis on the diversity of USP1, USP7, USP15, USP40, and USP48 needs to be stated to help bolster such a claim. The statement to follow, which mentions sequence analysis alone is not able to predict the catalytic residue, is also somewhat contradictory to the opening statement and insinuates that all active USPs should be tested, while you only examined 5.

• We have changed this to ”Our findings demonstrate that for the majority of tested USPs…”. The diversity of tested USPs is clarified earlier in the manuscript: “These USPs vary in domain architecture and allosteric regulation, and therefore represent different aspects of the USP family, known for its structural variety and modular architecture”. The statement about sequence analysis has been removed from the results section and is now only mentioned in the discussion. However, we do think that precise active site assignment for other USPs will require mutagenesis support.

  • Figure 4: legend title, the critical residues are not responsible for **performing** nucleophilic attack per se; that is the job of Cys. The title of the figure should be altered to clear this up.

• Correction was made as follows: " Variation in the ability of USP critical residue mutants to successfully and efficiently facilitate a nucleophilic attack.”

  • Discussion: paragraph 3, since the Hu 2002 USP7 mechanism is not valid for other USPs tested, the "consensus USP catalytic mechanism" should be referred to as the "canonical."

• Indeed! Correction was made.

  • Discussion: paragraph 4, "USP7, USP15 and USP40 all **three** have misaligned..." should be "USP7, USP15 and USP40 all have misaligned..."

• Correction was made.

  • Discussion: paragraph 8, "negative charge itself could **contributes**..." should be "negative charge itself could **contribute**..."

• Correction was made

  • Discussion: pg. 10, 3rd paragraph. Is the first sentence a statement of fact or a hypothesis? The writing is not clear to differentiate the two possibilities.

• Parts of the discussion have been rewritten, but the corresponding sentence has been rewritten as follows: “Canonically, it is thought that the fourth critical residue is involved in oxyanion hole formation.”

  • Discussion: pg. 10, 3rd paragraph, line 3, which "critical residue" does it refer to, the general base residue or the alternative residue?

• We've changed the text as follows: ". A dual role, with the third or fourth critical residue stabilizing catalytic histidine and oxyanion hole formation simultaneously is unlikely”.

  • Discussion: pg. 10, second last paragraph. Can the statement that "inaccurate assumptions about the catalytic triad ... be substantiated with an example?

• We apologize for the possible confusion, but our point here was to point out that it could be misdirecting conclusions if you strictly follow the canonical assignment of the catalytic triad. We have rewritten the sentence to make that more clear: “Additionally, assumptions about the catalytic triad solely based on the canonical catalytic triad assignment in USP could affect conclusions made regarding loss of function mutations in genetic screens. For example, we find that some USPs retain full or most of their activity once their canonical third catalytic residue is mutated.”

  • Table 1, "ubiquitin variant" is mostly often used in the literature to refer to the ubiquitin mutants generated by phage display pioneered by the Sidhu lab or designed mutants. "ubiquitin and homolog derivatives" is a better term for "ubiquitin variant" in this article.

• We have changed this to ubiquitin-like proteins

  • Table 1, the USP21 line "Lineair" is a typo, it should be "linear."

• Correction was made

  • References: citations for Cadzow, 2020. and Tsefou, 2021 do not appear in the bibliography.

• Correction was made

  • Add a hyphen to "Ubiquitin-specific proteases."

• Correction was made

  Reviewer #2 (Significance (Required)):

  General assessment:

  Based on the studies of prototypical ubiquitin-specific protease USP7, the field generally accepts that USPs are a class of cysteine proteases that contain a catalytic triad with a cysteine, a histidine and a general base residue (asparagine, aspartate, or serine). This manuscript described the importance of an alternative, highly conserved aspartate that plays a critical role in catalysis using an enzyme kinetics study on five out of 57 USPs. The work is a very interesting observation that could change the perception in the field. However, the atomic details of how this fourth, or alternative residue, plays its role in catalysis are not clear without the structure evidence of an intermediate/transition state-bound complex.

  Advance:

  The study provided the first systematic enzymology study of the role of a fourth conserved residue critical for the catalysis of USPs. It is a conceptual advance and a first step to elucidate possibly a new catalytic mechanism of USPs.

  Audience: The manuscript will be of interest to biochemists in the field of ubiquitination and drug discovery.

  Reviewers' expertise

  The reviewers are structural biologists with expertise in the structure, function and enzymology of ubiquitin enzymes in general, with practical experience in drug discovery targeting the DUB and kinase families.

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

  The article by Keijzer and colleagues describes an interesting study comparing the active site of multiple USPs (the largest subfamily of deubiquitinases) and elucidating the importance of specific residues lining the active site for catalysis. The authors carried out a careful analysis of the kinetic properties of 5 representative USPs and mutants thereof revealing a remarkable variety in their function that highlights that the majority of USPs studied do not require the canonical third residue of the catalytic triad of USPs for activity but instead rely on a highly conserved second critical residue. Furthermore, the authors apply complementary experimental approaches (mutagenesis, pH dependence of activity, crosslinking with Ub-PA) to allow distinguishing between residues important for the nucleophilic attack versus oxyanion hole stabilisation.

  This is a well-written, thorough enzymatic study of high technical quality. The experiments are described in sufficient detail to allow others to reproduce the experimental set up. The data presented fully support the claims of the paper and no additional experiments are required to further support the conclusions. It is great to see that the authors have carried out thermal stability assays on all WT and mutant proteins under investigation to ensure that any effects observed are not due to protein misfolding.

  Minor comments:

  • There are a few typos in the manuscript the authors should correct.

• Thank you, we have removed the typos from the manuscript.

  • The panels/paper legends to Figure 1B/C/D are mixed up. Please correct.

• Correction was made

  -It would be helpful to use different colours in the alignment shown in Supplementary Figure1 to indicate the position of the first and second critical residue.

• Thank you, we have highlighted these residues

  • I wonder if the authors could comment on how representative the 5 USPs characterised in this work are of the entire family.

• We address the variation of these USPs in more detail, both in the results as in the legend of figure 5: “These USPs vary in domain architecture and allosteric regulation, and therefore represent different aspects of the USP family, known for its structural variety and modular architecture”

Reviewer #3 (Significance (Required)): Deubiquitinating enzymes (DUBs) play essential roles in many cellular processes and their activity is associated with a variety of diseases. There is a lot of interest in targeting DUBs for therapeutic purposes and a number of small molecule inhibitors are undergoing clinical studies. While the structure and mechanism of multiple DUBs have been studied over the years, many open questions about their detailed catalytic mechanism remain and the importance of specific residues might often have been inferred based on sequence conservation alone without accompanying experimental support. This work makes an important contribution to the field by systematically examining 5 members of the USP family and defining the precise role of the first and second critical residue for the catalytic cycle. This work will be of interest to those studying the mechanism of DUBs in general and those trying to target specific DUBs with small molecules. In addition, this study will also be interesting more generally for those studying enzyme kinetics as it highlights the importance of experimental validation of a catalytic mechanism that has been predicted based on sequence conservation or structural studies.

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Referee #3

Evidence, reproducibility and clarity

The article by Keijzer and colleagues describes an interesting study comparing the active site of multiple USPs (the largest subfamily of deubiquitinases) and elucidating the importance of specific residues lining the active site for catalysis. The authors carried out a careful analysis of the kinetic properties of 5 representative USPs and mutants thereof revealing a remarkable variety in their function that highlights that the majority of USPs studied do not require the canonical third residue of the catalytic triad of USPs for activity but instead rely on a highly conserved second critical residue. Furthermore, the authors apply complementary experimental approaches (mutagenesis, pH dependence of activity, crosslinking with Ub-PA) to allow distinguishing between residues important for the nucleophilic attack versus oxyanion hole stabilisation.

This is a well-written, thorough enzymatic study of high technical quality. The experiments are described in sufficient detail to allow others to reproduce the experimental set up. The data presented fully support the claims of the paper and no additional experiments are required to further support the conclusions. It is great to see that the authors have carried out thermal stability assays on all WT and mutant proteins under investigation to ensure that any effects observed are not due to protein misfolding.

Minor comments:

• There are a few typos in the manuscript the authors should correct.
• The panels/paper legends to Figure 1B/C/D are mixed up. Please correct.
• It would be helpful to use different colours in the alignment shown in Supplementary Figure1 to indicate the position of the first and second critical residue.
• I wonder if the authors could comment on how representative the 5 USPs characterised in this work are of the entire family.

Significance

Deubiquitinating enzymes (DUBs) play essential roles in many cellular processes and their activity is associated with a variety of diseases. There is a lot of interest in targeting DUBs for therapeutic purposes and a number of small molecule inhibitors are undergoing clinical studies. While the structure and mechanism of multiple DUBs have been studied over the years, many open questions about their detailed catalytic mechanism remain and the importance of specific residues might often have been inferred based on sequence conservation alone without accompanying experimental support.

This work makes an important contribution to the field by systematically examining 5 members of the USP family and defining the precise role of the first and second critical residue for the catalytic cycle. This work will be of interest to those studying the mechanism of DUBs in general and those trying to target specific DUBs with small molecules. In addition, this study will also be interesting more generally for those studying enzyme kinetics as it highlights the importance of experimental validation of a catalytic mechanism that has been predicted based on sequence conservation or structural studies.

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Referee #2

Evidence, reproducibility and clarity

Dr. Sixma is a leading expert in DUB enzymology, especially the enzymology of USP family members. This manuscript is a welcome addition to the field and her body of work to date. Exploring the possibility of redundant or entirely new catalytic residues in USPs is indeed an important venture for differentiating these highly homologous enzymes. The paper is well-written, and the experiments are simplistic and understandable. However, as a whole, the work is not ground-breaking, and the mechanistic explanation of the experimental observation lacks substantiating evidence. The manuscript should be recommended for publication in an appropriate journal after some revision.

Major comments:

• A major concern of the article is about the mechanistic explanation of the role of the second critical residue Asp. The authors proposed two different possible mechanisms, including 1. the residue is flexible to position itself to replace the role of the canonical general base "first" critical residue; 2. Cys/His forms a dyad as seen in other cysteine proteases, and the "second critical residue" Asp participates in the oxyanion hole to stabilize the activated substrate. However, as the authors argue in their discussion, both mechanisms are speculative and have major issues: mechanism #1 requires the catalytic His to flip, and the conformation of the His and "second" critical residue is not optimal for them to form a hydrogen bond directly. The author suggested it may be mediated by a water molecule. However, no such structure has been reported. Mechanism #2 also has the trouble of lacking experimental evidence, and since the tetrahedral oxyanion intermediate is negatively charged, the same negatively charged Asp would be unfavourable. Without mechanistic evidence, the observation of the second (more) critical residue Asp is a very interesting one but beyond that, most of the discussions are speculative. The activity-based labelling experiment using Ub-PA, and the cellular experiments using the mutants only confirmed the observation but can not approve any of these mechanisms.
• The possibility of substrate trapping in some mutants is of interest. Paragraph 5 of the discussion even mentions this. I think this should be investigated by single-turnover assay techniques.

Minor general concern:

• The naming of the Asp/Asn/Ser in the canonical triad is a bit confusing. It is called "the third catalytic residue" and then the "first critical residue" (Intro, last paragraph). This is confusing because, in the catalytic triad, Cys/His are also critical residues. Given the importance of the fourth Asp residue, maybe the authors should come up with a different naming system. One suggestion could be calling the Asp/Asn/Ser the general base residue (in the canonical triad terms, Cys is the nucleophile, His is the general acid-base residue, Asp is the general base residue), and the 4th Asp as the "alternative general base residue"?
• The augment at the end of the discussion that this alternative Asp residue could lead to new inhibitors for this difficult class of cysteine proteases is a stretch. The majority, if not all, structurally defined inhibitors of USPs (USP7, USP1, USP14) are allosteric inhibitors that do not target the catalytic triad directly. I doubt the discovery of Asp will change that. The most variability of activity regulation of USPs comes from auxiliary domains of the FL USPs, or cofactor proteins, as the authors' lab has previously demonstrated for many of the USPs, including USP7, USP4, USP1, etc., and there lie more opportunities for new inhibitor discovery.
• Similarly, it is a fancy term to cite of DUBTACs, but I don't see much relevance of this alternative residue applied to DUBTACs. The authors could explore the idea a bit if they decide to cite this.

Minor comments and grammar: editing is difficult without the inclusion of line numbers. I have attempted to address errors the best I can, considering this.

• Synopsis: "..., the majority of USPs does not..." should be "do"
• Synopsis: "..., either critical residues can..." should be "residue"
• Intro: "Subsequently a tetrahedral..." should have a comma after subsequently
• Intro: 2nd paragraph, line 6, be more specific to be "peptide bond."
• Intro: in the 3rd paragraph, the residue numbers of the catalytic residues should be stated.
• Intro: the first line of paragraph 4. The statement is confusing and should be made clearer by simply stating, "The third catalytic residue in USPs is either Asp, Asn, or Ser."
• Intro: second last paragraph, be a bit more specific on what "resembles USP15 and USP7" could be "... USP8, another USP whose catalytic triad resembles those of USP15 and USP7" because the domain structure of these FL USPs is very different, only the triad is similar.
• Intro: the last paragraph mentions the loss of function USP15 mutation behaves like wild type and USP1. The term "loss of function" is misleading. If mutation to the canonical 3rd catalytic residue has no effect on activity, then it is not a loss of function mutant. Please specify the alanine mutation.
• Intro: last paragraph, "Michaelis Menten," should have a hyphen in between.
• Methods: please add a space between values and units; this comes up multiple times throughout the manuscript
• Methods: all taxonomic names should be italicized, i.e., E. coli
• Methods: protein stability section, "build-in" should be "built-in" (build-in is repeated elsewhere and needs to be fixed)
• Methods: structure superposition section, "... bound to ubiquitin were use whenever..." should be "...bound to ubiquitin were used whenever..."
• Methods: pH analysis section, "duplo" should be duplicate
• Methods: Expression of USP1 in RPE1 cells section, please briefly state how you determined the expression level of USP1 in transduced RPE1 USP1KO cells when selecting clones with comparable levels to RPE1 wt cells
• Methods: tCoffee webserver should be "T-Coffee"
• Methods: MSA. Can the authors provide more details on when doing BLAST, what were the criteria of selecting sequences from the result?
• Methods: please provide the details for determining the concentration of the enzymes used.
• Methods: Please provide the manufacturers of the Pherastar plate reader and the 384-well plate (please correct from "384 well-plate").
• Results: In paragraph 1, "lies a much better conserved..." you should use "more highly."
• Results: paragraph 1, "USP50 does not harbor either of" should be "USP50 harbors neither of"
• Supp Fig 2: USP39 does not have glutamate in position of the first critical residue, it is glutamine (Q)
• Results: second subsection title "The first critical residue is dispenUSP1..." needs to be fixed
• Results: pg. 8 last line "to crosslink", the word crosslink is not proper for the reaction between Ub-PA with USPs. It usually refers to a reactive linker that links two molecules. Words like "conjugate", "conjugation," or "covalent react with", and "activity-based labelling" are probably better choices depending on the context.
• Figure 1: figure legend describing B, C, and D are mixed up.
• Results: In paragraph 9, the statement that your data on 5 USPs is representative of most of the 57 members in that the third catalytic is dispensable is not a sound statement for the small sample size. I think more emphasis on the diversity of USP1, USP7, USP15, USP40, and USP48 needs to be stated to help bolster such a claim. The statement to follow, which mentions sequence analysis alone is not able to predict the catalytic residue, is also somewhat contradictory to the opening statement and insinuates that all active USPs should be tested, while you only examined 5.
• Figure 4: legend title, the critical residues are not responsible for performing nucleophilic attack per se; that is the job of Cys. The title of the figure should be altered to clear this up.
• Discussion: paragraph 3, since the Hu 2002 USP7 mechanism is not valid for other USPs tested, the "consensus USP catalytic mechanism" should be referred to as the "canonical."
• Discussion: paragraph 4, "USP7, USP15 and USP40 all three have misaligned..." should be "USP7, USP15 and USP40 all have misaligned..."
• Discussion: paragraph 8, "negative charge itself could contributes..." should be "negative charge itself could contribute..."
• Discussion: pg. 10, 3rd paragraph. Is the first sentence a statement of fact or a hypothesis? The writing is not clear to differentiate the two possibilities.
• Discussion: pg. 10, 3rd paragraph, line 3, which "critical residue" does it refer to, the general base residue or the alternative residue?
• Discussion: pg. 10, second last paragraph. Can the statement that "inaccurate assumptions about the catalytic triad ... be substantiated with an example?
• Table 1, "ubiquitin variant" is mostly often used in the literature to refer to the ubiquitin mutants generated by phage display pioneered by the Sidhu lab or designed mutants. "ubiquitin and homolog derivatives" is a better term for "ubiquitin variant" in this article.
• Table 1, the USP21 line "Lineair" is a typo, it should be "linear."
• References: citations for Cadzow, 2020. and Tsefou, 2021 do not appear in the bibliography.
• Add a hyphen to "Ubiquitin-specific proteases."

Significance

General assessment:

Based on the studies of prototypical ubiquitin-specific protease USP7, the field generally accepts that USPs are a class of cysteine proteases that contain a catalytic triad with a cysteine, a histidine and a general base residue (asparagine, aspartate, or serine). This manuscript described the importance of an alternative, highly conserved aspartate that plays a critical role in catalysis using an enzyme kinetics study on five out of 57 USPs. The work is a very interesting observation that could change the perception in the field. However, the atomic details of how this fourth, or alternative residue, plays its role in catalysis are not clear without the structure evidence of an intermediate/transition state-bound complex.

Advance:

The study provided the first systematic enzymology study of the role of a fourth conserved residue critical for the catalysis of USPs. It is a conceptual advance and a first step to elucidate possibly a new catalytic mechanism of USPs.

Audience: The manuscript will be of interest to biochemists in the field of ubiquitination and drug discovery.

Reviewers' expertise

The reviewers are structural biologists with expertise in the structure, function and enzymology of ubiquitin enzymes in general, with practical experience in drug discovery targeting the DUB and kinase families.

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:

The authors study the functional role of two adjacent active site residues as candidates for polarising the catalytic histidine in the "Asn/Asp" box from five phylogenetically unrelated ubiquitin specific proteases (USP1, USP7, USP15, USP40 and USP48). One of these residues is more variable across USPs (Asn, Asp, Ser), whereas the second one is absolutely conserved (Asp). To this end they use alanine mutants in kinetic experiments and test their ability to crosslink to ubiquitin propargyl as a proxy for testing the nucleophilicity of the catalytic cysteine. They then further evaluate the activity of the USP1 mutants in processing PCNA-Ub in RPE1 cells. They find that the role of these two residues differs between the different USPs studied, which is in line with previous work that has shown that in USP7, the amongst USPs less conserved residue takes on the major role of polarising the histidine, whereas in the more distantly related USP2, the absolutely conserved Asp is more important (Zhang W, et al. Contribution of active site residues to substrate hydrolysis by USP2: insights into catalysis by ubiquitin specific proteases. Biochemistry. 2011 50(21):4775-85. doi: 10.1021/bi101958h). This study expands on these findings to evaluate the role of these residues in four other USPs.

Major comments:

1. The authors compare highly diverse USPs; USP1 requires UAF1 for full activity and the complex is used in the study, USP7 requires a C-terminal tail peptide for full activity, USP40 and USP48 belong to the CHN class, whereas USP7, USP15 and USP1 belong to the CHD class of USPs. The rationale for selecting this diverse set of USPs is therefore not clear and makes direct comparisons of the findings more difficult. It is certainly interesting that the previously published differences between USP2 and USP7 with respect to these residues are also found in four other divergent USPs, but for this reason it isn't as "surprising" as the title suggests. The title, omission of background knowledge on USP2 in the abstract and presentation of the findings in a graph that makes direct comparisons (Figure 5) are therefore a bit misleading, which needs addressing.
2. The study relies on single alanine mutations, which will inevitably change the hydrogen bonding patterns and the local environment which could impact the conclusion. The authors should verify in kinetic assays at least for USP1, which is the main focus, that Asp to Asn mutants still display the same effects.
3. While neither mutant unfolds below 40 degrees, there are clear differences in thermal stability between some of the proteins used in the study (Supp. Fig. 1B). A full table of measured Tms by NanoDSF for all Wt and mutant proteins should be provided so that the reader can evaluate how the results may be impacted by local effects that impact the thermal stability. It is noticeable that USP40 and USP15 mutants in particular display large differences in thermal stability, which could directly affect the results. The authors should clearly discuss these limitations of the study.

Minor comments:

1. For USP48 and USP40 no published structures are available at present, so it isn't clear whether there are any differences in orientation of the studied residues. An unpublished USP40 structure is referred to but not shown. The general conclusion that structures do not reveal any differences in these residues may therefore not be valid for all the studied USPs. Please revise.
2. The introduction of the new terms "critical residue 1 and 2" are confusing and partially disproved by the study itself (replace with e.g. less conserved versus absolutely conserved 3rd triad residue or similar), please revise.
3. p. 3/4: please add pH information to buffers used in the stability studies. "Previous publication" and "manuscript in preparation" are contradictions.
4. p. 4. Assay buffer for USP1, USP7 and USP48 pH information is missing
5. p. 6: last heading: typo is dispensable
6. p. 8: please explain choice of USP1 C90R mutation
7. Explain choice of pH range 7-9 studied with regards to anticipated pKas
8. Importance of mutagenesis for studying enzymatic mechanisms is clear but limitations also need to be discussed; introduction of local changes etc.. this should be added to the discussion
9. Table 1: linear not lineair
10. Table 2: add information for mutant names (exact residue numbers) these data correspond to to improve clarity
11. Fig. 1D which structure is shown?
12. Fig. 4 bands for USP1/UAF1 D752A and USP15 WT/mutants very faint so difficult to see whether there is crosslinking or not, please comment
13. Fig.5: please see above for comment about graph and remove or revise.
14. Suppl. Table 2: global fit analysis not appropriate for when a poor fit was obtained or where the mutants were barely active (Figs S2, S3). These constants should be removed from the table or more information on the fitting provided. There seems to be some correlation between barely active mutants and the thermal stability, please comment.
15. Suppl. Fig. 1B: See above.

Referees cross-commenting

reviewers' comments are balanced

Significance

The study builds on previous work on USP7 and USP2 and while not a conceptual advance, adds to our understanding and knowledge of USP mechanisms. The in cellulo work of probing critical residues in USP1 for processing PCNA-Ub adds a new dimension.

However, the limitations of some of the experimental design, stability of mutants and choice of USPs (as outlined above) somewhat hamper the direct comparisons the study makes and previous work needs to be adequately represented (USP2). The work will be of interest to basic researchers and medicinal chemists in particular.

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Reply to the reviewers

We would like to thank all reviewers for their valuable and constructive comments, which helped us a lot to improve the manuscript.

The followings are point-by-point responses to the reviewers' comments:

Reviewer #1

Strong points

1. • The demonstration that pMAC-lncRNA accumulation depends upon Ema2 is convincing. This finding provides novel insights into the mechanism involved in TDSD in Tetrahymena. An important point that would be worth discussing is how ds pMAC-lncRNAs may pair with scnRNAs. An RNA helicase (Ema1?) may play an important role in this process.*

The requirement of Ema1 in the interaction between pMAC-lncRNAs and scnRNAs was reported previously by us (Aronica et al. 2008), which has been cited in this manuscript. Related to this point, we have added the following discussion in the revised manuscript (Page 10, Line 30):

“Although it is unclear whether lncRNAs are single or double stranded when Ema1 promotes the lncRNA-scnRNAs interaction, the less severe TDSD defect observed in the EMA2 KO cells compared to the EMA1 KO cells (Figure 3B) indicates that certain Ema1-dependent TDSD may be initiated by single-stranded lncRNAs or mRNAs that are transcribed independently of Ema2”.

• The manuscript is very well written. I noticed only a few typos (see minor comments below).*

The pointed typos have been corrected in the revised manuscript.

• The experiments are overall well done and well described. For non-Tetrahymena readers, it would be useful to clarify in the Results section (or in figure captions) whether the different KOs are in the MAC and/or also in the MIC*

We have indicated whether each KO line is somatic or germline (MAC+MIC) in the figure legends whenever these lines are referenced.

Responses for the suggestions:

Major concerns

1. • The search for Ema2 targets using mass spectrometry was performed in a wild-type SMT3 background. This implies that endogenous wild-type Smt3 may have competed with His-Smt3 for protein sumoylation. To what extent may this have been a problem for the enrichment of sumoylated proteins on nickel columns? This point is critical, since the authors discuss that other proteins involved in pMAC-lncRNA transcription may be modified by Ema2 (p. 12). They should repeat the experiment in an SMT3 KO, or use anti-Smt3 antibodies to enrich for sumoylated proteins. If this is not possible, they should at least provide additional explanations.*

We agree that a competition between His-tagged and non-tagged Smt3 lowered the sensitivity for the identification of SUMOylated proteins and we might miss some Ema2-dependent SUMOylated protein in the current study. However, we believe such protein, if any, is SUMOylated at very low level and not highly likely to be involved in the genome-wide orchestration of lncRNA transcription. We rather think that a critical Ema2-dependent SUMOylation event might be missed because some other residues of the same protein are SUMOylated by Ema2-independent manner and it was detected as a protein that was SUMOylated in both wild-type and EMA2 KO condition. Therefore, as was explained in Discussion, it is important to identify individual residues that are SUMOylated in Ema2-dependent manner. We are on our way to set up an experimental system that allows us to detect individual SUMOylated residues in Tetrahymena and we hope to analyze the functions of Ema2-dependent SUMOylated residues in future studies.

• In Figure 7A, the authors only show the localization of Spt6 in early exconjugants. Since Spt6 is essential for vegetative growth, one can expect that it also localizes in the vegetative MAC. Is it also found in the new developing MACs? The authors should complete the figure with additional panels showing vegetative cells and exconjugants at later stages (with their new MAC).*

The Spt6 is indeed localized in the MAC during vegetative growth and in the new MAC at late conjugation stage in the wild-type condition. We did not detect any anomaly of Spt6 localization in the EMA2 KO cells at least at the cytological level. The immunostaining results at the late conjugation stage are shown in Figure EV4 in the revised manuscript and mentioned in the revised text (Page 11, Line 13). The immunostaining results of vegetatively growing cells are only attached below because Spt6 localization at vegetative stage when EMA2 is not expressed is not highly relevant to this study.

• Along the same line, the authors show that the non sumoylatable Spt6 mutant does not inhibit pMAC-lncRNA synthesis. No scnRNA analysis is shown under these conditions: does TDSD still take place? It would also be interesting to check whether lncRNAs are still produced in the new MACs.*

The nonSUMOylatable Spt6 mutant (we now call SUMOylation defective Spt6 mutant according to one of the Reviewer 3’s suggestions) show lower mating, making us difficult to investigate its effect on TDSD. Because we did not detect Spt6 SUMOylation prior to mating, we believe the low mating phenotype of this mutant is not directly due to the loss of SUMOylation but instead some of the 77 K to R mutations affect the functions of Spt6 in efficient initiation of mating. Therefore, to precisely measure the effect of Ema2-dependent Spt6 SUMOylation, we need to identity exact Ema2-dependent SUMOylated residues of Spt6 to produce another nonSUMOylatable Spt6 mutant with fewer number of mutations that does not affect the mating process. Engaging in such work demands a substantial time investment, and we believe that the reviewers will concur that these experiments are components of our future projects.

Long dsRNA accumulation in the new MACs detected by the J2 antibody was comparable between wild-type and the SUMOylation-defective Spt6 mutant, suggesting that Spt6 SUMOylation is not necessary to produce lncRNAs in the new MAC. The data have been shown in Figure EV9 and mentioned in the main text (Page 12, Line 24) in the revised manuscript.

• The experiment shown in Figure 4C indicates that high-molecular weight (possibly sumoylated) proteins decrease to 50% in the EMA2 KO: this suggests that another sumoylation activity exists in the cell. A search for other putative SUMO E3 ligases is missing in this study.*

A few other putative SUMO E3 ligases indeed encoded in the Tetrahymena genome. Moreover, it is known that some substrates are SUMOylated without any SUMO E3 ligase in other eukaryotes. These points have been described in the revised text as follows (Page 8, Line 22):

“The remaining Ema2-independent SUMOylation is likely mediated by other SUMO E3 ligases (including the SP-RING containing proteins TTHERM_00227730, TTHERM_00442270 and TTHERM_00348490) and/or E3-independent SUMOylation (Sampson et al. 2001).”

We agree that exploring the roles of other SUMO E3 ligases in Tetrahymena would be important and interesting, and we believe it will be one of our future projects.

• Can one exclude that Spt6 is sumoylated at other stages (vegetative or during new MAC development) in an Ema2-independent manner?*

We have now included western blot observation of Spt6 at different life stages of wild-type cells as Figure EV2. We did not detect any slower-migrating Spt6 species in vegetative cells. This has been mentioned in the revised text as follows (Page 9, Line 17):

“Then, to examine the timing of the appearance of the slower migrating Spt6 species, we introduced the same Spt6-HA-expressing construct into a wild-type strain and Spt6-HA was analyzed by western blotting (Figure EV2). Consistent with the Ema2-dependent appearance of the slower migrating Spt6-HA, they were not detected in growing and starved vegetative wild-type cells (Figure EV2, Veg and 0 hpm, respectively) when Ema2 was not expressed (Figure 1). The slower migrating Spt6-HA was also detected at 8 hpm when the new MAC was already formed (Figure EV2, 8 hpm) suggesting that Spt6 is possibly SUMOylated also in the new MAC.”

• In which nucleus does coding transcription take place between 4.5 and 6 hpm? Can we exclude that the weaker association of Rpb3 with chromatin in the EMA2 KO cross also impairs coding transcription?*

Coding transcription takes place in the parental MAC at 4.5 and 6 hpm in wild-type cells. Also, because EMA2 KO cells did not show obvious defect in the progression of the conjugation processes, any essential mRNA transcriptions for these processes must occur even in the absence of Ema2. These points prompted us to add the following discussion in the Discussion section (Page 13, Line 14):

“Moreover, as EMA2 KO cells did not significantly impede the progression of conjugation processes, any essential mRNA transcriptions for these processes must take place in the parental MAC during conjugation even in the absence of Ema2. Therefore, the observed loss of the majority of Spt6 and RNAPII from chromatin in the absence of Ema2 (Figure 7B) must be a temporal event during the mid-conjugation stage. This suggest that RNAPII might be specifically engaged in pMAC-lncRNA transcription at this particular time window in wild-type cells.”

Minor concerns

• The authors do not explain how they found Ema2. More information could be useful.*

Ema2 was identified as a protein involved in DNA elimination during our systematic genetic investigation of genes exclusively expressed during conjugation. This has been mentioned in the revised manuscript (Page 6, Lines 4-5).

• In Figures 2B and 3B: the statistical significance of the differences observed for the IES retention index and small RNA amounts should be evaluated using appropriate tests.*

The result shown in Figure 2B (IES retention analysis) has been tested by Welch two-sample t-test and outcomes have been shown in the revised Figure 2B.

The result shown in Figure 3B (small RNA seq) has been tested by Wilcoxon rank sum test and outcomes have been shown in the revised Figure 3B.

Figure 3 caption: define acronym "IQR"

The definition of IQR (the interquartile range) has now been mentioned in the figure legend in the revised manuscript.

Figure 5 caption (line 4): there may be a word missing ("from conjugating cells?")

We have corrected the sentence by adding “cells” after “from conjugating” in Page30-Line 34.

Figure 8C: what does the asterisk stand for?

We realized that the asterisk is not necessary in the figure and thus it have been removed in the revised figure.

• p. 10 (bottom): an "o" is missing in "Aronica et al 2008"*

We have corrected the error.

• p.13 (2nd line): remove final "s" in "mimic"*

We have corrected the error.

• p. 14: change "were" to "was" in "the production of the EMA2 KO strains was described previously"*

We have corrected the error.

• p. 14: remove capital letters in "Gorovsky"*

We have corrected the error.

• p. 15 (Viability test for progeny): what does "6-mp" stand for?*

It is 6-methylpurine. We have added this information to the revised manuscript.

• p. 17 (end of first paragraph): change "contracts" to "constructs"*

We have corrected the error.

• p. 17 (2nd line of last paragraph): change "was" to "were " in "EMA2 cells containing the BP6MB1-His-SMT3 construct were mated..."*

We have corrected the error.

• p. 19 (3rd line of 2nd paragraph"): "spined own" should be replaced by "spinned down"*

We have corrected the error.

Reviewer #2

Major comments

From Figure 4C, the authors conclude that "Ema2 is the major SUMO E3 ligase during the mid-conjugation stages.", yet in Figure 5 show that only Spt6-SUMOylation is affected in Ema2 mutants. These conclusions seem inconsistent and should be reconciled as it is a central point in the paper. E.g. is Spt6 protein abundance based on the MS data supporting that this protein constitutes a major fraction of the (high mol weight) SUMOylated proteins? Of note, the discussion contains a very balanced discussion of this but the current description in the results should be improved.

Some of the proteins detected from both the wild-type and EMA2 KO conditions were possibly poly-histidine-containing proteins that bound intrinsically to the nickel-NTA beads or proteins unpacifically bound to some of the bead material. Taking these possibilities into account, a control experiment with wild-type cells not expressing His-Smt3 in the same condition is now included in the study and any proteins that were also identified in this experiment with log2 LFQ score above 25 were excluded in the new Figure 5A. We also removed any identified proteins containing more than 6 consecutive histidine residues from the plot. After these filtering processes, it is now clear that Spt6 is the major SUMOylated protein detected in the wild-type (with His-Smt3) condition and the LFQ intensities of other proteins (except Smt3) were ~16 or more hold less than that of Spt6. Together with the fact that the molecular weight range of most of the SUMOylated proteins fits very well to that of SUMOylated Spt6, we are now more confident to conclude that Ema2 is the major SUMO E3 ligase during the mid-conjugation stages and Spt6 is the major target of Ema2. We have modified the corresponding figure and texts to explain this filtering and the outcomes (Page 9, Lines 2-9).

The western blots carried out for the chromatin fraction and presented in Figures 7B, 7C, and 8B have variable levels of histone H3 which serves as a fractionation control, thus indicating some experimental variability. To support the quantitative conclusions, the authors should indicate how many times were these fractionation experiments repeated and should also provide experimental replicate data in the supplements. These data are important to firmly support the quantitative conclusions the authors currently draw from the experiments.

Each of these fractionation experiments was done three times and gave comparative results. The replicate data have been shown in Figures EV5, EV6 and EV8.

Minor comments

Page 3: "Because small RNA-producing loci are also small RNA targets ... " It should be specified that this is the case specifically for the studied system as it is not generally the case for small RNA loci. Overall, this third intro paragraph is a bit hard to read and might be improved by first introducing Tetrahymena and its distinctive cellular biology and then moving to the observation that small RNA source and target loci are separated in this ciliate.

We have modified the description to “Because small RNA-producing loci are also small RNA targets in most of the studied small RNA-directed heterochromatin formation processes, it poses a challenge to separately investigate lncRNA transcription for small RNA biogenesis and that for small RNA-dependent recruitment of downstream effectors in these processes.” (Page 3, Lines 24-27). We believe this has improved overall readability of the paragraph.

Figure annotation and readability: The manuscript and figure labels are rich in abbreviation (and sometimes even abbreviations of abbreviations, e.g. na = new MAC = new macronucleus).

We agree that there are many abbreviations in this manuscript but we believe most of them are necessary to keep the text and figures concise. To increase readability, we have spelled out all “abbreviations of abbreviations” when they appear the first time in the text. In fact, “na” was used not as an abbreviation but as a mark in the figures. We have modified the corresponding figure legends to make this point clearer. Also, to make the abbreviation “TDSD” more generalizable, we modified the manuscript to used it as “target-directed small RNA degradation” instead of “target-directed scnRNA degradation”.

Also Figures 4, 5 - the addition of the protein name after α-HA, -GST or -His would make the interpretation of blots easier.

Because anti-GST is detecting both GST alone and GST-Ema2, in Figure 4B, we had indicated the names of the proteins next to the blots. These might be less visible due to the busy arrangement of the panels in the previous manuscript. We have made extra space to make these labeles more visible. For Figure 4C, Figure 5B and Figure 5C, we have followed the reviewer’s suggestion and changed the labels to show the proteins detected.

In Figure 4, it is unclear how the protein quantification was made (leading the the "reduced to ~50% in the EMA2 KO" statement). Please clarify.

The total signal intensities of HA-Smt3 in triplicated experiments were analyzed by western blotting and quantified. We now have included the data as a part of Figure 4C in the revised manuscript and explained the quantification procedure in the figure lagend and Materials and Method.

In some places, the current manuscript refers to implicit knowledge that some non-specialists may not take for granted. For example, dsRNA formation is important for scnRNA production, motivating detection using the J2 antibody. Editing for non-expert readability could help reach a broader readership.

In this study, we used the J2 antibody not because dsRNA formation is important for the scnRNA production but because it allows us to cytologically detect lncRNAs in the parental MAC. We have modified the related sentence (Page 10, Lines 17-20) in the revised manuscript to improve readability. We have also added a discussion about single vs double-strand nature of lncRNA in the parental MAC (Page 10, Lines 30-34) as mentioned in our reply for the first comment of Reviewer 1.

• Also, on Page 7, bottom, it would be helpful to briefly explain to the reader how SUMOylation works to motivate the conclusion from the Ubc9 interaction.*

We have added a brief explanation for the actions of E1 and E2 enzymes in SUMOylation in the revised text (Page 8, Line 6-7).

**Referees cross-commenting**

My report (rev #2) closely aligns with that of rev #3. While all reports are positive, rev #1 suggests several lines of additional work, such as the characterization of lncRNA expression in the new MAC (major concern 3) and a search for other SUMO E3 ligase (major concern 4). While several interesting ideas are brought up here, I see such added investigations as non-essential for the current paper. I would encourage to focus revision work on the substantiation of the already included experiments.

The lncRNA expression in the new MAC in the C-KR mutant has been analyzed and included in Figure EV9. We have included some discussion regarding other SUMO E3 ligases and reserved their functional investigations for our future studies as Reviewer #2 and #3 suggested.

Reviewer #3

It is not entirely clear why the transcripts of small RNA targets are necessarily non-coding. labelling them as nascent would be sufficient in my opinion

In the described examples of small RNA-directed heterochromatin formation processes in the various eukaryotes in Introduction, the targets of small RNAs are indeed lncRNAs. Therefore, to separately discuss small RNA targets from mRNA, we keep using the term lncRNA for the former.

It is unclear whether mRNAs can also be small RNA targets in the Tetrahymena DNA elimination process. We have added the following sentence in Introduction (Page 4, Line 30):

“Although mRNAs are transcribed in the parental MAC, it remains unclear if they also can induce TDSD and how mRNAs and pMAC-lncRNAs can be transcribed from overlapping locations.”

Nonetheless, because EMA2 KO did not show detectable defect in the progression of conjugation processes, we believe any essential mRNA transcriptions for these processes occur in the parental MAC in EMA2 KO (which are now mentioned in Discussion [Page 13, Lines 14-20] for replying to one of Reviewer 1’s suggestions) and thus believe that the defects of EMA2 KO observed/discussed in this manuscript are due to the loss of lncRNAs. Therefore, we believe using lncRNA to label the RNAs transcribed by Ema2-directed SUMOylation is valid.

the nomenclature of methylated H3K9 might need some adjustment. Consider the abbreviation H3K9me2/3 instead of H3K9me

We followed the suggestion and H3K9me2/3 or H3K9m3 have been used in the revised manuscript.

it would be desirable if the authors could cross reference to the Paramecium field where possible given that this is a second, powerful study system in small RNA-mediated genome elimination.

We have extensively modified Introduction to describe the small RNA-directed genome rearrangement process of Tetrahymena and Paramecium as much as possible in parallel.

Main text:

"The conjugation-specific expression and the localization switch from the parental to the new MAC are reminiscent of the factors involved in DNA elimination (Mochizuki et al, 2002; Coyne et al, 1999; Kataoka & Mochizuki, 2015; Liu et al, 2007; Yao et al, 2007)."

please name these other factors here.

We have added “such as the Piwi protein Twi1, which is loaded by scnRNAs, and PRC2 (Mochizuki et al. 2002; Liu et al. 2007; Noto et al. 2010)” at the end of this sentence (Page 6, Line 13).

Figure 5A: what is the author's interpretation of the finding that most identified proteins remain unchanged? are these Ema2 independent SUMOylated proteins or are these background proteins that are not SUMOylated?

As mentioned in our reply to Reviewer 2, some of the proteins detected from both WT and EMA2 KO were possibly poly-histidine-containing proteins that bound intrinsically to the nickel-NTA beads without His-Smt3 conjugation or proteins unpacifically bound to some of the bead material. Taking these possibilities into account, a control experiment with wild-type cells not expressing His-Smt3 in the same condition has now been included and any proteins that were also identified in this experiment with log2 LFQ score above 25 were excluded in the new Figure 5A. We also removed any proteins containing more than 6 consecutive histidine residues from the plot. After these filtering processes, it is now clear that Spt6 is the major SUMOylated protein detected in the wild-type (with His-Smt3 expression) condition and the LFQ intensities of other proteins (except Smt3) were ~16 or more hold less than that of Spt6. We have modified the corresponding figure and texts (Page 9, Lines 2-9) to explain this filtering procedure and the outcomes.

Even after this filtering, many proteins were identified similarly between wild-type and EMA2 KO conditions. As mentioned in our reply for one of the comments by Reviewer 1, these are most likely Ema2-independent SUMOylated proteins either mediated by another SUMO E3 ligase or by E3-independent SUMOylation. We have added these points in the revised manuscript (Page 8, Lines 22-25).

"However, the cells rescued by HA-SPT6N-KR and HA-SPT6-M-KR showed severe defects in meiotic progression and mating initiation, respectively, making their SUMOylation status during conjugation uninvestigable." Why can't you investigate the SUMOylation capacity of these variants in wildtype cells?

The suggested experiment is probably a valid way to investigate the SUMOylation of HA-Spt6N-KR and HA-Spt6-M-KR. However, in such experimental setting, SUMOylation of Spt6 might be blocked not by loss of SUMOylation sites but by competition between the wild-type and the mutant Spt6. Moreover, even if one of them is proved to be unSUMOylatable (we now decided to call it SUMOylation-defective mutant [please see below]), we cannot examine its effect on lncRNA transcription if it has to be co-expressed with the wild-type Spt6. Therefore, we decided not to further examine the SUMOylation of the two mutants.

"Therefore, Spt6-C-KR is an unSUMOylatable Spt6 mutant." How sure can you be about this given the dynamic range of the detection in this experiment?

Whatever the dynamic range is, it is not possible to conclude that there is zero SUMOylation on Spt6-C-KR in the experimental setting we used. So, we have decided to call it a “SUMOylation-defective mutant” and modified the corresponding sentence as follows (Page 12, Line 18):

“Therefore, Spt6-C-KR represents a SUMOylation-defective Spt6 mutant, exhibiting at least a reduced level of SUMOylation compared to Spt6 in the absence of Ema2 (compare Figure 8B and Figure 5B).”

Figure 1A: label the plot to make it more accessible. Axis labels are missing.

Axis labels and explanations for the stages have been added in the revised Figure 1A.

Figure 3A: can you speculate about the higher molecular weight signal in the northern blot that appears in the later time-points and that seems to be partially dependent on Ema2?

The appearance of these higher molecular weight signals correlates with the presence or absence of lncRNAs detected by the J2 antibody at 4.5 hpm (Figure 6B). However, their presence in EMA2 KO cells at 6 hpm, the time point before the development of the new MAC, does not fit well to the absence of J2 staining in the parental MAC in EMA2 KO cells. Therefore, we currently have no clear idea for the identity of the higher molecular weight signals.

Figure 3B: why are the scanRNA levels at 3h already so different between WT and mutant cells? Lane 1 versus lanes 3 and 5?

The following sentence has been added in the revised manuscript (Page 7, Line 20):

“Because TDSD takes place concurrently with the scnRNA production (Schoeberl et al. 2012), the increased abundance of MDS-complementary scnRNAs at 3 hpm in the EMA2 KO cells compared to the wild-type cells can also be attributed to the necessity of Ema2 in TDSD.”

Figure 5: could you comment on the weak Smt3 signal that remains for Spt6 in the Ema2 KO conditions. Is this due to other SUMO-ligases or is the Ema2 KO not a full loss of function condition?

The following sentence has been added in the revised manuscript (Page 9, Line 31):

“The remaining SUMOylation observed on Spt6 in the absence of Ema2 is likely facilitated by other SUMO E3 ligases and/or E3-independent SUMOylation, as discussed earlier for the other instances of Ema2-independent SUMOylations.”

Figure 6C: are the many arrowheads not confusing? Are they needed?

We have removed most of the arrowheads from the figure and marked only the parental MACs. In addition, we have used the same labeling for all immunofluorescent staining figures.

Figure 8A: the cartoon depicting different colors for the various Lysine residues is not immediately clear to the reader. Try to make this more accessible.

We have modified the drawing to make the markings for the mutated lysine residues more visible in the revised figure.

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Referee #3

Evidence, reproducibility and clarity

This study presents novel data and evidence for a critical involvement of protein SUMOylation in the process of noncoding RNA transcription during the process of conjugation in Tetrahymena. Loss of the critical SUMO E3 Ligase Ema2 leads to a loss of ncRNA transcription in the parental macronucleus, ultimately leading to the lack of scanRNA traget molecules on chromatin, and as a result a loss of heterochromatin formation as well as defective target-dependent small RNA degradation. The paper is very well written, the figures are mostly a treat, the data is well discussed and placed in context, and the claims are supported by robust data. The authors went a long way to nail the relevant target protein of Ema2 and provide on the one side compelling evidence that the transcription elongation factor Spt6 is a bona fide SUMOylation substrate for Ema2. Quite surprisingly, however, a mutant Spt6 construct that shows no sign of SUMOylation in cells does rescue the Spt6 loss of function phenotype. While this puts the relevance of Spt6 SUMOylation in the process slightly into question, the authors provide a compelling discussion as to how SUMOylation still might be essential for proper Spt6 function in stimulating ncRNA transcription. All in all, this is a great paper that reports important data for the ciliate community, for the transcription community, and the larger small RNA community.

the following comments hopefully help to further improve the paper. I do not recommend any additional experiments.

Introduction:

• It is not entirely clear why the transcripts of small RNA targets are necessarily non-coding. labelling them as nascent would be sufficient in my opinion
• the nomenclature of methylated H3K9 might need some adjustment. Consider the abbreviation H3K9me2/3 instead of H3K9me
• it would be desirable if the authors could cross reference to the Paramecium field where possible given that this is a second, powerful study system in small RNA-mediated genome elimination.

Main text:

• "The conjugation-specific expression and the localization switch from the parental to the new MAC are reminiscent of the factors involved in DNA elimination (Mochizuki et al, 2002; Coyne et al, 1999; Kataoka & Mochizuki, 2015; Liu et al, 2007; Yao et al, 2007)." please name these other factors here.
• Figure 5A: what is the author's interpretation of the finding that most identified proteins remain unchanged? are these Ema2 independent SUMOylated proteins or are these background proteins that are not SUMOylated?
• "However, the cells rescued by HA-SPT6N-KR and HA-SPT6-M-KR showed severe defects in meiotic progression and mating initiation, respectively, making their SUMOylation status during conjugation uninvestigable." Why can't you investigate the SUMOylation capacity of these variants in wildtype cells?
• "Therefore, Spt6-C-KR is an unSUMOylatable Spt6 mutant." How sure can you be about this given the dynamic range of the detection in this experiment?
• Figure 1A: label the plot to make it more accessible. Axis labels are missing.
• Figure 3A: can you speculate about the higher molecular weight signal in the northern blot that appears in the later time-points and that seems to be partially dependent on Ema2?
• Figure 3B: why are the scanRNA levels at 3h already so different between WT and mutant cells? Lane 1 versus lanes 3 and 5?
• Figure 5: could you comment on the weak Smt3 signal that remains for Spt6 in the Ema2 KO conditions. Is this due to other SUMO-ligases or is the Ema2 KO not a full loss of function condition?
• Figure 6C: are the many arrowheads not confusing? Are they needed?
• Figure 8A: the cartoon depicting different colors for the various Lysine residues is not immediately clear to the reader. Try to make this more accessible.

Referees cross-commenting

I agree with the comment from reviewer #2 that additional experiments are not required at this stage. Several constructive points have been raised by all three reviewers that will strengthen this already very mature work.

Significance

This is a very strong experimental study that reports very interesting findings that do go beyond the ciliate community. Spt6 is a major transcription elongation factor and understanding the various functions of this factor by studying in vivo processes is highly important. The paper opens up a new research niche. The findings are very well presented and the discussion does a great job in putting the somewhat surprising results n the non SUMOylatable mutant into context.

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Referee #2

Evidence, reproducibility and clarity

Summary

During conjugation (the sexual reproduction stage in the Tetrahymena ciliates), programmed DNA elimination guided by small RNAs termed scnRNAs results in the specific elimination of many repetitive sequences. This specificity relies on the target-directed scan RNA degradation (TDSD) pathway where scnRNAs matching the active parental macronucleus are eliminated.

The manuscript by Shehzada et al. identifies a novel player in Tetrahymena TDSD: SUMO E3 ligase Ema2. The authors show by northen and small RNA-seq that Ema2 is required for TDSD. Furthermore, the paper describes how Ema2 post-translationally modifies the transcription elongation factor Spt6 by SUMOylation and that Ema2 is required to produce long double-stranded scnRNA precursor transcripts from the parental macronucleus, possibly via its modification of Spt6.

Major comments

From Figure 4C, the authors conclude that "Ema2 is the major SUMO E3 ligase during the mid-conjugation stages.", yet in Figure 5 show that only Spt6-SUMOylation is affected in Ema2 mutants. These conclusions seem inconsistent and should be reconciled as it is a central point in the paper. E.g. is Spt6 protein abundance based on the MS data supporting that this protein constitutes a major fraction of the (high mol weight) SUMOylated proteins? Of note, the discussion contains a very balanced discussion of this but the current description in the results should be improved.

The western blots carried out for the chromatin fraction and presented in Figures 7B, 7C, and 8B have variable levels of histone H3 which serves as a fractionation control, thus indicating some experimental variability. To support the quantitative conclusions, the authors should indicate how many times were these fractionation experiments repeated and should also provide experimental replicate data in the supplements. These data are important to firmly support the quantitative conclusions the authors currently draw from the experiments.

Minor comments

Page 3: "Because small RNA-producing loci are also small RNA targets ... " It should be specified that this is the case specifically for the studied system as it is not generally the case for small RNA loci. Overall, this third intro paragraph is a bit hard to read and might be improved by first introducing Tetrahymena and its distinctive cellular biology and then moving to the observation that small RNA source and target loci are separated in this ciliate

Figure annotation and readability: The manuscript and figure labels are rich in abbreviation (and sometimes even abbreviations of abbreviations, e.g. na = new MAC = new macronucleus). Also Figures 4, 5 - the addition of the protein name after α-HA, -GST or -His would make the interpretation of blots easier.

In Figure 4, it is unclear how the protein quantification was made (leading the the "reduced to ~50% in the EMA2 KO" statement). Please clarify.

In some places, the current manuscript refers to implicit knowledge that some non-specialists may not take for granted. For example, dsRNA formation is important for scnRNA production, motivating detection using the J2 antibody. Editing for non-expert readability could help reach a broader readership. Also, on Page 7, bottom, it would be helpful to briefly explain to the reader how SUMOylation works to motivate the conclusion from the Ubc9 interaction.

Referees cross-commenting

My report (rev #2) closely aligns with that of rev #3. While all reports are positive, rev #1 suggests several lines of additional work, such as the characterization of lncRNA expression in the new MAC (major concern 3) and a search for other SUMO E3 ligase (major concern 4). While several interesting ideas are brought up here, I see such added investigations as non-essential for the current paper. I would encourage to focus revision work on the substantiation of the already included experiments.

Significance

Overall, the presented work is well-structured, well-executed experimentally and carefully interpreted. The manuscript in most places (see minor comments) is clear and easy to follow for the expected broad readership in the fundamental biology of small RNAs and programmed DNA elimination. The main weakness of the paper is the proposed mechanistic connection from the Ema2 KO phenotype to Spt6 SUMOylation function in TDSD. The authors, however, have a very balanced description of this aspect in the discussion. In addition, there are some important technical questions to address regarding protein quantification by western blotting.

The work presented elucidates the crucial role of SUMO E3 ligase Ema2 in the TDSD pathway for scnRNAs in Tetrahymena. This advance is significant as TDSD is the foundation for the specificity of programmed DNA elimination in Tetrahymena and as it is currently not well understood mechanistically.

This work will be of interest to a broad readership for two reasons: (i) it advances our understanding of programmed DNA elimination in Tetrahymena, which is a major mechanistic model system for eukaryotic programmed DNA elimination. And (ii) it makes mechanistic connections to small RNA-mediated transcriptional silencing in yeast and fruit flies with possible general implications for these processes across eukaryotes.

In sum, the paper presents interesting new findings about small RNA biology and DNA elimination and was a pleasure to read.

The reviewers' declared field of expertise: small RNAs, chromatin, transcription

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Referee #1

Evidence, reproducibility and clarity

The authors convincingly show that Ema2, a conjugation-specific SUMO E3 ligase, localizes in the parental MAC during early conjugation stages, then moves to the new MAC. Using somatic EMA2 KO strains, they show that Ema2 is necessary for IES elimination and the recovery of viable progeny. They demonstrate that MAC scnRNAs do not disappear in an EMA2 KO and conclude that Ema2 is required for TDSD. They also show that ds lncRNA amounts in the parental MAC drop to background levels in an EMA2 KO, while they remain similar to WT in meiotic MICs or the new MACs.

They also present evidence supporting that the transcription factor Spt6 is one of the targets of Ema2-mediated sumoylation. Spt6 is found in the parental MAC of conjugating cells, regardless of Ema2. However, Ema2 is crucial for the stable chromatin association of both Spt6 and Rpb3 (a subunit of RNA polymerase II). Unexpectedly, a non-sumoylatable Spt6 mutant is able to complement a SPT6 KO, since it maintains the synthesis of lncRNA in the parental MAC. Nonetheless, this mutant strongly impairs new MAC development and IES elimination. As a whole, the role of Spt6 sumoylation in programmed DNA elimination is not clearly established, and it probably affects another step than pMAC-lncRNA synthesis.

Strong points:

1. The demonstration that pMAC-lncRNA accumulation depends upon Ema2 is convincing. This finding provides novel insights into the mechanism involved in TDSD in Tetrahymena. An important point that would be worth discussing is how ds pMAC-lncRNAs may pair with scnRNAs. An RNA helicase (Ema1?) may play an important role in this process.
2. The manuscript is very well written. I noticed only a few typos (see minor comments below).
3. The experiments are overall well done and well described. For non-Tetrahymena readers, it would be useful to clarify in the Results section (or in figure captions) whether the different KOs are in the MAC and/or also in the MIC

Major concerns:

1. The search for Ema2 targets using mass spectrometry was performed in a wild-type SMT3 background. This implies that endogenous wild-type Smt3 may have competed with His-Smt3 for protein sumoylation. To what extent may this have been a problem for the enrichment of sumoylated proteins on nickel columns? This point is critical, since the authors discuss that other proteins involved in pMAC-lncRNA transcription may be modified by Ema2 (p. 12). They should repeat the experiment in an SMT3 KO, or use anti-Smt3 antibodies to enrich for sumoylated proteins. If this is not possible, they should at least provide additional explanations.
2. In Figure 7A, the authors only show the localization of Spt6 in early exconjugants. Since Spt6 is essential for vegetative growth, one can expect that it also localizes in the vegetative MAC. Is it also found in the new developing MACs? The authors should complete the figure with additional panels showing vegetative cells and exconjugants at later stages (with their new MAC).
3. Along the same line, the authors show that the non sumoylatable Spt6 mutant does not inhibit pMAC-lncRNA synthesis. No scnRNA analysis is shown under these conditions: does TDSD still take place? It would also be interesting to check whether lncRNAs are still produced in the new MACs.
4. The experiment shown in Figure 4C indicates that high-molecular weight (possibly sumoylated) proteins decrease to 50% in the EMA2 KO: this suggests that another sumoylation activity exists in the cell. A search for other putative SUMO E3 ligases is missing in this study.
5. Can one exclude that Spt6 is sumoylated at other stages (vegetative or during new MAC development) in an Ema2-independent manner?
6. In which nucleus does coding transcription take place between 4.5 and 6 hpm? Can we exclude that the weaker association of Rpb3 with chromatin in the EMA2 KO cross also impairs coding transcription?

Minor concerns

1. The authors do not explain how they found Ema2. More information could be useful.
2. In Figures 2B and 3B: the statistical significance of the differences observed for the IES retention index and small RNA amounts should be evaluated using appropriate tests.

Figure 3 caption: define acronym "IQR"

Figure 5 caption (line 4): there may be a word missing ("from conjugating cells?")

Figure 8C: what does the asterisk stand for?

p. 10 (bottom): an "o" is missing in "Aronica et al 2008"

p. 13 (2nd line): remove final "s" in "mimic"

p. 14: change "were" to "was" in "the production of the EMA2 KO strains was described previously"

p. 14: remove capital letters in "Gorovsky"

p. 15 ({section sign} Viability test for progeny): what does "6-mp" stand for?

p. 17 (end of first paragraph): change "contracts" to "constructs"

p. 17 (2nd line of last paragraph): change "was" to "were " in "EMA2 cells containing the BP6MB1-His-SMT3 construct were mated..."

p. 19 (3rd line of 2nd paragraph"): "spined own" should be replaced by "spinned down"

Significance

In this manuscript Shehzada et al report important novel findings on the molecular mechanisms involved in RNA-mediated control of programmed DNA elimination in the ciliate Tetrahymena thermophila. In this organism, non-coding transcription takes place in distinct nuclei and produces double-stranded (ds) long non-coding RNAs (lncRNAs) at different stages during conjugation. First, bidirectional transcription in the MIC during meiosis produces ds lncRNAs that are processed to short scnRNAs. Second, lncRNAs from the parental MAC (pMAC-lncRNAs) are thought to drive the degradation of scnRNAs homologous to parental MAC DNA, in a process called TDSD (target-directed scnRNA degradation). Third, the remaining MIC-specific scnRNAs are imported to the new MACs, where their pair with lncRNAs and drive heterochromatin formation and DNA elimination.

The present study focuses on TDSD, a process that has been poorly described at the molecular level. The strongest part of the work is the demonstration that the SUMO E3 ligase Ema2 is necessary for the production of pMAC-lncRNAs, which in turn impairs the selective degradation of MAC scnRNAs. A less convincing part is the identification of Ema2 targets. The authors identify Spt6 as one of the Ema2-dependent sumoylated proteins. However, they show that Spt6 sumoylation is not necessary for pMAC-lncRNA transcription.

In principle, the results presented in this manuscript should be of broad interest for the scientific communities working on non-coding RNA biology and the epigenetic control of programmed genome rearrangements.

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Reply to the reviewers

Response to Referees Letter

We thank the reviewers for their constructive comments and their positive comments that this study provides insights into the non-canonical roles of Bcl-xL in cancer and may lead to therapeutic approaches to repress metastatic capacity. We have carefully read their comments and have extensively revised the manuscript accordingly. The specific points made by each reviewer are addressed below in blue color.

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Response to Reviewer #1:

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

Summary In this study the authors build on their previous work that Bcl-xL has a role in metastasis promotion independent of it's function in the mitochondrial apoptotic pathway. They show that Bcl-xL can be found in the nucleus of some human breast cancer cells and through a mass spec approach show that CtBP2 promotes the nuclear translocation of Bcl-xL. Using various knockdown/knockout methods they show that reduced levels of CtBP2 reduces metastasis, because of loss of Bcl-xL translocation to the nucleus. The authors map this interaction and show that this interaction modulates metastasis.

Major comments * Figure 1 - a more comprehsive analysis of nuclear Bcl-xL should be conducted. The data presented only shows 3 different samples, with no quantification. Perhaps the authors could stain a breast cancer TMA or similar?

__Response: __We performed breast cancer TMA staining experiment as suggested. This experiment provides further support to our conclusion. We have included the following information in the revised manuscript.

“We further evaluated human breast specimens in tissue microarrays (TMAs), consisting of 25 non-neoplastic breast tissues, 150 primary breast cancer, 55 lymph node metastases, and 99 metastatic breast cancer at various distant sites, for the expression and localization of Bcl-xL by immunohistochemistry. Compared to normal breast tissues, the intensity of Bcl-xL was significantly higher in breast cancer, including primary tumors, lymph node (LN) metastases, and distant metastases (Table 1a and 1b). The proportion of positive perinuclear/nuclear Bcl-xL cases was significantly increased in human breast cancer tissues compared to normal breast tissues (Table 1c and Figure 1d), and it showed an increasing trend towards metastases (Table 1d, p =0.004).”

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* Figure 2 - could the authors show a graph with a representation of the mass spectrometry data, so the reader can get a sense of how many proteins were found to be associated with Bcl-xL?

__Response: __As suggested, we have included the mass spectrometry data in Supplemental Table 1. Forty proteins were commonly immunoprecipitated by anti-HA magnetic beads from all three cell lines overexpressing HA-tagged wt Bcl-xL and two Bcl-xL mutants but not from the parental cells overexpressing the control vector.

* Have the authors tried any other ways to verify the interaction between Bcl-xL and CtBP2? For instance, do they co-localise when imaged? Also, can the reverse IP be performed?

__Response: __We have verified the interaction between Bcl-xL and CtBP2 by several methods, including IP, reverse IP, and co-immunostaining. Please find HA-Bcl-xL IP and Western for endogenous CtBP2 (Figure 2a), co-immunostaining of endogenous Bcl-xL and CtBP2-V5 (Figure 2b and 2c), co-immunostaining of endogenous Bcl-xL and endogenous CtBP2 (Figure 4e), HA-Bcl-xL IP and Western for seven different constructs of V5 tagged CtBP2 (Figure 5b and 5c), and V5-CtBP2 IP and Western for seven different constructs of Myc tagged Bcl-xL (Figure 6b).

* Figure 2C - the authors claim that this data shows that Bcl-xL nuclear translocation is reduced in cells with reduced levels of CtBP2 - however, although they quantify this I simply do not see it from the images presented. I do not think this data supports the conclusion that knockdown of CtBP2 reduces Bcl-xL translocation to the nucleus. Furthermore, this data is only shown with overexpressed Bcl-xL - have the authors tried with endogenous staining of Bcl-xL?

Response: To assist Reviewer #1’s visualization, below are some marked RFP+ cells that responded to Dox-inducible shRNA expression from Figure 2e. Please note that these cells were not sorted by dsRed so that they gave us a unique opportunity to determine whether the knockdown of CtBP2 affected Bcl-xL nuclear localization by comparing subcellular localization of HA-Bcl-xL in the dsRed-positive cells and the neighboring dsRed-negative cells in the same images. The nuclear-to-cytosol ratio of HA-Bcl-xL was reduced in the dsRed-positive shCtBP2 cells compared to the dsRed-negative cells in both shCtBP2 #2260 and #2403 cultures on dox, not in shRLuc #713 control cells on dox.

In addition, we have performed endogenous staining of Bcl-xL and found that CtBP2 knockout reduced the nuclear to cytosol ratio of endogenous Bcl-xL (Figure 4f).

* Figure 2e-f - again these data are in cells with overexpressed Bcl-xL - does the same effect on invasion happen when only CtBP2 levels are reduced, without overexpression of Bcl-xL? What happens when Bcl-xL is knocked down? Also, doxycycline has been shown to affect mitochondrial function, which might confound this data - perhaps another way to knockdown CtBP2 (e.g. CRISPR which is used later in the study) would rule this out

Response: First, we have previously reported that CtBP2 knockdown reduced migration in cells without overexpression of Bcl-xL (Paliwal et al., 2007), and others have shown that siRNA knockdown of Bcl-xL reduces migration and invasion (Trisciuoglio et al., 2017).

Second, to control any effect of doxycycline, we have included the doxycycline-fed control cells that express doxycycline-inducible shRNA against Renilla Luciferase (shRLuc #713) in revised Figure 2g and 2h (original Figure 2e and 2f).

Third, the novelty of this study is that the discovery that Bcl-xL and CtBP2 interact with each other to promote metastasis. Our study showed that CtBP2 controls Bcl-xL in two ways: nuclear translocation and transcription. Because we found that knockout CtBP2 reduced transcription of endogenous Bcl-xL (Figure 4a-c), it will make the interpretation of the migration effect difficult. Using cells overexpressing HA-Bcl-xL, whose transcription is not regulated by CtBP2, we can evaluate whether the invasion effect of HA-Bcl-xL is mediated by CtBP2 when CtBP2 is knocked down. While overexpression of Bcl-xL promotes invasion (Choi et al., 2016), knockdown of CtBP2 can reverse the effect (Figure 2g).

* Figure 3c - these blots are not labelled, but ideally this would be shown with endogenous Bcl-xL, rather that just the overexpressed HA-Bcl-xL. However these data are more convincing than the images presented in Figure 2c

__Response: __We apologize for the missing labels in these blots of Figure 3c when we merged the graphs. We have now added them back.

* Figure 4 - the authors use CRISPR to knockout CtBP2 - logically this data would go with the shRNA data shown before, as it seems to just repeat what has already been shown?

__Response: __In Figure 4, we examined the effect of CtBP2 knockout on the endogenous Bcl-xL. We were pleased to see that CtBP2 knockout reduced the nuclear-to-cytosol ratio of endogenous Bcl-xL. Moreover, we observed that CtBP2 knockout reduced transcription of Bcl-xL. These knockout data (Figure 4) were logically presented after the knockdown data (Figure 2 and 3).

* Figure 4d - what does "SN" refer to? There is no loading control for this part of the fractionation - I assume this is supernatant? If so, why is there no loading control for this (same applies to figure 3c). Also, why are these not on the same blot? If CtBP2 knockdown reduces Bcl-xL mRNA level, does it also reduce Bcl-xL protein levels? We should be able to tell this from the blots in figure 4d, but since they are on different membranes this is impossible to deduce.

__Response: __We apologize for the missing information. We have added “SN: soluble nuclear fraction” in the figure legend of Figure 4d and re-run all the samples on the same blot. No detection of cytoplasmic proteins and chromatin-bound proteins in the soluble nuclear fraction suggested good fractionation as described (Méndez and Stillman, 2000, PMID: 11046155). CtBP2 knockout indeed reduced Bcl-xL protein levels, as shown in Figure 4a.

* Figure 5c - molecular weight markers should be included here.

__Response: __We apologize for the missing labels of the molecular weight markers, and we have added them in the revision.

* Figure 7a - the text says that MM102 treatment "significantly reduced" H3K4me3 levels - where is the quantification of this?

__Response: __We appreciate the suggestion, and we have now added the quantification in Figure 7a.

Minor comments * Some of the figures are not properly labelled * Some of the data are presented in an awkward manner - the authors should consider re-structuring either the manuscript or the figures so there is less "jumping around"

__Response: __We apologize for the missing labels again, and we have now labeled the figures properly. We hope that the revision (with additional data and properly labelled figures) has made the structure of the manuscript sound.

Reviewer #1 (Significance (Required)):

General assessment * Provides new insight into non-canonical roles of Bcl-xL in cancer * Relies heavily on over-expressed proteins to draw conclusions * If the data were stronger and supported the conclusions, this study could be of interest to a broad cancer audience

My expertise Cell biology, cell death, cancer, imaging

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): ____ __ The manuscript describes a large number of experiments each of which describes a small part of the functional cascade of Bcl-xL in nuclear function and metastatic tumor behavior. No one experiment accomplishes a lot, but taken as a total, the story is compelling and fairly complete.

Major: Figure 1 shows Bcl-xL in one primary sample (a) but clearly not in a second one (c). The authors state 3 of 15. Can they make any comment about breast cancer subtype of these 3 or outcomes? This seems fairly thin evidence of Bcl-xL involvement in human tumorigenesis in general - a better survey might be performed with tissue microarrays of more than one cancer subtype. I'm not sure that this figure is compelling or necessary really for the rest of the manuscript. Really, the main weakness of this paper is some proof that this Bcl-xL-mediated pathway is significant in some proportion of human cancer and metastasis. Perhaps some RNASeq datasets on metastatic versus localized cancers could be mined to establish this relvance?

__Response: __We appreciate this suggestion. We have compared the breast cancer subtypes and the outcomes of the cases used in the original immunofluorescent study. No particular cancer subtype or outcome of these cases is associated with the presence of more nuclear Bcl-xL.

As suggested by the reviewer, we used breast cancer TMAs to investigate the involvement of Bcl-xL in human tumorigenesis in general. We have found that the cases positive of peri-nuclear and nuclear Bcl-xL showed an increasing trend of metastases (Table 1d). We have included the following information in the revised manuscript.

“We further evaluated human breast specimens in tissue microarrays (TMAs), consisting of 25 non-neoplastic breast tissues, 150 primary breast cancer, 55 lymph node metastases, and 99 metastatic breast cancer at various distant sites, for the expression and localization of Bcl-xL by immunohistochemistry. Compared to normal breast tissues, the intensity of Bcl-xL was significantly higher in breast cancer, including primary tumors, lymph node (LN) metastases, and distant metastases (Table 1a and 1b). The proportion of positive perinuclear/nuclear Bcl-xL cases was significantly increased in human breast cancer tissues compared to normal breast tissues (Table 1c and Figure 1d), and it showed an increasing trend towards metastases (Table 1d, p =0.004).”

Most other experiments and figures are well explained. The only one I have some trouble with is Figure 8 CUT and RUN data where we are only presented with peaks around six genes. Is there a way to summarize data for the rest of the genome? Or to display a composite of CUT and RUN data on promoters that are not predicted to be targets of Bcl-xL and MLL1 activity (compared to those that are)?

__Response: __We have deposited the entire CUT&RUN-Seq datasets in Gene Expression Omnibus (accession #GSE221629, https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc= GSE221629), which will become publicly available when the manuscript is published.

It is very challenging to present 1,190 unique H3K4me3 histone modification regions, and we tried our best to present the CUT&RUN-Seq data in the revised manuscript. In addition to the differential H3K4me3 peaks around promoters of six genes, we have included genome browser view, including the whole gene body by zooming out in Supplementary Figure S7 and peaks for 9 regions that are not targets of Bcl-xL and MLL1 activity in Supplementary Figure S8. Furthermore, we used Hypergeometric Optimization of Motif EnRichment (HOMER) to perform motif analysis for the differential H3K4me3 peaks. Enrichment p-values of the motifs were between 1e-12 and 1e-2 (Supplementary Table S5). It is of note that motifs with a p-value of more than 1e-10 or even 1e-12 are likely to be false positives (http://homer.ucsd.edu/homer/introduction/basics.html). The result revealed the limitation to identify motifs around the H3K4me3 CUT&RUN peaks recognized by the nuclear Bcl-xL complex.

Minor: While the main future direction pointed out by the manuscript was made in the last sentence of the Discussion, it could be spelled out in more detail to enforce the manuscript's impact.

__Response: __We appreciate this suggestion and expanded the discussion in the revised manuscript to enforce the impact of this work.

Reviewer #2 (Significance (Required)):

The authors describe nuclear targets and functions of the anti-apoptotic protein TF Bcl-xL, which has long been of research interest to this group. Specifically, this manuscript follows up on Choi 2016 which established that nuclear localization seemed to be critical for promotion of metastatic/invasion properties of Bcl-xL independent of its anti-apoptotic function. Due to the membrane localization in cells, it was unclear how Bcl-xL entered the nucleus, simulating the current paper. Here the authors (i) demonstrate this nuclear localization happens without mutation to the protein, (ii) localization is promoted by binding to CtBP2 in co-precipitations, (iii) enforced loss of CtBP2 expression correlated with lower metastasis, (iii) specific domains within the two proteins are necessary for physical interaction and function (iii) the histone methyltransferase MLL is critical for downstream transcriptomic impacts which include upregulation of the TGFbeta pathway. Description of this pathway and the specific protein domains necessary may lead to therapeutic targets to repress metastatic capacity. This reviewer is an expert as a cancer biologist and epidemiologist.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __ Summary Zhang et al. investigated new roles of Bcl-xL and CtBP2 in cancer progression. They previously reported that Bcl-xL is nuclear localized and promotes cancer metastasis by inducing global histone H3 trimethyl Lys4 (H3K4me3) independent of its anti-apoptotic activity. In this study, they found that CtBP2 is a key factor for promoting the nuclear translocation of Bcl-xL. Furthermore, they showed that the binding between Bcl-xL and CtBP2 is required for MLL1 activation. MLL1 mediates the Bcl-xL-induced H3K4me3 activation and upregulation of TGFβ mRNA level. By global analysis of histone H3K4me3, the authors demonstrated that H3K4me3 modifications are enriched in the promoter regions of genes encoding TGFβ and related signaling pathways in cancer cells overexpressing Bcl-xL. Therefore, they concluded that Bcl-xL exerts its metastatic function by interacting with CtBP2 and MLL1. The mechanism for histone modification by Bcl-xL is interesting and this study expanded our current understanding of epigenetic regulation in cancer. However, the mechanism for MLL1 activation induced by Bcl-xL is not fully demonstrated.

Major points 1) Figure 1) The number of primary breast cancer and lymph node specimens is too small. The authors analyzed only two cases of primer breast cancer and one case of lymph node metastasis. They should also present the result of normal breast tissues to show increased nuclear enrichment during disease progression. In addition, quantification of nuclear signals and statistical analysis are necessary. More importantly, the expression of CtBP2 and MLL1 should be evaluated in these clinical samples because they claimed that the interaction of Bcl-xL/CtBP2/MLL1 is important for tumor metastasis in this study.

__Response: __We appreciate this suggestion to increase the number of the clinical samples. We have stained breast cancer TMAs and included normal breast tissues to show increased nuclear enrichment during disease progression (Table 1). We have included the following information in the revised manuscript. Although we would also like to co-stain these breast cancer TMAs with CtBP2 and MLL1, there are no suitable antibodies for co-staining these two proteins with Bcl-xL in these FFPE sections.

“We further evaluated breast cancer specimens in tissue microarrays (TMAs) for the expression and localization of Bcl-xL by immunohistochemistry. Compared to normal breast tissues, the intensity of Bcl-xL was significantly higher in breast cancer, including primary tumors, lymph node (LN) metastases, and distant metastases (Table 1a and 1b). Perinuclear/nuclear Bcl-xL is significantly increased in human breast cancer tissues compared to normal breast tissues (Table 1c and Figure 1d). The proportion of peri-nuclear and nuclear Bcl-xL positive cases showed an increasing trend towards metastasis (Table 1d).”

2) (Figure 2c) In this experiment, the expression of Bcl-xL is mainly observed in the cytoplasm even in the condition of shControl. Therefore, I think that the nuclear localization of Bcl-xL is not convincingly regulated by CtBP2 expression change. Overexpression of CtBP2 is also necessary to show CtBP2-dependent nuclear localization of Bcl-xL.

__Response: __We appreciate this suggestion to overexpress CtBP2. We have performed this experiment by transiently transfecting cells with CtBP2 and found that overexpression of CtBP2 increased the nuclear to cytosol ratio of Bcl-xL (new Figure 2b and 2c) and included the following information in the revised manuscript.

“To determine the role of CtBP2 in mediating Bcl-xL’s nuclear translocation, we employed overexpression and knockdown of CtBP2 approaches. To overexpress CtBP2, we transfected a V5-tagged CtBP2 construct (Paliwal et al., 2006) into 293T cells and performed immunofluorescent staining using anti-V5 and anti-Bcl-xL antibodies. We observed an increased nuclear-to-cytosol ratio of endogenous Bcl-xL in cells overexpressing CtBP2-V5 (Figure 2b and 2c).”

3) (Figure 6d-e) These results are important because the anti-apoptotic activity is not inhibited even if the interaction between CtBP2 and Bcl-xL is lost. I wonder whether the authors analyzed the cellular localization of each mutant protein (particularly, wt, construct #5 and #6) in the presence of CtBP2. In addition, the authors should examine how the histone K4me3 and MLL1 activity is affected by overexpressing construct #5 and #6 to elucidate the metastatic ability by these constructs (Figure 6e). The authors should describe whether wt Bcl-xL is constract #2 or not in the legends.

__Response: __We appreciate that the reviewer pointed out the importance of our finding that even if the interaction between CtBP2 and Bcl-xL is lost, the anti-apoptotic activity of Bcl-xL is not inhibited. As suggested by the reviewer, we described wt Bcl-xL as construct #2 in the manuscript, and we analyzed the subcellular localization of wt HA-Bcl-xL (construct #2, which binds to CtBP2), construct #5 (which binds to CtBP2), and construct #6 (which does not bind to CtBP2), in the presence of endogenous CtBP2 in N134 mouse PNET cells. We found that the nuclear to cytosol ratio of wt HA-Bcl-xL (construct #2) and construct #5 was similar to each other, and we observed a reduction in the nuclear-to-cytosol ratio of construct #6 (Figure 6f and 6g). This is in consistent of the reduction of the metastatic ability of construct #6.

Further, we examined H3K4me3 and MLL1 in these cells and found that H3K4me3 was reduced in construct #6 compared to wt HA-Bcl-xL (construct #2) and construct #5 (Figure 6c). We also found that H3K4me3 levels were reduced in the CtBP2 knockout cells (Supplementary Figure S5b).

Minor points 4) (Figure 2d) Labels for these graphs are lacking.

__Response: __We apologize for the missing labels when we merged the graphs. We have added them back (new Figure 2f).

5) (Figure 2e, f) The authors should label in these graphs whether these results are statistically significant or not.

__Response: __Thanks for the suggestion. We have labeled * for statistically significant (P 6) (Figure 3c) No labels for these blots.

__Response: __We apologize for the missing labels when we merged the graphs. We have added them back.

7) (Figure 3b) They should describe the full spell of n/a in the legends.

__Response: __Thanks for the suggestion. We have described “n/a: non-sorted parental cells” in the legends in the revision.

8) (Figure 4f) The label of Y-axis should be corrected.

__Response: __Thanks for the suggestion. We have corrected the label of Y-axis.

9) (Figure 8c) The location of gene transcriptional start site and ChIP signal level should be shown. In addition, the genome browser view including whole gene body by zooming out should be shown.

__Response: __In addition to the differential peaks around promoters of six genes in Fig. 8, we have included the whole gene body with the location of the gene transcriptional start site in Supplementary Figure S7.

Reviewer #3 (Significance (Required)):

It is interesting that Bcl-xL can be transported to the nucleus and modulate the entire epigenetic condition for promoting metastatic ability. In the previous study, this group highlighted the nuclear function of Bcl-xL in cancer cells. This concept, Bcl-xL functions independent of its anti-apoptotic activity (Choi et al. Nat Commun 2016;7:10384.), is highly original and will bring some impacts on cancer research. In this study, the authors revealed molecular mechanisms to elucidate this nuclear translocation of Bcl-xL and how Bcl-xL regulate the epigenetic condition. However, the authors should present more evidences to demonstrate the mechanism that CtBP2/Bcl-xL interaction with MLL1 regulate global K4me3 levels in the nucleus to promote metastasis. 1) First of all, there are insufficient data to demonstrate how the interaction with Bcl-xL is involved in MLL1 activation. In Figure 7e, the authors analyzed H3K4me3 level by only inhibiting MLL1 expression and activity. However, the authors should investigate whether Bcl-xL and CtBP2 knockdown or overexpression modulate MLL1-mediated histone H3K4me3 regulation.

Response: __We appreciate that Reviewer #3 considered our work to be highly original. As suggested, we investigated whether CtBP2 knockout affected H3K4me3 levels and found that H3K4me3 levels were reduced in the CtBP2 knockout cells (Supplementary Figure S5b). Conversely, we have reported that Bcl-xL overexpression increases H3K4me3 levels (Choi et al., 2016). The main take-home message of this study is the discovery of the nuclear translocation mechanism of Bcl-xL through a novel interaction with CtBP2. We have shown that Bcl-xL or CtBP2 binds to MLL1 only when Bcl-xL and CtB2 bind to each other (__Figure 5b, 5c, and__ 6b__).

2) (Figure 8) The authors should explain why MLL1 activation specifically affect the K4me3 levels of TGFβ signal-associated genes. I wonder whether Bcl-xL/MLL1/CtBP2 functions as cofactors by binding to certain transcription factors. In addition, Bcl-xL, CtBP2 and MLL1 ChIP-seq/CUT & RUN analysis would be preferable.

__Response: __We have tried but have not been able to successfully establish the CUT&RUN conditions using Bcl-xL, CtBP2, and MLL1 antibodies. Whether Bcl-xL/MLL1/CtBP2 functions as cofactors by binding to certain transcription factors is a very interesting question. Additional studies are required to identify the other components of this Bcl-xL/CtBP2/MLL1 protein complex, which is beyond the scope of this work. This is added in the Discussion of the revised manuscript.

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Referee #3

Evidence, reproducibility and clarity

Summary

Zhang et al. investigated new roles of Bcl-xL and CtBP2 in cancer progression. They previously reported that Bcl-xL is nuclear localized and promotes cancer metastasis by inducing global histone H3 trimethyl Lys4 (H3K4me3) independent of its anti-apoptotic activity. In this study, they found that CtBP2 is a key factor for promoting the nuclear translocation of Bcl-xL. Furthermore, they showed that the binding between Bcl-xL and CtBP2 is required for MLL1 activation. MLL1 mediates the Bcl-xL-induced H3K4me3 activation and upregulation of TGFβ mRNA level. By global analysis of histone H3K4me3, the authors demonstrated that H3K4me3 modifications are enriched in the promoter regions of genes encoding TGFβ and related signaling pathways in cancer cells overexpressing Bcl-xL. Therefore, they concluded that Bcl-xL exerts its metastatic function by interacting with CtBP2 and MLL1. The mechanism for histone modification by Bcl-xL is interesting and this study expanded our current understanding of epigenetic regulation in cancer. However, the mechanism for MLL1 activation induced by Bcl-xL is not fully demonstrated.

Major points

1. Figure 1) The number of primary breast cancer and lymph node specimens is too small. The authors analyzed only two cases of primer breast cancer and one case of lymph node metastasis. They should also present the result of normal breast tissues to show increased nuclear enrichment during disease progression. In addition, quantification of nuclear signals and statistical analysis are necessary. More importantly, the expression of CtBP2 and MLL1 should be evaluated in these clinical samples because they claimed that the interaction of Bcl-xL/CtBP2/MLL1 is important for tumor metastasis in this study.
2. (Figure 2c) In this experiment, the expression of Bcl-xL is mainly observed in the cytoplasm even in the condition of shControl. Therefore, I think that the nuclear localization of Bcl-xL is not convincingly regulated by CtBP2 expression change. Overexpression of CtBP2 is also necessary to show CtBP2-dependent nuclear localization of Bcl-xL.
3. (Figure 6d-e) These results are important because the anti-apoptotic activity is not inhibited even if the interaction between CtBP2 and Bcl-xL is lost. I wonder whether the authors analyzed the cellular localization of each mutant protein (particularly, wt, construct #5 and #6) in the presence of CtBP2. In addition, the authors should examine how the histone K4me3 and MLL1 activity is affected by overexpressing construct #5 and #6 to elucidate the metastatic ability by these constructs (Figure 6e). The authors should describe whether wt Bcl-xL is constract #2 or not in the legends.

Minor points

1. (Figure 2d) Labels for these graphs are lacking.
2. (Figure 2e, f) The authors should label in these graphs whether these results are statistically significant or not.
3. (Figure 3c) No labels for these blots.
4. (Figure 3b) They should describe the full spell of n/a in the legends.
5. (Figure 4f) The label of Y-axis should be corrected.
6. (Figure 8c) The location of gene transcriptional start site and ChIP signal level should be shown. In addition, the genome browser view including whole gene body by zooming out should be shown.

Significance

It is interesting that Bcl-xL can be transported to the nucleus and modulate the entire epigenetic condition for promoting metastatic ability. In the previous study, this group highlighted the nuclear function of Bcl-xL in cancer cells. This concept, Bcl-xL functions independent of its anti-apoptotic activity (Choi et al. Nat Commun 2016;7:10384.), is highly original and will bring some impacts on cancer research. In this study, the authors revealed molecular mechanisms to elucidate this nuclear translocation of Bcl-xL and how Bcl-xL regulate the epigenetic condition. However, the authors should present more evidences to demonstrate the mechanism that CtBP2/Bcl-xL interaction with MLL1 regulate global K4me3 levels in the nucleus to promote metastasis.

1. First of all, there are insufficient data to demonstrate how the interaction with Bcl-xL is involved in MLL1 activation. In Figure 7e, the authors analyzed H3K4me3 level by only inhibiting MLL1 expression and activity. However, the authors should investigate whether Bcl-xL and CtBP2 knockdown or overexpression modulate MLL1-mediated histone H3K4me3 regulation.
2. (Figure 8) The authors should explain why MLL1 activation specifically affect the K4me3 levels of TGFβ signal-associated genes. I wonder whether Bcl-xL/MLL1/CtBP2 functions as cofactors by binding to certain transcription factors. In addition, Bcl-xL, CtBP2 and MLL1 ChIP-seq/CUT & RUN analysis would be preferable.

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

The manuscript describes a large number of experiments each of which describes a small part of the functional cascade of Bcl-xL in nuclear function and metastatic tumor behavior. No one experiment accomplishes a lot, but taken as a total, the story is compelling and fairly complete.

Major:

Figure 1 shows Bcl-xL in one primary sample (a) but clearly not in a second one (c). The authors state 3 of 15. Can they make any comment about breast cancer subtype of these 3 or outcomes? This seems fairly thin evidence of Bcl-xL involvement in human tumorigenesis in general - a better survey might be performed with tissue microarrays of more than one cancer subtype. I'm not sure that this figure is compelling or necessary really for the rest of the manuscript. Really, the main weakness of this paper is some proof that this Bcl-xL-mediated pathway is significant in some proportion of human cancer and metastasis. Perhaps some RNASeq datasets on metastatic versus localized cancers could be mined to establish this relvance?

Most other experiments and figures are well explained. The only one I have some trouble with is Figure 8 CUT and RUN data where we are only presented with peaks around six genes. Is there a way to summarize data for the rest of the genome? Or to display a composite of CUT and RUN data on promoters that are not predicted to be targets of Bcl-xL and MLL1 activity (compared to those that are)?

Minor:

While the main future direction pointed out by the manuscript was made in the last sentence of the Discussion, it could be spelled out in more detail to enforce the manuscript's impact.

Significance

The authors describe nuclear targets and functions of the anti-apoptotic protein TF Bcl-xL, which has long been of research interest to this group. Specifically, this manuscript follows up on Choi 2016 which established that nuclear localization seemed to be critical for promotion of metastatic/invasion properties of Bcl-xL independent of its anti-apoptotic function. Due to the membrane localization in cells, it was unclear how Bcl-xL entered the nucleus, simulating the current paper. Here the authors (i) demonstrate this nuclear localization happens without mutation to the protein, (ii) localization is promoted by binding to CtBP2 in co-precipitations, (iii) enforced loss of CtBP2 expression correlated with lower metastasis, (iii) specific domains within the two proteins are necessary for physical interaction and function (iii) the histone methyltransferase MLL is critical for downstream transcriptomic impacts which include upregulation of the TGFbeta pathway. Description of this pathway and the specific protein domains necessary may lead to therapeutic targets to repress metastatic capacity. This reviewer is an expert as a cancer biologist and epidemiologist.

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

In this study the authors build on their previous work that Bcl-xL has a role in metastasis promotion independent of it's function in the mitochondrial apoptotic pathway. They show that Bcl-xL can be found in the nucleus of some human breast cancer cells and through a mass spec approach show that CtBP2 promotes the nuclear translocation of Bcl-xL. Using various knockdown/knockout methods they show that reduced levels of CtBP2 reduces metastasis, because of loss of Bcl-xL translocation to the nucleus. The authors map this interaction and show that this interaction modulates metastasis.

Major comments

• Figure 1 - a more comprehsive analysis of nuclear Bcl-xL should be conducted. The data presented only shows 3 different samples, with no quantification. Perhaps the authors could stain a breast cancer TMA or simiilar?
• Figure 2 - could the authors show the a graph with a representation of the mass spectrometry data, so the reader can get a sense of how many proteins were found to be associated with Bcl-xL?
• Have the authors tried any other ways to verify the interaction between Bcl-xL and CtBP2? For instance, do they co-localise when imaged? Also, can the reverse IP be performed?
• Figure 2C - the authors claim that this data shows that Bcl-xL nuclear translocation is reduced in cells with reduced levels of CtBP2 - however, although they quantify this I simply do not see it from the images presented. I do not think this data supports the conclusion that knockdown of CtBP2 reduces Bcl-xL translocation to the nucleus.Furthermore, this data is only shown with overexpressed Bcl-xL - have the authors tried with endogenous staining of Bcl-xL?
• Figure 2e-f - again these data are in cells with overexpressed Bcl-xL - does the same effect on invasion happen when only CtBP2 levels are reduced, without overexpression of Bcl-xL? What happens when Bcl-xL is knocked down? Also, doxycycline has been shown to affect mitochondrial function, which might confound this data - perhaps another way to knockdown CtBP2 (e.g. CRISPR which is used later in the study) would rule this out
• Figure 3c - these blots are not labelled, but ideally this would be shown with endogenous Bcl-xL, rather that just the overexpressed HA-Bcl-xL. However these data are more convincing than the images presented in Figure 2c
• Figure 4 - the authors use CRISPR to knockout CtBP2 - logically this data would go with the shRNA data shown before, as it seems to just repeat what has already been shown?
• Figure 4d - what does "SN" refer to? There is no loading control for this part of the fractionation - I assume this is supernatant? If so, why is there no loading control for this (same applies to figure 3c). Also, why are these not on the same blot? If CtBP2 knockdown reduces Bcl-xL mRNA level, does it also reduce Bcl-xL protein levels? We should be able to tell this from the blots in figure 4d, but since they are on different membranes this is impossible to deduce
• Figure 5c - molecular weight markers should be included here
• Figure 7a - the text says that MM102 treatment "significantly reduced" H3K4me3 levels - where is the quantification of this?

Minor comments

• Some of the figures are not properly labelled
• Some of the data are presented in an awkward manner - the authors should consider re-structuring either the manuscript or the figures so there is less "jumping around"

Significance

General assessment

• Provides new insight into non-canonical roles of Bcl-xL in cancer
• Relies heavily on over-expressed proteins to draw conclusions
• If the data were stronger and supported the conclusions, this study could be of interest to a broad cancer audience

My expertise

Cell biology, cell death, cancer, imaging

Transparent Peer Review

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

This article by Raphael Schleutker and Stefan Luschnig addresses the importance of S-palmitoylation of the proteolipid protein M6, one of the three components of tricellular septate junction along with Anakonda and Giotactin, in the assembly of tricellular junctions using Drosophila embryo as a model system. Using a combination of state-of-the-art genome engineering, live imaging and biochemistry, the authors demonstrated that M6 is palmitoylated in vivo, elegantly identified the cysteine residue that is palmitoylated, showed that this modification is essential for interaction with Anakonda and provided convincing evidence that palmytoylation is required for the initial assembly of tricellular junctions.

Major comments:

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them? The claims are largely supported by the very high quality data assembled in this article. I have just a few concerns that can be resolved by modifying the text or, optionally, by carrying out additional experiments:

• in the summary (lane 40) and all along the article it is stated that 'Abolishing M6 palmitoylation leads to delayed accumulation of M6 and Aka at vertices but does not affect the rate of TCJ growth or mobility of M6 or Aka.'<br /> However, whilst the data presented convincingly demonstrate the delayed localization of GFP::M6 delta Palm at TCJ, that of Aka at TCJ is not shown. Although I think this is a reasonable hypothesis, without showing Aka localization, this claim is too strong and should be toned down, or better (optional) show the dynamics of Aka localization. Lanes 184 and 197 'indicating that effcient TCJ formation depends on M6 palmitoylation.' TCJ formation is not assessed here, what is measured is the localization of M6 at vertex. I suggest to amend the text accordingly.

• Fig. 5C and lane 292' Lack of M6 palmitoylation reduces, although it does not completely abolish, the interaction with Aka, ....' In Fig. 5C, GFP::M6 efficiently co-precipitates three forms of Aka with different molecular weights. The two upper bands are highly enriched in the GFP::M6 coIp. In contrast, GFP::M6 delta Palm seems to coIp only the low molecular weight form of Aka. Could the authors explain what the three forms of Aka are, and provide potential explanations or interpretations of this result?

• 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.

• Are the data and the methods presented in such a way that they can be reproduced? The data are of very high quality and the methods sufficiently described (with appropriate references where necessary) and presented in such a way that they can be reproduced.

• Are the experiments adequately replicated and statistical analysis adequate? Although the microscopy data are perfectly quantified and the appropriate statistical tests are used, unless I am mistaken, the number of replicates and the number of independent experiments carried out in biochemistry (Fig. 2 and Fig. 5) are not indicated.

Minor comments:

• Specific experimental issues that are easily addressable.

• The localization of M6 on living specimens, GFP::M6 enriched at the tricellular junction, differs from the localization of M6 detected by anti-M6 on fixed samples, i.e. M6 homogenous distributed at the bicellular junction, no enrichment at the tricellular junction. Please comment and possibly explain the reason for the difference in localisation. Is the anti-GFP staining on the GFP::M6 sample restricted to the bicellular junction without apparent TCJ enrichment?

• In Fig. S2, isoforms E and F are expressed at low level but fully rescue Gli localization but not Aka. These results are somewhat surprising if Gli localization relies on Aka and M6 localization at TCJ. Is localization of M6 at TCJ important or is it the expression of M6 that matters? Would it be possible to compare the expression levels of the different isoforms?.

• lane 118 'Notably, vertex enrichment varied between M6-GFP isoforms and was inversely proportional to overall signal intensity, suggesting that saturation effects upon overexpression impede vertex enrichment. Consistent with this notion, endogenous GFP::M6CA06602 showed higher vertex enrichment (7.8-fold; Fig. 1E, L) than the individual overexpressed isoforms.' To conclude that all isoforms contain the elements for vertex localization, it would be interesting to provide the level of expression (signal intensity) for all M6 isoform as well as M6deltaPAlm-GFP to appreciate the threshold above which saturation is achieved? Or better (optional) to express the different isoforms in a M6 mutant background. Could the authors exclude the possibility that the position of the GFP moiety affect the localization of M6 at TCJ?

• lanes 187 '...in a single spot that subsequently extends basally with a speed of 0.09 μm/min ' The images are presumably projections along the apical basal axis, so it is difficult to appreciate the apical to basal extension, perhaps an orthogonal section would help.

• Are prior studies referenced appropriately? yes

• Are the text and figures clear and accurate? yes

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.

The following aspects are important:

Tricellular junctions are hot spots integrating mechanical and chemical inputs that are essential to ensure epithelia homeostasis. It is therefore essential to understand how the components of tricellular junctions are located and assembled to form functional tricellular junctions. The authors brilliantly demonstrate the key role of S-palmitoylation in M6 localization and ability to interact with Aka in vivo. The fact that the role of palmitoylation appears to be conserved for the assembly of vertebrate TCJs, made up of components that are not conserved throughout evolution, indicates a fundamental function of palmitoylation in protein-protein interactions at the level of TCJs and in their vesicular trafficking. As palmitoylation is reversible, this work also raises the question of how palmitoylation is regulated in time and space to ensure the plasticity of TCJs in developing epithelia.

• 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?

• 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,...).

This study follows on from that showing the role of Angulin1 palmitoylation in its localization to tricellular junctions in vertebrates. The present study demonstrates the conserved nature of the role of this post-translational modification in the assembly of complex membrane structures essential for epithelial homeostasis. In addition, it demonstrates the dynamic nature and temporality of the role of palmytoylation in the early stages of recruitment of M6 to the vertex, opening up numerous hypotheses for future work at the conceptual and fonctional levels, elegantly presented in the discssion.

• 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?

I believe this article is dedicated to a rather broad audience. Although this article may at first appear to be aimed at specialists, the findings go beyond the interest in tricellular junctions in Drosophila, since the role of palmytoylation of tricellular components appears to be conserved in vertebrates. In addition, this study will have an impact on the overall cell biology community, including membrane trafficking and the role of lipid modification additions on the subcellular dynamics of transmembrane proteins in a physiological context.

• 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 developmental cell biologist, with an expertise in epithelial junctions and epithelial tissue homeostasis, using vertebrate and invertebrate model systems.

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Referee #1

Evidence, reproducibility and clarity

The epithelial diffusion barrier in triangular junctions is initially formed by a protein complex of Aka, Gli and M6. Aka and M6 act upstream of Gli. GPM6a, the vertebrate homolog of M6 is palmitoylated, whose functional implications have not thoroughly been analyzed, yet. It order to better define the function of M6 and especially the role of the palmitoyl moity, the authors conducted a genetic analysis of M6 in Drosophila embryos.

• They first establish a genetic system with defined mutants (deletion and CS mutants which are not palmitoylated), tagged protein at the genetic locus and an quantitative assay for protein enrichment at triangular junctions. Secondly they provide biochemical evidence that M6 is palmitoylated at a cluster of three conserved cysteine residues in vivo. With a palmitoylation-deficient mutant, thirdly the authors investigate the function of the palmitoyl moiety for protein localization at triangular junctions and complex formation with the other proteins at triangular junctions. The authors reveal a quantitative function of the palmitoyl moiety at triangular junctions with respect to enrichment and initial accumulation but not for later functions during growth of triangular junctions. The lower enrichment of the non-palmitoylated M6 mutant are sufficient for recruitment of Aka and Gli. Importantly, reducing Aka in combination with the non-palmitoylated mutant leads to a strong phenotype with respect to Gli localization and and leads to a genetically synthetic embryonic lethality. Fourthly, on a molecular level, the palmitoyl residue mediates binding to Aka but is not required for di/oligomerization of M6 itself as shown by immunoprecipitation from embryonic lysates.

• Though the function of M6 acting together with Aka and Gli has been demonstrated previously, molecular details of the interactions and targeting of the proteins to triangular junctions have remained unclear. Similarly, although palmitoylation of the vertebrate homologue has been previously demonstrated, its functional implications have not been investigated in a physiological context with stringent genetics. The current study provides convincing data about the role of the palmitoylated moiety of M6. Importantly, the authors manage to differentiate a function of the palmitoyl residue in initial accumulation of M6 at triangular junctions versus maintenance. Also the authors manage to reveal an essential function of M6 palmitoylation when the dose of Aka is reduced. In summary, the study provides novel and interesting insights into the detailed molecular requirements of epithelial barrier formation. Although the quality of the data and analysis provides an argument for publication on its own, it may be noted that similar mechanisms may underlie barrier formation at triangular junction in vertebrates given the conservation of the protein components.

Minor comments:

1. L100: it is stated that "... is not detectable on other known TCJ components". What about Angulin-1, which is palmitoylated?

2. L122 In my understanding all M6 isoforms contain an element which is sufficient. Not "required".

3. L336. The allele designation "DeltaPalm" is misleading. A designation like "3xCS" would be more better because three defined cysteine residues are mutated.

4. L329 A reference to FLYBASE is missing. Similarly not reference to stock centers are provides. To document the importance of the community services it is essential that their services are properly cited in a way that can be automatically tracked, e. g. by a literature citation.

Significance

In summary, the study provides novel and interesting insights into the detailed molecular requirements of epithelial barrier formation. Although the quality of the data and analysis provides an argument for publication on its own, it may be noted that similar mechanisms may underlie barrier formation at triangular junction in vertebrates given the conservation of the protein components.

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Reply to the reviewers

Reviewer #1:

Comment: The author investigated the role of the stress sensor pathway in the mechanism of tumor cell survival<br /> They identified a long noncoding RNA as JUNI that regulates antagonizing MAP phosphatase and favors the JUN transcription. JUNI correlated with the survival of several cancer histotypes, particularly in RCC, as a highly specific and correlated prognosis.

The abstract although not always required from the journal should be divided into methods used to reach the main findings and clear presentation of results

Response: We do not know yet to which Journal the paper will be sent. The format will be adjusted to the Journal requirements.

it is unclear whether JUNI is a positive or negative regulator of JUI (I assume the reviewer meant JUN)

Response: The text in the abstract was changed to” JUNI positively regulates the expression of its neighboring gene JUN, a key transducer of signals that regulate multiple transcriptional outputs.”

Hope it is clearer now

When the author indicates that JUNI antagonizes MAP PHOSPHATASE is not correct the term antagonism is related to receptors but the authors did not show any receptor.

Response: The term "antagonism" does not only refer to receptor drugs. In pharmacology, antagonism generally describes the interaction between a drug (or other molecule) and a receptor or biological target that results in the inhibition or blocking of the receptor's activity. However, this concept can extend beyond receptor drugs and apply to various biological interactions.

Outside of the realm of drugs and receptors, antagonism can also refer to antagonistic relationships between different biological processes, molecules, or organisms.

Overall, while antagonism is commonly discussed in the context of receptor drugs, the concept of antagonism can apply to a broader range of interactions in biology and other fields.

Response: The p values for the prognostic values of JUNI and DUSP14 in RCC were added to the abstract.

Generally, Jun oncogene correlated with poor overall survival while the table indicates promote survival so good prognosis?

Response: This manuscript describes for the first time the biological activity and cancer relevance of JUNI. It positively regulates stress induced c-Jun and can be used as prognostic marker in ccRCC.

The significance of JUNI and its interactome in ccRCC prognosis is unequivocal, according to data analysis of cancer relevant data (TCGA) regardless to its effects on c-Jun. The concern raised by reviewer 1 and 2 is whether the cancer-relevant effects are mediated by c-Jun regulation. We suggest that despite regulating stress induced c-Jun, they are not! This suggestion is based on three points: 1. We show in the manuscript that a large portion of JUNI dependent effects on cellular survival activity is c-Jun independent. 2. We describe many interacting proteins that may, in a JUN-independent manner, affect tumorigenesis. 3. In this study we examined JUNI’s functions which are cell-autonomous. However, neither the non -autonomous effects nor effects on cells that compose the tumor environment were studied. Reports that lncRNAs may have a role in immune responses and high expression of JUNI in CD8 cells may suggest this direction for future investigation (Carpenter, S et al. science, 341(6147), pp.789-792; Mickaël, M. et al https://doi.org/10.1101/2021.12.01.470587)

Therefore, we assume that direct correlations in every biological activity between JUNI and JUN is an over simplified consumption. Analogy for that can be found with another major regulator of c-Jun, JNK, which is stress induced, c-Jun regulator involved in stress-induced cell death, whereas c-Jun itself is contributing in many cases to drug resistance.

The introduction contains the main information to follow the role of JUN and renal carcinoma<br /> However, should be improved with background on the key role of stress genes in the pro-survival pathway of tumors during progression and hypoxia condition. Too many references on long noncoding compared to the JUN complex with AP-1 and transformation

Response: A section describing the major stress pathway in ccRCC, HIF 1 and its role in ccrCC was added. Due to the limitation of word count in most journals we cannot expend this section further

Results In Figure 1 the authors showed expression levels of JUNI and JUN that are clearly different after UV stimuli. they demonstrate that are both regulated by UV but the amount and the time are different. the author should comment on these data if they want to study the regulative mechanism

Response: The following comment was added at the end of the first section: Overall, these results suggested that JUNI is a stress-induced gene whose expression pattern resembles that of JUN, therefore, we investigated the potential existence of regulatory effects between the two genes, especially post exposure of cells to stress.

Figure 1 F the cellular distribution of JUNI which is the rational of this experiment to provide that is into nucleus while normally is into the cytoplasm? What adds this experiment?

Response: This is the first reported description of JUNI. We attempted to characterize it as much as possible. It’s localization was not described previously and we suggest that it is mainly nuclear. A novel important information that should be presented.

In Figure 2 the authors provided that the kinase pathway is important for Jun regulation but the effect on JUNI a Luciferase assay needs to be provided

Response: We respectfully disagree with the reviewer. We believe that examining the expression from a DNA fragment identical to the endogenous one is superior to artificial system, such as luciferase.

In Figure 3 for Migration assay is necessary to see cells on the other side of the filter by staining not a graphical representation

Response: The graphical representation is an accumulated result of at least 3 experiment. However, a figure representing a single experiment was added as a supplement figure s1.

The experiment on kinase does not add any data to what is already known on jun probably should be shifted in Figure 6

Response: We apologize, this question was not fully understood as there is no experiment on kinase in figure 3. If case the reviewer was referring to kinase inhibition in Fig 2A we do think it is needed as a positive control for the kinases activity.

Table 1 is cited two times once in the context of Figure 3 and then in Figure 6 indicating that the authors go forward and back on their experimental design

Response: Table 1 is indeed referred to in two places. It is first mentioned when we investigated the potential relevance of JUNI for human cancer, given its regulatory impact on the neighboring JUN gene and its influence on motility. Later, the types of cancers described in figure 1 were further processed in order to examine relations between JUNI and DUSP14 in human cancer. We do not see it as a flaw in experimental design but rather as further evolution of the story based on data discovered in earlier stages.

in figure 4 the apoptotic cells are not clearly visible a specific staining marker is necessary to provide the phenomenon

Response: Two corrections were made to demonstrate apoptosis clearly. The pictures in Figure 4 panel A were replaced with a better-quality image with addition of DNA staining to demonstrate the cell death clearer, appearance of cell blebbing and nuclear fragmentation. Panel B demonstrating increase in cleaved caspase 3 in JUNI silenced cells after all treatment was added.

Additionally XTT assay should be reported as the percentage of survival cells not staining incorporated compared to untreated cells over time

Response: We do apologize for the legend omission, but XTT assays, colonies formation and soft agar colonies formation are presented in Figure 4 H-J and Figure S3 for all cell lines

The data on prognosis and correlation of gene expression are not clearly presented and discussed

Response: Figure S4 was replaced by table S3 to demonstrate clearer the differences in Medians survival caused by JUNI of DUSP 14. Text was changed in the last section of results.

The western blot need to be quantified

Response: All blots were quantified

Reviewer #2:

1. While the experimental data showed JUNI, like c-JUN, is pro-survival of cancer cells, the clinical sample analyses correlated it positively with patients' survival. This discrepancy casts doubts in significance of the findings. The authors need to re-evaluate their data and conclusion

Response: This manuscript describes for the first time the biological activity and cancer relevance of JUNI. It positively regulates stress induced c-Jun and can be used as prognostic marker in ccRCC.

The significance of JUNI and its interactome in ccRCC prognosis is unequivocal, according to data analysis of cancer relevant data (TCGA) regardless to its effects on c-Jun. The concern raised by reviewer 1 and 2 is whether the cancer-relevant effects are mediated by c-Jun regulation. We suggest that despite regulating stress induced c-Jun, they are not! This suggestion is based on three points: 1. We show in the manuscript that a large portion of JUNI dependent effects on cellular survival activity is c-Jun independent. 2. We describe many interacting proteins that may, in a JUN-independent manner, affect tumorigenesis. 3. In this study we examined JUNI’s functions which are cell-autonomous. However, neither the non -autonomous effects nor effects on cells that compose the tumor environment were studied. Reports that lncRNAs may have a role in immune responses and high expression of JUNI in CD8 cells may suggest this direction for future investigation (Carpenter, S et al. science, 341(6147), pp.789-792; Mickaël, M. et al https://doi.org/10.1101/2021.12.01.470587)

Therefore, we assume that direct correlations in every biological activity between JUNI and JUN is an over simplified consumption. Analogy for that can be found with another major regulator of c-Jun, JNK, which is stress induced, c-Jun regulator involved in stress-induced cell death, whereas c-Jun itself is contributing in many cases to drug resistance.

Response: The Western blotting data need at least triplicate biological experiments and quantification. This is particularly important for trivial differences, such as shown in Fig. 6.

Response: All westerns X=3. Representative experiments are depicted. Quantification was added.

The identification and gene structure of LINC01135 and its relevance to c-Jun need better clarity

Response: First result section. “According to ENCODE data, JUNI contains five main exons and has multiple isoforms. Twenty-seven different transcript isoforms were described according to LNCipedia ranging from 213 to 6213 bases {Volders, 2019 #2907}. The relevance to c-Jun was referred to in discussion: Both the effects of JUNI on c-Jun induction and cellular survival were demonstrated using under-expression conditions by targeting, the common, first, exon of JUNI. Nevertheless, this exon was also sufficient for c-Jun induction upon stress exposure, under conditions of overexpression.

Page 9-10, Line 198-199, there are no results in Fig. 1 showing that JUNI induction was dependent to serum stimulation of starved cells

Response: “ Similar to JUN, the induction was dose dependent (Fig 1C), and the rapid response to stress (Fig 1D) as well as to serum stimulation of starved cells, identified by others (36), qualifies it as an “immediate early” lncRNA.”

Serum stimulation is described in reference 36

What is the Y-axis in figures 2B, 4E-G

Response: Legend was added to Y-axis of Figures 2B and 4 E-G

In Fig. 3B, actin image is missing

Response: Actin was hidden in the graphic process. Corrected.

In Fig. 4. brightfield images are inaccurate for distinguishing apoptosis and necrosis. Additional molecular markers need to be used, such as caspase-3 cleavage and LDH release

Response: Two corrections were made to demonstrate apoptosis clearly. The pictures in Figure 4 panel A were replaced with a better-quality image with addition of DNA staining to demonstrate the cell death clearer, appearance of cell blebbing and nuclear fragmentation. Panel B demonstrating increase in cleaved caspase 3 in JUNI silenced cells after all treatment was added.

The inconsistency of using four cell types in each assay. For example, in Fig. 4A, B, E-G and Suppl Fig. 1, HMCB, MDA-MB-231 and CHL1 cells were used to test the short-term effect of JUNI knockdown on cell survival, whereas Hela, MDA-MB-231 and CHL1 cells were chosen to determine the long-term effect of JUNI knockdown. Similar case in other figures.

Response: Effects on Jun regulation and the effects on long term survival were tested in all four cell lines both by XTT and clonogenic assays whereas effects on short term survival were tested in three out of the four cell lines. It is practically impossible to perform a study of this magnitude were all assays were tested in all cell lines. Using four cell lines was applied to prove the major points.

In Fig. 5D, no difference of c-Jun expression between NS and siJUN groups

Response: Correct, the western in 5D was replaced by a more representative one

Cell survival in Fig. 5 lacked statistical analyses

Response: Error bars were mistakably omitted. The figure was corrected.

In Suppl Fig. 2C, there is no figure to show the reduced colonies formation in soft agar in MDA-MB-231 cells, contradicting to that stated in the manuscript

Response: Indeed Figure 4 J and S3 C presented colonies formation in HMCB and HeLa cells. The text was corrected.

Reviewer #3: "linc01135" - this is a human gene, should be capitalized

Response: linc01135 was capitalized

Please indicate primers in Fig1A and mention this in relevant part of Results

Response: The following section was added: “Importantly, ENCODE predicts that the first exon is shared by all, therefore, all primers to analyze JUNI’s expression as well as siRNAs to silence it, were targeted for this exon.”

Fig1C-F - please add a legend to explain the colors

Response: Legend was added into the Figure as well

Copy number: It is important to establish the approximate copy number of JUNI RNAs in the cell lines tested. FISH would be one appropriate method. This could also be referenced back to the RNA-seq TPM values. Are we talking about <1 copy /cell, or many? Quick inspection of ENCODE RNA-seq in the UCSC browser suggest an intermediate value that varies between cell lines. This value is very important when interpreting mechanistic experiments later on

Response: The copy number in HMCB and MDA-MB-231 was calculated by comparison of CT values obtained from RNAs from a known number of cells relative to calibration curve of known concentrations of JUNI. The following section was added to the first paragraph of the results: “quantitation of JUNI’s copy number in untreated HMCB and MBA-MD-231 cells revealed the presence of minimal amount of about 8 copies per cell”

Fig3 - again, no figure legends, difficult for reader

Response: Legend was added to Fig. 3A

In general, the figures could be much more clearly annotated and presented with more care. They do not do justice to the quality of the work itself. For example, Fig4E-G why not label each panel with the time course, the cell line tested etc etc to save us the work of digging through the Legends?

Response: We thank the reviewer for this remark. All figures were corrected, legends and proteins quantification was added.

Rescue experiments: The rescue experiments in Fig5D are nicely done and the results are interesting. However, I would request the authors to perform similar experiments with JUNI rescue. Specifically, to knock down JUNI with siRNA, and then reintroduce it from an 'immune' expression plasmid, where the siRNA site is mutated. This will further strengthen the claim that JUNI siRNA is acting through the intended target to cause observed effects on cell viability

Response: As the effects on survival are strongest in the longer term, 14 days after silencing, rescue experiments were performed to test the rescue in the survival of HMCB and HeLa cells using clonogenic assays. Results are presented in figure 4 L

IncPrint data: was Jun protein found to be an interactor? This might be mentioned in the text, whether it is yes or no

Response: c-Jun was screened and did not interact with JUNI. The text was changed as following” Interestingly, c-Jun itself does not interact with JUNI (Table S2, Normalized luciferase intensity MS2, RLU =0.44). By contrast, the dual specificity protein phosphatase 14….”

Expression: A key issue is the expression of JUNI in healthy and diseased cells and organs. Is JUNI ubiquitous (and essential to both healthy and tumor cells), or is it specific to tumor cells? Which tumor types? This would be straightforward to find out from public data. I would suggest a main figure panel. Also, is JUNI upregulated across tumors? Could find this out from GEPIA2 or other databases.

Response: Figure 7E describing the levels of JUNI in variety of normal and tumor samples was added.

Non-tumor cells: Like many studies, this one focusses on effect of LOF in transformed cells. However, therapeutic relevance is tied to specific effect in transformed cells. Therefore I believe the paper would be vastly strengthened, if knockdowns+viability assays were also performed in some non-transformed cells. Eg HEK293, immortalised fibroblasts, RPE1 etc

Response: Indeed discrimination between Normal and cancer cells is an essential point for further research and translation. We examined the affects of silencing on spontaneously immortalized keratinocytes, HaCat cells, and the results are depicted in Figure 4 K.

Alternative reagents: The siRNA experiments are well performed with two independent sequences. An important additional experiment would be to replicate these experiments with antisense oligonucleotides. This would both further strengthen the confidence in experiments, and open more lines of potential therapies. This experiment I would consider optional

Response: Stable CRISPR can not be formed. We are currently constructing inducible CRISPR but the construction consumes longer time than the scope of this revision.

Advanced models: All the present experiments are performed in monolayer cell lines. The authors will no doubt be aware that the paper would be substantially strenghtened if functional experiments could be replicated in more advanced models: spheroids, PDX, explants, mice...

Response: We examined the protective role of JUNI in Doxorubicin treated spheroids of HMCB and CHL1 cells. The results are depicted in figure 4 D and E.

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Referee #3

Evidence, reproducibility and clarity

Kumar and colleagues present an apparently novel, cancer-promoting lncRNA 'JUNI' and perform a rather thorough and careful analysis of its in vitro functions and molecular mechanisms.JUNI is located adjacent to the Jun protein coding gene, although intriguingly the two appear to be rather indepent of each other at the level of gene products. JUNI appears to be necessary for cancer cell line growth and survival (monolayer) in multiple contexts. Particularly interesting is the demonstration that JUNI appears to function in trans. Overall this is an excellent paper - work is solidly and carefully done, hypotheses are well formulated and thoroughly tested. The JUNI lncRNA is well supported in public annotations, seems to be highly expressed, and it is surprising that virtually no work has been carried out on it so far. Furthermore, the apparently essentiality of JUNI to cancer cells has potentially important therapeutic and mechanistic ramifications.

These are suggestions for improvement of the work.

"linc01135" - this is a human gene, should be capitalised.

Please indicate primers and ASOs in Fig1A and mention this in relevant part of Results.

Fig1C-F - please add a legend to explain the colors.

Copy number: It is important to establish the approximate copy number of JUNI RNAs in the cell lines tested. FISH would be one appropriate method. This could also be referenced back to the RNA-seq TPM values. Are we talking about <1 copy /cell, or many? Quick inspection of ENCODE RNA-seq in the UCSC browser suggest an intermediate value that varies between cell lines. This value is very important when interpreting mechanistic experiments later on.

Fig3 - again, no figure legends, difficult for reader.

In general, the figures could be much more clearly annotated and presented with more care. They do not do justice to the quality of the work itself. For example, Fig4E-G why not label each panel with the time course, the cell line tested etc etc to save us the work of digging through the Legends?

Rescue experiments: The rescue experiments in Fig5D are nicely done and the results are interesting. However, I would request the authors to perform similar experiments with JUNI rescue. Specifically, to knock down JUNI with siRNA, and then reintroduce it from an 'immune' expression plasmid, where the siRNA site is mutated. This will further strengthen the claim that JUNI siRNA is acting through the intended target to cause observed effects on cell viability.

IncPrint data: was Jun protein found to be an interactor? This might be mentioned in the text, whether it is yes or no.

Expression: A key issue is the expression of JUNI in healthy and diseased cells and organs. Is JUNI ubiquitous (and essential to both healthy and tumor cells), or is it specific to tumor cells? Which tumor types? This would be straightforward to find out from public data. I would suggest a main figure panel. Also, is JUNI upregulated across tumors? Could find this out from GEPIA2 or other databases.

Non-tumor cells: Like many studies, this one focusses on effect of LOF in transformed cells. However, therapeutic relevance is tied to specific effect in transformed cells. Therefore I believe the paper would be vastly strengthened, if knockdowns+viability assays were also performed in some non-transformed cells. Eg HEK293, immortalised fibroblasts, RPE1 etc.

Alternative reagents: The siRNA experiments are well performed with two independent sequences. An important additional experiment would be to replicate these experiments with antisense oligonucleotides. This would both further strengthen the confidence in experiments, and open more lines of potential therapies. This experiment I would consider optional.

Advanced models: All the present experiments are performed in monolayer cell lines. The authors will no doubt be aware that the paper would be substantially strenghtened if functional experiments could be replicated in more advanced models: spheroids, PDX, explants, mice...

Significance

This is an important advance in the cancer field. It reveals a potential new lncRNA oncogene, JUNI, which appears to be necessary for cancer cell survival in multiple contexts through mechanisms defined by the authors. Future work will be required to understand the degree to which JUNI's activity is cancer specific, and its functional effects will have to be replicated in more faithful cancer models.

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Referee #2

Evidence, reproducibility and clarity

This work identified a lncRNA JUNI located near c-JUN and investigated its relationships with c-JUN and stress response, survival, and cancer prognosis. Experiments are logically designed, and the research topic is novel. The main concern is weaknesses in data interpretation and significance. Additionally, the paper needs improvement in experimental rigor with statistical assessment of multiple data sets; data description and conclusion need better clarity.

Overall comments:

1. While the experimental data showed JUNI, like c-JUN, is pro-survival of cancer cells, the clinical sample analyses correlated it positively with patients' survival. This discrepancy casts doubts in significance of the findings. The authors need to re-evaluate their data and conclusion.
2. The Western blotting data need at least triplicate biological experiments and quantification. This is particularly important for trivial differences, such as shown in Fig. 6.

Specific comments:

1. The identification and gene structure of LINC01135 and its relevance to c-Jun need better clarity.
2. Page 9-10, Line 198-199, there are no results in Fig. 1 showing that JUNI induction was dependent to serum stimulation of starved cells.
3. What is the Y-axis in figures 2B, 4E-G
4. In Fig. 3B, actin image is missing.
5. In Fig. 4. brightfield images are inaccurate for distinguishing apoptosis and necrosis. Additional molecular markers need to be used, such as caspase-3 cleavage and LDH release.
6. The inconsistency of using four cell types in each assay. For example, in Fig. 4A, B, E-G and Suppl Fig. 1, HMCB, MDA-MB-231 and CHL1 cells were used to test the short-term effect of JUNI knockdown on cell survival, whereas Hela, MDA-MB-231 and CHL1 cells were chosen to determine the long-term effect of JUNI knockdown. Similar case in other figures.
7. In Fig. 5D, no difference of c-Jun expression between NS and siJUN groups.
8. Cell survival in Fig. 5 lacked statistical analyses
9. In Suppl Fig. 2C, there is no figure to show the reduced colonies formation in soft agar in MDA-MB-231 cells, contradicting to that stated in the manuscript.

Significance

Experiments are logically designed, and the research topic is novel. The main concern is weaknesses in data interpretation and significance. Additionally, the paper needs improvement in experimental rigor with statistical assessment of multiple data sets; data description and conclusion need better clarity.

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Referee #1

Evidence, reproducibility and clarity

The author investigated the role of the stress sensor pathway in the mechanism of tumor cell survival<br /> They identified a long noncoding RNA as JUNI that regulates antagonizing MAP phosphatase and favors the JUN transcription. JUNI correlated with the survival of several cancer histotypes, particularly in RCC, as a highly specific and correlated prognosis.

The abstract although not always required from the journal should be divided into methods used to reach the main findings and clear presentation of results it is unclear whether JUNI is a positive or negative regulator of JUI. When the author indicates that JUNI antagonizes MAP PHOSPHATASE is not correct the term antagonism is related to receptors but the authors did not show any receptor. Correlated with prognosis ( negative or positive ) Statistical value should be reported in the abstract. Generally, Jun oncogene correlated with poor overall survival while the table indicates promote survival so good prognosis?

Major comments

The introduction contains the main information to follow the role of JUN and renal carcinoma<br /> However, should be improved with background on the key role of stress genes in the pro-survival pathway of tumors during progression and hypoxia condition. Too many references on long noncoding compared to the JUN complex with AP-1 and transformation.<br /> Results In Figure 1 the authors showed expression levels of JUNI and JUN that are clearly different after UV stimuli they demonstrate that are both regulated by UV but the amount and the time are different the author should comment on these data if they want to study the regulative mechanism figure 1 F the cellular distribution of JUNI which is the rational of this experiment to provide that is into nucleus while normally is into the cytoplasm? What adds this experiment?<br /> In Figure 2 the authors provided that the kinase pathway is important for Jun regulation but the effect on JUNI a Luciferase assay needs to be provided<br /> In Figure 3 for Migration assay is necessary to see cells on the other side of the filter by staining not a graphical representation the experiment on kinase does not add any data to what is already known on jun probably should be shifted in Figure 6. Table 1 is cited two times once in the context of Figure 3 and then in Figure 6 indicating that the authors go forward and back on their experimental design<br /> in figure 4 the apoptotic cells are not clearly visible a specific staining marker is necessary to provide the phenomenon additionally XTT assay should be reported as the percentage of survival cells not staining incorporated compared to untreated cells over time.<br /> The data on prognosis and correlation of gene expression are not clearly presented and discussed

Significance

The authors identified a long noncoding RNA as JUNI that regulates antagonizing MAP phosphatase and favors the JUN transcription. JUNI correlated with survival of several cancer histotypes In particular in RCC as a highly specific and correlated prognosis.

The data are not presented with a good rationale often the authors go forward and back on the experimental design. The data are not presented in the best way some data are shown as bar graph but need to be supported by cell staining of transwell staining and standard plot for survival rate The western blot need to be quantified

In general, the experimental design does not match the rational

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Reply to the reviewers

_We have underlined the important points in the reviewer's comments. All responses have been read and authorized by all authors of this manuscript. Authors would like to thank the reviewers and the editor for their valuable time. We believe that the comments and suggestions from both reviewers will significantly improve SMorph and the manuscript. _

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

First of all, I want to apologize the authors and editor for my delay. Secondly, for clarity, I want to disclose that I am the author of the Fiji's 'Sholl Analysis' plugin, that the authors cite extensively (Ferreira et al, Nat Methods, 2014).

In this study, Sethi et al introduce a software tool - SMorph - for bulk morphometric analysis of neurons and glia (astrocytes and microglia), based on the Sholl technique. The authors compare it to the state-of-the-art in a series of validation experiments (stab wound injury), to conclude that it is 1000 times faster that existing tools. Empowered by the tool, the authors show that chronic administration of a tricyclic antidepressant (DMI) leads to structural changes of astrocytes in the mouse hippocampus. The paper is well written, the description of the tool is clear, and the authors make all of the source code available, as well as most of the imagery analyzed in the manuscript. The latter on its own, makes me really appreciative of the authors work.

We thank reviewer #1 for their careful reading of the manuscript and their comments.

**Major comments:**

A major strength of SMorph is that it leverages the Python ecosystem, which allow the authors take advantage of powerful python packages such as sklearn, without the need for external packages or tools. However, I have strong criticisms for the claims that are made in terms of speed and broad-applicability of the software, including PCA.

Speed:

The 1000x speed gains, assumes - for the most part -- that the processing in Fiji cannot be automated. This is false. I read the source code of SMorph, and with exception of the PCA analysis, all aspects of SMorph can be automated in Fiji, using any of Fiji's scripting languages to make direct calls to the Fiji and Sholl Analysis plugin APIs (See https://javadoc.scijava.org/) . Now, perhaps the authors do not have experience with ImageJ scripting, or perhaps we Fiji developers failed to provide clear tutorials and examples on how to do so. Or perhaps, there is something inherently cumbersome with Fiji scripting that makes this hard (e.g., there is a current limitation with the ImageJ2 version of 'Sholl Analysis' that does not make it macro recordable). It such limitations do exist, it is perfectly fine to mention them, but do contact us at https://forum.image.sc, if something is unclear. We do strive to make our work as re-usable as possible. Unfortunately our own research does not always allow us the time required to do so. Case in point, our scripting examples (e.g., https://github.com/tferr/ASA/blob/master/scripting-examples/3D_Analysis_ImageStack.py; https://github.com/tferr/ASA/blob/master/scripting-examples/3D_Analysis_ImageStack.py) are not well advertised. That being said, I am still surprised that in their side-by-side comparisons the authors were not able to automate more the processing steps (e.g., the ImageJ1 version of 'Sholl Analysis' remains fully functional and is macro recordable). If I misunderstood what was done, please provide the ImageJ macros you used. Also, I wanted to mention that i) semi-manual tracing with Simple Neurite Tracer (now "SNT"), can also be scripted (see https://doi.org/10.1101/2020.07.13.179325); and that ii) Fiji commands and plugins can also be called in native python using pyimagej (https://pypi.org/project/pyimagej/), see e.g., https://github.com/morphonets/SNT/tree/master/notebooks#snt-notebooks). Arguably, the fact that SMorph handles blob detection and skeletonization-based metrics directly is more advantageous from a user point of view. In Fiji, blob detection, skeletonization and Strahler analysis (https://imagej.net/Strahler_Analysis) of the skeleton are handled by different plugins. However, those are also fully scriptable, and interoperate well. The point that topographic skeletonization in Fiji can originate loops is valid, however the authors should know that such cycles can be detected and pruned programmatically using e.g., pixel intensities (see https://imagej.net/AnalyzeSkeleton.html#Loop_detection_and_pruning and the original publication (https://pubmed.ncbi.nlm.nih.gov/20232465/)

We completely agree with the reviewer’s assertion that most parts of the functionality of SMorph can be automated within imageJ as well, and in such comparison, the speed gains with SMorph will not be >1000X.

However, automating the analysis in imageJ is beyond the scope of the present manuscript. In fact, imageJ analysis comparison was not a part of our original manuscript at all. Upon presubmission inquiry to one of the affiliate journals of Review Commons, we were specifically asked to include a side-by-side comparison with “already available” methods. So, we decided to use ImageJ as it is, and automation, if any, was limited to simple macros to run a series of commands sequentially on batches of images. Although it is true that this analysis could be done much more efficiently with additional scripting, it would not have met the definition of “already available” tools. The imageJ analysis was performed in a way an average biologist with no programming experience would perform it, since that group will find SMorph most useful. In no way do we intend to imply that imageJ analysis can’t be made more efficient and automated. Perhaps it was not clear from the way the text was framed in the initial version of the manuscript. We will add additional text to make this point clearer.

On a side-note, in response to reviewer #2’s comments, we will perform the speed comparison on a per-image basis, so the speed gain (1080X) may change a little in the new comparison.

Broad applicability:

In our work, we made a significant effort to ensure that automated Sholl could be performed on any cell type: e.g., By supporting 2D and 3D images, by allowing repeated measures at each sampled distance, and by improving curve fitting. For linear profiles, we implemented the ability to perform polynomial fits of arbitrary degree, and implemented heuristics for 'best degree' determination. For normalized profiles, we implemented several normalizers, and alternatives for determining regression coefficients. We did not tackle segmentation of images directly (we did provide some accompanying scripts to aid users, see e.g. https://imagej.net/BAR) because in our case that is handled directly by ImageJ and Fiji's large collection of plugins. However, in SMorph, several of these parameters are hard-wired in the code. They may be suitable to the analyzed images, but they can be hardly generalized to other datasets. In detail: In terms of segmentation, SMorph is restricted to 2D images, scales data to a fixed 98 percentile, and uses a fixed auto-threshold method (Otsu). These settings are tethered to the authors imagery. They will give ill results for someone else using a different imaging setup, or staining method. In terms of curve fitting, the polynomial regression seems to be fixed at a 3rd order polynomial, which will not be suitable to different cell types (not even to all cells of 'radial morphology').

We have indeed hard-coded the parameters that the reviewer mentions, and we agree that we can perhaps give all options to the end-users to choose from. The decision was made to hard-code the parameters so that SMorph becomes very easy and minimalistic to use for the end-users. But the reviewer is right to point out that this may compromise the broad applicability and accuracy. We will update the code in the revised version of the manuscript to give the users control over choosing these parameters.

PCA:

The idea of making PCA analysis of Sholl-based morphometry accessible to a broader user base has merit and is welcomed. However, it has to be done carefully in a self-critic manner as opposed to a black-box solution. E.g., in the text it is mentioned that 2 principal components are used, in the tutorial notebook, 3. Why not provide intuitive scree plots that empower users with the ability to criticize choice? Also, it would be useful for users to understand which metrics correlate with each other, and their variable weights.

Reviewer #1’s suggestions would indeed make the PCA analysis more useful to the users. In the revised version of the code, we will provide additional data/plots to the user for making an informed choice of the significant principal components e.g. the elbow method, Ogive or Pareto plots, variable weights of different features in the principal components and correlation/covariance matrices.

When we showcased the utility of PCA to distinguish closely related morphology groups (as in Type-1 and Type-2 PV neurons), we had been unable to base the distinction on individual metrics, at least not in a robust manner (see Fig. S4 in Ferreira et al, 2014). A minor conundrum of the paper, is that it does not directly highlight the advantages of "analyzes in a multidimensional space". The differences between groups in the stab wound and DMI assays are such, that PCA is hardly needed: I.e., the differences depicted Fig2F,G are already significant, and already convey changes in "size and branch complexity" (as per PC1). The same argument applies to Fig. 5. The paper would profit from having this discussed.

PCA data indeed is not required to make any of the inferences we make in the paper and is superfluous. However, as mentioned in the discussion section of this manuscript, the low-dimensional PCA data can be used in future for other applications, e.g to cluster the astrocytes into morphometrically-defined subpopulations. SMorph can be further developed to perform real-time classification of these cells into morphometric clusters, which will allow the researchers to investigate clusters-specific gene expression, electrophysiology etc. Preliminary results from our lab do suggest that such clusters are differentially altered by stress and antidepressant treatments. However, these results are preliminary and are a part of a long-term future study. The data is really premature to publish at this stage, since it will require a lot of experimentation to show that these astrocyte subpopulations are indeed physiologically and functionally different. Nevertheless, we think that the utility of SMorph for such analyses may help others to come up with additional innovative ways to use the PCA data. Hence, we do believe that the community will benefit from the current release of SMorph having PCA. PCA data was shown in the figures just to demonstrate the functionality of SMorph. We will add additional text to make these points clearer.

Other:

- All metrics and parameters should be expressed in physical units (e.g.," radii increasing by 3 pixels", axes in Figure 2, 3, 5, S2) so that readers can directly interpret them.

In the revised manuscript, we will convert all units into actual physical distances.

- The paper would profit from the insights provided by Bird & Cuntz (https://pubmed.ncbi.nlm.nih.gov/31167149/)

We thank the reviewer for suggesting this paper. We will include this in the discussion of the manuscript.

**Minor comments:**

- Usage of RGB images (8-bit per channel) seems hardly justifiable. Aren't you loosing dynamic range of GFAP signal?

We agree that we could have captured the images at a higher dynamic range. However, for the changes we observe between treatment groups using GFAP immunoreactivity signal as presented in the manuscript, we do not see an advantage of using higher dynamic range. However, as the reviewer rightly pointed out, under certain conditions, imaging using a higher dynamic range may help and hence, we will include this recommendation in the materials and methods section.

- Please explain how MaxAbsScaler "prevents sub-optimal results"

Since morphometric features extracted from cell images either have different units or are scalar, we had to perform normalization before PCA. We will add further explanation in the methods section of the manuscript.

- The fact that automated batch processing can stall on a single bad 'contrast ratio' image seems rather cumbersome to deal with

This problem has been resolved in the current version of SMorph, which will be uploaded with the revised version of the manuscript.

- Please add a license to https://github.com/parulsethi/SMorph/. Without it, other projects may shy away from using SMorph

We will add a ____GPLv3 license

- "mounted on stereotax" should be "mounted on a stereotaxis device"?

We will make this change

- Ensure Schoenen is capitalized

We will make this change

Reviewer #1 (Significance (Required)):

I find the Desipramine results interesting. However, given the existing claims that DMI can modulate LTP, I regret that the authors did not look at structural modifications in hippocampal neurons (e.g., by performing the experiments in Thy1-M-eGFP animals). I understand, that doing so at this point would be a large undertaking.

Another manuscript from our lab__1, as well as work from other labs have shown that stress causes significant degenerative changes in hippocampal astrocytes__2,3__. In the light of these observations, we do believe that our observation of chronic antidepressant treatment inducing structural plasticity in astrocytes is significant. Structural alterations in neurons after DMI treatment are of interest. But in our experience, we have not seen gross morphological (dendritic arborization) changes in hippocampal neurons as a result of antidepressant drug treatments. Such changes are restricted to spine morphology and axonal varicosities, which is beyond the capabilities of SMorph. __

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

This paper addresses the challenge of automatic Sholl analysis of large dataset of multiple cell types such as neurons, astrocytes and microglia. The developed approach should improve the speed of morphology analysis compared to the state of the art without compromising on the accuracy. The authors present an interesting application of their tool to the morphological analysis of astrocytes following chronic antidepressant treatment. The paper is well written, and the tool presented could be beneficial for different applications and context. However, some major aspects should be addressed by the author concerning the description of the algorithms used and the quantification of the results.

We thank reviewer #2 for their careful reading of the paper and their comments.

**Major comments/Questions:**

1. In the Results and/or Methods sections, the author should better describe how their approach is different from state-of-the-art approaches in terms of algorithms used and how these difference impacts on the speed and accuracy of the analysis.

We will add these descriptions in the methods section in response to this comment as well as some comments from reviewer #1.

Imaging was performed on a Zeiss LSM 880 airyscan confocal microscope. Is this method robust to other types of imaging techniques, other microscopes, variable levels of signal-to-noise? This should be tested and quantified.

We will demonstrate the results obtained from images taken using different microscopes and imaging techniques, and quantify the outcome.

Manual cropping of the cells with ImageJ was used. However, in the methods section, the authors mention that other machine learning tools could be used for this task. Why were these tools not implemented in this paper in order to propose a fully automated analysis approach in combination with SMorph?

We have tried both the machine learning tools cited in this paper (one for DAB images and other for confocal images). However, in our experience, we do not get robust performance from these tools with our datasets, and these tools will perhaps need more optimization for broad applicability. We are developing an auto-cropping tool in-house, but that is beyond the scope of the current study. Another point is that these tools are tailor-made for astrocytes, and their integration into SMorph will restrict its applicability to just one cell type.

In the methods section you state that cropped cells need to have a good contrast ratio for automated batch processing. Could you define what a good contrast ratio is and characterize the performance of your approach for different contrast ratio?

In the revised manuscript, we will compare the images taken from multiple microscopes and quantify the outcome. We will change the text accordingly. As such, the comment on rejected cells referred to really poor quality images. In the revised manuscript, we will make specific recommendations on imaging parameters so that this should not be an issue at all.

It is mentioned that the analysis routine can be interupted by a cell with lower contrast ratio. This is a major drawback of the approach (but I think that it could be easily improved), as such interruptions may not be= practicable for many applications that need to rely on automated processing.

We have already rectified this problem and the updated version of SMorph will be uploaded with the revised manuscript.

Also, you should precise how the contrast ratio should be enhanced without modifying raw data in order to be processed with your approach. You suggest removing cells with lower contrast ratio from the analysis, but can this impact on the findings especially if some treatments impact on the detected fluorescence signal? Can you propose ways to improve the robustness of your approach to variable signal ratios?

It is indeed possible that removing cells from analysis, may in certain cases, affect the results. To rectify this, we are testing the method on images obtained from different microscopes and under different imaging conditions. From these analyses, we will deduce minimum recommendations for imaging conditions so that images don’t have to be edited/altogether removed from analysis for the software to work. In the materials and methods section, we will add these recommendations to the users on the optimal range of imaging parameters. This way, rejection/modification of images should not be an issue.

In the Results section, you describe the time necessary to perform different analysis. However, giving a total time in hours is not very informative as this will likely vary a lot depending on the size of the dataset, complexity of the images, etc. You should compare the average time per image for both methods and types of analysis.

We compared the total time required for the entire dataset, since SMorph is meant for batch-processing all the images at once. However, we can change the comparisons to time taken per image. We can divide the total time taken by SMorph by the number of images analysed. However, in our opinion, the time taken to initiate SMorph will make these comparisons inaccurate.

You state that for the number of branch point, the lower value of the measured slope when comparing SMorph and ImageJ was related to a constant overestimation of this parameter with ImageJ. How was this quantified? I think you should stress out more the comparison of both approaches with the manually annotated dataset.

In the revised version of this manuscript, we will include some examples of skeletonized images that overestimate the number of forks. We have observed this to be a recurring problem with the skeletonization tools we have tried in imageJ. This can be rectified in imageJ itself as pointed out by reviewer #1. However, that’s beyond the scope of the present study and will not fit the definition of comparison with “already available” methods.

How can you explain the differences in the 2D-projected Area, total skeleton length and convex hull between SMorph and ImageJ, which all show a slope around 0.83? Can you quantify the performance of both methods by comparing them with your manually annotated dataset?

In the revised version, we will include the correlation data between completely manual and SMorph comparisons. We will discuss these comparisons further in the manuscript and make specific conclusions about the accuracy.

In the introduction and discussion, you mention that you present a method that works on neurons, astrocytes and microglia. However, I don't see in the paper the comparison between the accuracy for all these cell types as you seem to have analyzed only the morphology of astrocytes.

In the revised manuscript, we will include the Sholl analysis comparison (imageJ vs SMorph) from images of neurons and microglia.

You mention that your method is quite sensitive to variation in contrast ratio. You should quantify the contrast ratio throughout the experiments and ensure that this is not biasing the SMorph analysis for some of the treatments.

We thank both reviewers for highlighting this issue in the initial version of SMorph. As mentioned in our response to point #6, we will perform additional analyses to make specific recommendations to the end users regarding imaging parameters so that SMorph can work on images as they are. As such, our comments on contrast ratio applied only to very poor quality images. If images are acquired conforming to the imaging parameters we will recommend in the revised manuscript, images can be analysed without any issues.

**Minor Points :**

1. Precise the exact inclusion and exclusion criteria for Soma detection and rephrase: "The high-intensity blobs were detected as a position of soma..." & "Boundary blobs coming from adjacent cells...".

We will add a complete explanation of blob detection and the exclusion criterion in the methods section.

Throughout the text, make sure to always refer to an analysis time per image or per cell and not only include absolute duration values without reference to the task at hand (e.g. in the discussion : SMorph took 40 second to complete the analysis... please state to which analysis you are exactly referring to and if applicable if it varies from cell to cell).

We will change all comparisons to time taken per cell. Text will be added to mention which datasets were used when any claims of speed are made.

When you state in the discussion that "Although some methods do allow Sholl analysis without manual neurite tracing, they still work on one cell at a time", please precise if the only aspect that is missing from this type of analysis is batch processing (looping through the data) or if there is a major obstacle to automate this technique. This is important a SMorph does proceed with the analysis one cell at a time but can work in a loop/batch.

We will elaborate further on our assertion regarding the challenges of using imageJ plugins for sholl analysis in large batches of cells.

Reviewer #2 (Significance (Required)):

This tool could very useful to researchers in the field of cellular neuroscience working with high-throughput analysis of microscopy data. The authors show some interesting improvements over existing methods. An improved quantitative characterization of the robustness of their approach would be of great importance to ensure the significance of this tool to a large community of researchers using different types of microscopes or studying different cell types.

My expertise is in the field of optical microscopy and high-throughput (automated) image analysis for neuroscience. My expertise to evaluate the biological findings in this study is very limited.

We thank reviewer #2 for their careful reading of the manuscript and their insightful comments. Growing evidence (clinical and preclinical) shows a significant reduction in astrocyte density in key limbic brain regions as a result of depression. We believe that the structural plasticity induced by chronic antidepressant treatment, as demonstrated in this manuscript, is an interesting novel plasticity mechanism that can negate deleterious effects of stress on astrocytes.

The improvements suggested by both reviewers will help us to greatly improve SMorph in the revised version of this manuscript.

References:

1. Virmani, G., D’almeida, P., Nandi, A. & Marathe, S. Subfield-specific Effects of Chronic Mild Unpredictable Stress on Hippocampal Astrocytes. doi:10.1101/2020.02.07.938472.
2. Czéh, B., Simon, M., Schmelting, B., Hiemke, C. & Fuchs, E. Astroglial plasticity in the hippocampus is affected by chronic psychosocial stress and concomitant fluoxetine treatment. Neuropsychopharmacology 31, 1616–1626 (2006).
3. Musholt, K. et al. Neonatal separation stress reduces glial fibrillary acidic protein- and S100beta-immunoreactive astrocytes in the rat medial precentral cortex. Dev. Neurobiol. 69, 203–211 (2009).

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Reply to the reviewers

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

**Summary:**

-The authors have carried out an extensive survey of dorso-ventral axis determination in the cricket Gryllus bimaculatus. They did this through analysing and knocking down key components of the two main pathways involved in D/V patterning, the toll pathway and BMP signalling. This analysis was placed in a comparative context, looking at published data on four other insect species, with the aim of contributing to our understanding of the evolution of D/V patterning.

-The authors find significant similarities between D/V patterning in Gryllus and in Drosophila - These similarities are both in the relative contributions of toll and BMP to D/V polarization and in the early ovarian activation of the toll pathway. Despite these similarities, a closer analyses of the molecular interactions uncovers some significant differences, most notably, the absence of several key modulators of BMP activity. These results lead the authors to conclude that the similarities in D/V patterning between Gryllus and Drosophila are due to convergence and not due to the conservation in Drosophila of an ancestral patterning mechanism that has been lost in almost all other lineages studied.

**Major comments:**

•All in all this is an excellent paper. There is a huge amount of data in here, and everything is done very meticulously and carefully. There is a good balance between mostly descriptive work (gene expression patterns, cell movements in WT embryos) and experimental work. I could find no obvious flaws with any of the results or methods, and I think the authors have made a convincing case to support their conclusions, without being too dogmatic.

•I don't see a need for any additional experiments beyond what the authors have done. They have covered all relevant aspects of D/V patterning, and make a convincing case with the data they have.

**Minor comments:**

The few comments I have are very minor and technical:

•Missing taxonomic names (families) in Fig. 1

•Missing label in Fig. 6 Panel A.

•Punctuation could be improved. There are several instances of missing commas, and other places with unnecessary commas.

*Reviewer #1 (Significance (Required)):

•The manuscript represents an admirable amount of work. One can say that in a single paper, the authors have provided nearly as much information about Gryllus D/V patterning as is available for other "second-order" insect model species such as Oncopeltus or Nasonia. A such, it provides an additional major phylogenetic anchor point for understanding the evolution of early patterning.

•In terms of significance to advancing our knowledge, the data in the manuscript is, as stated above, an anchor point. It does not on its own provide any major novel insight, but fits into an ever-expanding body of comparative knowledge, whose importance is greater than the sum of its parts. Perhaps the most interesting conclusion, is indeed the one the authors have chosen as the selling-point of their paper, the fact that there is functional convergence in certain aspects of D/V patterning between two widely diverged insect species, with very different oogenesis and early development. This is again, not a major advance on its own, but an important additional piece of the comparative picture of early insect development.

•This paper will be of significant interest to the research community of comparative insect development (the community to which this reviewer belongs). It will also be of interest to those interested in examples of convergence at the functional and molecular level, to those interested in the evolution of gene families and to those interested specifically in the signalling pathways discussed (even in a non-comparative context).*

Response

We thank the reviewer for the very positive response to our paper.

We added missing taxonomic names and labels in Figure 6A and improved the punctuation throughout the manuscript.

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

In this paper Pechmann and colleagues investigate the molecular mechanisms of dorso-ventral patterning in Gryllus bimaculatus. As a basis for their study they carry out thorough RNAseq analyses of various embryonic stages. Gryllus is a member of the hemimetabolous insects and therefore of interest for comparison with holometabolous insects such as Drosophila, Tribolium and Nasonia. Previous work has shown that there are significant differences in the use of Toll and Sog in establishing the dorso-ventral gradient of BMP signaling among Drosophila and Nasonia. Pechmann et al find that in Gryllus Toll has a similar role as in Drosophila and is regulated via Pipe, so far only found in Drosophila. Furthermore, they show by RNAi knockdown studies that loss of BMP signaling has little impact on the differentiation of mesoderm in Gryllus, like in Drosophila, hence, BMP signaling has largely a role in dorsal fates. Ventral fates are under direct control of the Toll gradient. Surprisingly, they also find that the key antagonist of BMP signaling and shuttle for BMPs, Sog, has been lost in Ensifera, the lineage leading to Gryllus.

This is a thorough and detailed study involving a series of functional experiments, which highlights the flexibility and evolvability of GRN of the dorso-ventral body axis formation in insects. The major finding that Gryllus is more similar to Drosophila than is Nasonia and Tribolium is interesting and even somewhat unexpected, since Drosophila is often regarded as the derived odd ball. The authors discuss two obvious explanations: the situation found in Gryllus and Drosophila reflects the ancestral condition, or, alternatively, it is the result of convergent evolution. They tend to favor the latter hypothesis. This study is an important advancement to our understanding, as it shows the constraints and the evolvability of a key patterning system to establish a body axis.

Even though the authors show nicely that Toll signaling is required to establish the BMP signaling gradient, the loss of Sog in Gryllus leaves the question unanswered how the long range BMP gradient and its shape is established. In Drosophila and vertebrates, Sog/Chordin acts both as an antagonist close to its source and as a shuttling factor, promoting BMP signaling at a distance, which is crucially important for the long range and the shape of the BMP signaling gradient. It would be desirable to test the function of other potential BMP antagonists (follistatin, gremlin, noggin) or competing BMPs (BMP3, ADAMP) in this context.

As a minor suggestion, I would recommend to summarize the findings in a synthetic picture depicting the evolutionary scenarios of the two hypotheses.

Reviewer #2 (Significance (Required)):

This study is an important advancement to our understanding, as it shows the constraints and the evolvability of a key patterning system to establish a body axis.

Response

We thank the reviewer for the very positive response to our paper.

As the reviewer suggested we added a schematic representation (Figure 11) depicting the two scenarios, which explain the evolution of DV patterning.

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

**Summary**

This manuscript continues a series of beautiful papers from Roth, Pechman, Lynch and colleagues analysing D/V patterning in a range of insects. The work started with Drosophila and has extended to other holometabolous and now hemimetabolous insect species.

This paper is in many ways one of the most remarkable of the series, for it shows that the mechanisms of D/V patterning in the cricket Gryllus are, in several striking respects, very similar to those known from Drosophila - much more so than in some of the other insects studied to date, even though Gryllus is phylogenetically the most distant from Drosophila.

Specifically, the authors present compelling data to show that the roles of Toll and dpp, as inferred from their knockdown phenotypes, are remarkably similar in Gryllus and Drosophila. This is very different from the consequences of toll and dpp knockdown in the hemipteran Oncopeltus, a species which almost certainly shares a more recent common ancestor with Drosophila.

The discussion, after summarising the results, addresses the interpretation of this surprising observation. The authors favour the hypothesis that the similarity between Drosophila and Gryllus is the result of convergence in the roles and regulation of Toll and dpp signalling, rather than an ancestral trait that has been lost to a greater or lesser extent in Oncopeltus, and in the two other insects previously studied. The argument for this interpretation is carefully made, on the basis of a thorough knowledge of the comparative embryological literature (including highly relevant recent work).

**Major comments**

The work depends on an analysis of candidate genes, not de novo functional searches. However, it builds on the well established understanding of the relevant genetic machinery in Drosophila, and on extensive knowledge of the genome and transcriptome of Gryllus, a dataset that has been substantially extended by new work reported in this paper, on ovary and embryonic transcriptomes. These data are sufficiently complete to give confidence that all orthologues of most of the known candidate genes have been identified, and to highlight the apparent absence from the Gryllus genome of any sog/chordin orthologue - a key dpp inhibitor widely involved in D/v patterning.

The embryology is beautifully described. The early stages of these very yolky eggs are not easy to handle, but the stainings reported here are almost all of high quality, as are the movies of live development using a nuclear GFP marked line.

The gene knockdowns appear to have been carried out carefully with due regard for the potential biases caused by sterility following parental RNAi. Phenotypes have been documented effectively by the expression of marker genes in fixed embryos, and by live imaging of development in knockdown embryos. Tables in the supplementary data show that sufficient numbers have been obtained. The work is carefully interpreted, and where inferences are less than certain, they are carefully phrased.

I find the results convincing, and therefore accept the conclusion of fundamental similarity between the roles of Toll and dpp in Drosophila and Gryllus.

Time will tell whether or not the authors favoured interpretation of these data as convergent is correct, but I certainly believe that the argument as here presented in the discussion is appropriate for publication in its current form. The abstract is, appropriately, more non-committal than the discussion itself on the interpretation of these results.

The paper is well written.

**Minor points**

Videos - please state orientation of the embryos, especially in videos 2 &4

Page 23 bottom "The early dorsal-to-ventral gradient of pMad (Figure 5AB) indicates that BMP signalling plays an important role ...." suggests would be better than indicates here, until functional data is considered.

Reviewer #3 (Significance (Required)):

The gene networks mediating patterning of the D/V body axis are related across the whole range of animals, with in particular the involvement of TGFb/dpp signalling being almost universal in this process. However, there are a great many variations on this theme. Even within the insects, the mechanisms that have been described for establishing localised TGFb and Toll signalling span the range from self organisation to effective maternal prelocalisation. This has made the GRN underlying D/V patterning a key model for studies of the evolution of gene regulatory networks.

This paper adds an interesting and important twist to the story. It is certainly not the result that any of us would have expected, based on prior published work from Oncopeltus.

If indeed it does turn out to be a case of convergence, a more detailed mechanistic analysis of that convergence will provide considerable insight into the reproducibility of evolution.

Other published work: There is no comparable work on D/V patterning in any other polyneopteran insect, to my knowledge.

Audience: Insect developmental biologists, evolutionary developmental biologists and others interested in the evolution of gene regulatory networks.

My expertise: Arthropod embryology, axial patterning, evolutionary developmental biology.

I have not reviewed in detail the presentation of the transcriptomic data and the phylogenetic analysis of gene sequences as presented in the supplementary info.

Response

We thank the reviewer for the very positive response to our paper.

We made the small textual corrections suggested by the reviewer.

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Reply to the reviewers

Overall, we were pleased that the reviewers found our study carefully designed and interesting. We have addressed their comments below.

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

The manuscript by Kern, et al., demonstrates that phagocytosis in macrophages is regulated in part by the intermolecular distance of phagocytosis-promoting receptors engaging phagocytic targets. Cells expressing chimeric receptors containing cytosolic domains of Fc receptors (FcR) and defined ligand-binding DNA domains were used to drive phagocytosis of opsonized glass beads coated with complementary DNA ligands of defined spacing and number. These so-called origami ligands allowed manipulation of receptor spacing following engagement, which allowed the demonstration that tight spacing of ligands (7 nm or 3.5 nm) optimized signaling for phagocytosis. The study is carefully performed and convincing. I have a few technical concerns and minor suggestions.

1. __ It is assumed that the origami preparations were entirely uniform. How much variation was there? Is that supported by TIRF microscopy of origami preparations? Was the TIRF microscopy calibrated for uniformity of fluorescence (ie., shade correction)?__ Our laboratory, Dong et al., has extensively characterized the origami uniformity and robustness of these exact pegboards. This paper was just posted on bioRxiv (Dong et. al, 2021). We have also cited this paper in our revised manuscript in reference to the characterization of the DNA origami (Line 117).

We did not use any shade correction. Instead we only collected data from a central ROI in our TIRF field. To check for uniformity of illumination, we plotted the origami pegboard fluorescent intensity along the x and y axis. We observed very modest drop off in signal - the average signal intensity of origamis within 100 pixels of the edge is 76 ± 6% the intensity of origamis in a 100 pixel square in the center of the ROI. Fitting this data with a Gaussian model resulted in very poor R values. While this may account for some of the variation in signal intensity at individual points, we expect the normalized averages of each condition to be unaffected. We have amended the methods to describe this strategy (Lines 851-854).

(Image could not be uploaded)

__ Likewise, how much variation was there in the expression of the chimeric receptors? Large variation in receptor numbers per cell could significantly alter the quantitative studies. Aside from the flow sorting for cells expressing two different molecules, how were cells selected for analysis?__

We thank the reviewer for bringing up this point. We confirmed comparable receptor expression levels at the cell cortex of the DNA CAR-𝛾 and the DNA CAR-adhesion used throughout the paper. We also have confirmed that receptor levels at the cell cortex were similar for the large DNA CAR constructs used in Figure 6C-D. This data is now included in Figures S5 and S7. We have also altered the text to include this (lines 169-172):

Expression of the various DNA CARs at the cell cortex was comparable, and engulfment of beads functionalized with both the 4T and the 4S origami platforms was dependent on the Fc𝛾R signaling domain (Figure S5).

When quantifying bead engulfment, cells were selected for analysis based on a threshold of GFP fluorescence, which was held constant throughout analysis for each individual experiment. We have amended the “Quantification of engulfment” methods section to convey this (lines 921-923).

__ The scale of the origami relative to the cells is difficult to discern in Figures 2C and D. Additional text would be helpful to indicate, for example, that the spots on the Fig. 2D inset indicate entire origami rather than ligand spots on individual origami particles.__

Thank you for pointing this out, we see how the legend was unclear and have corrected it (lines 453-454), including specifically noting “Each diffraction limited magenta spot represents an origami pegboard.” We have also outlined the cell boundary in yellow to make the cell size more clear.

__ Figure 5 legend, line 482: How was macrophage membrane visualized for these measurements?__

We have added the following clarification (line 535-536): “The macrophage membrane was visualized using the DNA CAR𝛾, which was present throughout the cell cortex.”

__ line 265: "our data suggest that there may be a local density-dependent trigger for receptor phosphorylation and downstream signaling". This threshold-dependent trigger response was also indicated in the study of Zhang, et al. 2010. PNAS.__

The Zhang et al. study was influential in our study design, and we wish to give the appropriate credit. Zhang et al. found that a sufficient amount of IgG is necessary to activate late (but not early) steps in the phagocytic signaling pathway. In contrast, our study addresses IgG concentration in small nanoclusters. We find that this nanoscale density affects receptor phosphorylation. Thus, we think these two studies are distinct and complementary.

Lines 283-287 now read:

While this model has largely fallen out of favor, more recent studies have found that a critical IgG threshold is needed to activate the final stages of phagocytosis (Zhang et al., 2010). Our data suggest that there may also be a nanoscale density-dependent trigger for receptor phosphorylation and downstream signaling.

__ line 55: Rephrase, “we found that a minimum threshold of 8 ligands per cluster maximized FcgR-driven engulfment.” It is difficult to picture how a minimum threshold maximizes something.__

We now state “we found that 8 or more ligands per cluster maximized FcgR-driven engulfment.”

__ line 184: Rephrase, "we created... pegboards with very high-affinity DNA ligands that are predicted not to dissociate on a time scale of >7 hr". Remove "not".__

Thank you for pointing this out, it is now correct.

Reviewer #1 (Significance (Required)):

This study provides a significant advance in understanding about the molecular mechanisms of signaling for particle ingestion by phagocytosis.

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

The manuscript on “Tight nanoscale clustering of Fcg-receptors using DNA origami promotes phagocytosis" studies how clustering and nanoscale spacing of ligand molecules for a chimeric Fcg-receptors influence the phagocytosis of functionalized silicon beads by macrophage cell lines. The basis of this study is the design of a chimeric Fc-receptor (DNA-CARg) comprising an extracellular SNAP-tag domain that can be loaded with single-stranded (ss) DNA, the transmembrane part of CD86 and the cytosolic part of the Fc-receptor g-chain containing an immunoreceptor tyrosine-based activation motif (ITAM) as well as a C-terminal green fluorescent protein (GFP). As control the authors used a similar designed DNA-CAR that is lacking the intracellular ITAM-containing FCg tail. The chosen target for this chimeric DNA-CAR, are silicon beads covered by a lipid bilayer that contains biotin-labelled lipids that, via Neutravidin, can be loaded with a biotinylated DNA origami pegboard displaying complimentary ss-DNA as ligand for the DNA-CAR. The DNA origami pegboard contains four ATTO647N fluorescence for visualization and the ssDNA ligand in different quantities and spacing. Using these principles, the authors study how ligand affinity, concentration and spacing influence the activation of the DNA-CARg and the engulfment of the loaded beads.

The authors show that bead engulfment is increased between 2 till 8 ssDNA ligands on the pegboard. After this, ligand numbers do not play a role anymore in the engulfment. They then study the role of the ligand spacing using pegboards that either contain 4 single strand DNA ligands in close (7nm/3,5nm) proximity or a more spaced version using 21/17,5 nm or 35/38,5 nm. The authors find that the bead engulfment is maximally and positively affected by the close spacing of the ssDNA ligands. In their final experiments the authors vary the design of the DNA-CARs by tetramerization of the ITAM-containing Fcg-signaling subunit. In their discussion the authors mention different possibilities for the effect of spacing on the engulfment process.

I think that, in general, this is an interesting study. However, it has some caveats and open issues that should be clarified before its publication.

**Major comments**

1. __ As a general comment, it is somewhat a pity that the authors did not use the endogenous FcR as a control. It would have been quite easy for the authors to place the SNAP-tag domain on the Fcg extracellular domain which would allow to do all their experiments in parallel, not only with the DNA-CAR, but also with a DNA-containing wild type receptor. Such a control would be important because, by using a CD86 transmembrane domain, the authors do not know whether the nanoscale localization of their chimeric receptors is reflecting that of the endogenous Fcg receptor.__

We agree with the reviewer completely. We have repeated experiments shown in Figure 4A with a DNA-CAR containing the Fc𝛾 transmembrane domain instead of CD86 as the reviewer suggests. We also included a DNA-CAR version of the Fc𝛾R1 alpha chain, although this construct was not expressed as well as the others. These data are now included in Figure S5, and referenced in lines 167-168.

__ An important issue that is discussed by the authors but not addressed in this manuscript is whether the different amount and spacing of the ligand is only impacting on signaling or also on the mechanical stress of the cells. Indeed, mechanical stress on the cytoskeleton arrangement could influence the engulfment process. For this, it would be very important to test that the different bead engulfment, for example, those shown in Fig. 4, is strictly dependent on signaling kinases. The authors should repeat the experiment of Fig. 4 a and b in the presence or absence of kinase inhibitors such as the Syk inhibitor R406 or the Src inhibitor PP2 to show whether the different phase of engulfment is dependent on the signaling function of these kinases. This crucial experiment is clearly missing from their study.__

We agree this is an interesting point. We find that ligand spacing affects receptor phosphorylation; however this does not preclude effects on downstream aspects of the signaling pathway. We will clarify this by adding the following comment to the manuscript (line 299-301):

While our data pinpoints a role for ligand spacing in regulating receptor phosphorylation, it is possible that later steps in the phagocytic signaling pathway are also directly affected by ligand spacing.

The DNA-CAR-adhesion in Figure 1 strongly suggests that intracellular signaling is essential for phagocytosis. We have now included additional controls using this construct as detailed in our response to point 3 below. Unfortunately, Src and Syk inhibitors or knockout abrogate Fc𝛾R mediated phagocytosis (for example, PMIDs 11698501, 9632805, 12176909, 15136586) and thus would eliminate phagocytosis in both the 4T and 4S conditions. This precludes analysis of downstream steps in the phagocytic signaling pathway.

__ Another problem of this study is that the authors show in Fig. 1A the control DNA-CAR-adhesion but then hardly use it in their study. For example, the crucial experiments shown in Fig. 4 should be conducted in parallel with DNA-CAR-adhesion expressing macrophage cells. This study could provide another indication whether or not ITAM signaling is important for the engulfment process.__

We have added this control. It is now included in Figure S5 and S7. Figure 3D also shows that the DNA-CAR-adhesion combined with the 4T origami pegboards does not activate phagocytosis and we have amended the text to make this more clear (line 152).

__ Another important aspect is how the concentration of the loaded origami pegboard is influencing the engulfment process. In particular, it would be interesting to show the padlocks with different spacings such as the 4T closed spacing versus 4s large spacing show a different dependency on the concentration of this padlock loading on the beads. This would be another important experiment to add to their study.__

We agree that this is an interesting question. We suspect that at a very high origami density, 4S signaling would improve, and potentially approach the 4T. However, we are currently coating the beads in saturating levels of origami pegboards. Thus we cannot increase origami pegboard density and address this directly.

**Minor comments:**

1. __ The definition of the ITAM is Immunoreceptor Tyrosine-based Activation Motif and not "Immune Tyrosine Activation Motif" as stated by the authors.__ We have corrected this.

__ The authors discuss that it is the segregation of the inhibitory phosphatase CD45 from the clustered Fc receptors is the major mechanism explaining their finding that 4T closed spacing is more effective than 4s large spacing. With the event of the CRISPR/Cas9 technology it is trivial to delete the CD45 gene in the genome of the RAW264.7 macrophage cell line used in this study and I am puzzled why they author are not conducting such a simple but for their study very important experiment (it takes only 1-2 month to get the results).__

This experiment may be informative but we have two concerns about its feasibility. First, CD45 is a phosphatase with many different roles in macrophage biology, including activating Src family kinases by dephosphorylating inhibitory phosphorylation sites (PMID 8175795, 18249142, 12414720). Second, CD45 is not the only bulky phosphatase segregated from receptor nanoclusters. For example, CD148 is also excluded from the phagocytic synapse (PMID 21525931). CD45 and CD148 double knockout macrophages show hyperphosphorylation of the inhibitory tyrosine on Src family kinases, severe inhibition of phagocytosis, and an overall decrease in tyrosine phosphorylation (PMID 18249142). CD45 knockout alone showed mild phenotypes in macrophages. We anticipate that knocking out CD45 alone would have little effect, and knocking out both of these phosphatases would preclude analysis of phagocytosis. Because of our feasibility concerns and the lengthy timeline for this experiment, we believe this is outside of the scope of our study.

In our discussion, we simplistically described our possible models in terms of CD45 exclusion, as the mechanisms of CD45 exclusion have been well characterized. This was an error and we have amended our discussion to read (lines 335-343):

As an alternative model, a denser cluster of ligated receptors may enhance the steric exclusion of the bulky transmembrane proteins like the phosphatases CD45 and CD148 (Bakalar et al., 2018; Goodridge et al., 2012; Zhu, Brdicka, Katsumoto, Lin, & Weiss, 2008).

Reviewer #2 (Significance (Required)):

The innovative part of this study is the combination of SNAP-tag attached, chimeric Fc-receptor with the DNA origami pegboard technology to address important open question on receptor function.

**Referees cross-commenting**

I find most of my three reviewing colleagues reasonable

I also agrée to Reviewer #1 comments 2

Likewise, how much variation was there in the expression of the chimeric receptors? Large variation in receptor numbers per cell could significantly alter the quantitative studies. Aside from the flow sorting for cells expressing two different molecules, how were cells selected for analysis?

But I want to add it is not only the amount of receptors but ils the nanoscale location that is key to receptor function

We have ensured that all receptors are trafficked to the cell surface. We have also measured their intensity at the cell cortex as discussed in response to Reviewer 1.

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

This is a very nicely done synthetic biology/biophysics study on the effect of ligands spacing on phagocytosis. They use a DNA based recognition system that the group has previously use to investigate T cell signaling, but express the SNAP tag linked transmembrane receptor in a macrophage cell line and present the ligands using DNA origami mats to control the number and spacing of complementary ligands that are designed to be in the typical range for low or high affinity FcR, a receptor that can trigger phagocytosis. The study offers some very nice quantitative data sets that will be of immediate interest to groups working in this area and, in the future, for design of synthetic receptors for immunotherapy applications. Other groups are working on similar platform for TCR. I don't feel there is any need for more experiments, but I have some questions and suggestions. Answering and considering these could clarify the new biological knowledge gained.

We thank the reviewer for their support of our manuscript. Given the reviewer’s statement that no new experiments are required, we have answered their questions to the best of our ability given the current data. Should the editor decide that any of these topics require experimental data to enhance the significance of the paper, we are happy to discuss new experiments.

Reviewer #3 (Significance (Required)):

I think the significance would be increased by addressing these questions, that would help understand how the synthesis system described related to other system directed as similar questions and more natural settings.

1. __ The densities of the freely mobile DNA ligands required to trigger phagocytosis is quite high. Was the length of the DNA duplexes optimized? The entire complex for both the intermediate and high affinity duplexes seems quite short, perhaps The extracellular domain of the DNA-CAR (SNAP tag and ssDNA strand) are approximately 10 nm (PMID 28340336). The biotinylated ligand ssDNA is attached to the bilayer via neutravidin, resulting in a predicted 14 nm intermembrane spacing. The endogenous IgG FcR complex is 11.5 nm. Bakalar et al (PMID 29958103) tested the effect of antigen height on phagocytosis and found that the shortest intermembrane distance tested (approximately 15 nm) was the most effective. As the reviewer notes, the optimal distance between macrophage and target may be larger than our DNA-CAR. However we think the intermembrane spacing in our system is within the biologically relevant range.

We saw robust phagocytosis at 300 molecules/micron of ssDNA, which is similar to the IgG density used on supported lipid bilayer-coated beads in other phagocytosis studies (PMID 29958103, 32768386). As the reviewer noticed, this is significantly higher than ligand density necessary to activate T cells (PMID 28340336). We have added a comment on ligand density to lines 96-97.

__ Are the origami mats generally laterally mobile on the bilayers. If so, what is the diffusion coefficient? Can one detect the mats accumulating in the initial interface between the bead and cell, particularly in cased where there is no phagocytosis? Would immobility of the mats make them more efficient at mediating phagocytosis compared to the monodispersed ligands, which I assume are highly mobile and might even be "slippery".__

We have confirmed that our bead protocol generally produces mobile bilayers, where his-tagged proteins can freely diffuse to the cell-bead interface (see accumulation of a his-tagged FRB binding to a transmembrane FKBP receptor at the cell-bead synapse below). We can qualitatively say that the origamis appear mobile on a planar lipid bilayer (see Dong et. al 2021 and images below). Directly measuring the diffusion coefficient on the beads is extremely difficult because the beads themselves are mobile (both diffusing and rotating), and cannot be imaged via TIRF. We do not see much accumulation of the origami at cell-bead synapses. This could reflect lower mobility of the origamis, or could be because the relative enrichment of origamis is difficult to detect over the signal from unligated origamis.

Overall, we expect the origami pegboards (tethered by 12 neutravidins) are less mobile than single strand DNA (tethered by a single neutravidin, supported by qualitative images below). We are uncertain whether this promotes phagocytosis. At least one study suggests that increased IgG mobility promotes phagocytosis (PMID 25771017). However, the zipper model would suggest that tethered ligands may provide a better foothold for the macrophage as it zippers the phagosome closed (PMID 14732161). Hypothetically, ligand mobility could affect signaling in two ways - first by promoting nanocluster formation, and second by serving as a stable platform for signaling as the phagosome closes. Since our system has pre-formed nanoclusters, the effect of ligand mobility may be quite different than in the endogenous setting.

(Image could not be uploaded)

In the above images, a 10xHis-FRB labeled with AlexaFluor647 was conjugated to Ni-chelating lipids in the bead supported lipid bilayer. The macrophages express a synthetic receptor containing an extracellular FKBP and an intracellular GFP. Upon addition of rapamycin, FRB and FKBP form a high affinity dimer, and FRB accumulates at the bead-macrophage contact sites.

(Image could not be uploaded)

In the above images, single molecules were imaged for 3 sec. The tracks of each molecule are depicted by lines, colored to distinguish between individual molecules. The scale bar represents 5 microns in both panels.

__ Breaking down the analysis into initiation and completion is interesting. When using the non-signalling adhesion constructs, would they get to the initiation stage or would that attachment be less extensive than the initiation phase.__

This is an interesting question. While we did not include the DNA-CAR-adhesion in our kinetic experiments, we have now quantified the frequency of cups that would match our ‘initiation’ criteria in 3 representative data sets where macrophages were fixed after 45 minutes of interaction with origami pegboard-coated beads. We found that an average of 16/125 of 4T beads touching DNA-CAR-adhesion macrophages met the ‘initiation’ criteria and an average of 2/125 were eaten (14% total). In comparison, we examined 4T beads touching DNA CAR𝛾 macrophages and found that on average 23/125 met the ‘initiation’ criteria, and 45/125 were already engulfed (54%). This suggests that the DNA-CAR-adhesion alone may induce enough interaction to meet our initiation criteria, but without active signaling from the FcR this extensive interaction is rare. We have added this data in a new Figure S6 and commented on this in lines 213-215.

__ It would be interesting to put these results in perspective of earier work on spacing with planar nanoarrays, although these can't be applied to beads. For integrin mediated adhesion there was a very distinct threshold for RGD ligand spacing that could be related to the size of some integrin-cytoskeletal linkers (PMID: 15067875). On the other hand, T cell activation seemed more continuous with changes in spacing over a wide range with no discrete threshold (PMID: 24117051, 24125583) unless the spacing was increased to allow access to CD45, in which case a more discrete threshold was generated (PMID: 29713075). The results here for phagocytosis with the very small ligands that would likely exclude CD45 seems to be more of a continuum without a discrete threshold, although high densities of ligand are needed. This issue of continuous sensing vs sharp threshold is biologically interesting so would be good assess this by as consistent standards are possible across systems.__

We agree that this is an interesting body of literature worth adding to our discussion. We have added a paragraph that puts our study in the context of prior work on related systems, including these nanolithography studies (Line 364-382):

How does the spacing requirements for Fc𝛾R nanoclusters compare to other signaling systems? Engineered multivalent Fc oligomers revealed that IgE ligand geometry alters Fcε receptor signaling in mast cells (Sil, Lee, Luo, Holowka, & Baird, 2007). DNA origami nanoparticles and planar nanolithography arrays have previously examined optimal inter-ligand distance for the T cell receptor, B cell receptor, NK cell receptor CD16, death receptor Fas, and integrins (Arnold et al., 2004; Berger et al., 2020; Cai et al., 2018; Deeg et al., 2013; Delcassian et al., 2013; Dong et al., 2021; Veneziano et al., 2020). Some systems, like integrin-mediated cell adhesion, appear to have very discrete threshold requirements for ligand spacing while others, like T cell activation, appear to continuously improve with reduced intermolecular spacing (Arnold et al., 2004; Cai et al., 2018). Our system may be more similar to the continuous improvement observed in T cell activation, as our most spaced ligands (36.5 nm) are capable of activating some phagocytosis, albeit not as potently as the 4T. Interestingly, as the intermembrane distance between T cell and target increases, the requirement for tight ligand spacing becomes more stringent (Cai et al., 2018). This suggests that IgG bound to tall antigens may be more dependent on tight nanocluster spacing than short antigens. Planar arrays have also been used to vary inter-cluster spacing, in addition to inter-ligand spacing (Cai et al., 2018; Freeman et al., 2016). Examining the optimal inter-cluster spacing during phagosome closure may be an interesting direction for future studies.

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Additional experiments performed in revision

In addition to these reviewer comments, we have added additional controls validating the DNA-CAR-4x𝛾 used in Figure 6c,d. We compared the DNA-CAR-4x𝛾 to versions of the DNA-CAR-1x𝛾-3x𝛥ITAM construct with the functional ITAM in the second and fourth positions (see the schematics now included Figure S7). We found that four individual receptors with a single ITAM each were able to induce phagocytosis regardless of which position the ITAM was in. However the DNA-CAR-4x𝛾 construct, which also contains 4 ITAMs, was not. This further validates the experiment presented in 6c,d. We also fixed minor errors we discovered in the presentation of data for Figures 1C and S1A.

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Reply to the reviewers

__Reviewer #1 __ __1. One key citation missing from the current manuscript is from Hwang et al. 2014 (PMID 25288734). This study has already described that the isp-1 mutant strain survives longer during P. aeruginosa infection. This citation also describes that the gene expression profile of isp-1 mutants animals includes a considerable number of pathogen-responsive genes that are similarly induced during infection. While the current manuscript does go into the mechanism of this resistance with more detail, they should amend the language to more appropriately reflect previous work, notably the above reference.

__

We apologize for the oversight and have added the suggested citation. Hwang et al. show that isp-1 worms have increased resistance to bacterial pathogens that is dependent on HIF-1/HIF1 and AAK-2/AMPK. In future work, it will be interesting to examine whether HIF-1 and AAK-2 act in concert with, or independently of, ATFS-1 and the p38-mediated innate immune signaling pathway to mediate pathogen resistance and longevity in isp-1 worms. We will add these points to our discussion.

__2. The authors suggest that ROS activation of the p38 MAPK pathway is likely not the mechanism that explains the resistance of long-lived mitochondrial mutant animals due to their reduced food intake. However, is ROS production nonetheless involved? Does antioxidant treatment suppress the increased resistance during infection of isp-1 and/or nuo-6 mutant animals?

__

To address this question, we will treat wild-type, isp-1 and nuo-6 worms with antioxidant and then measure resistance to bacterial pathogens using the P. aeruginosa strain PA14 slow kill assay. For the antioxidant treatment, we will use 10 mM Vitamin C as we have previously shown that this concentration is effective at reducing ROS in isp-1 worms to decrease isp-1 lifespan (Van Raamsdonk and Hekimi 2012, PNAS). Although antioxidant treatment can have pleiotropic effects, if this decreases survival of bacterial pathogen exposure, it will suggest that the elevated ROS production in isp-1 and nuo-6 worms may contribute to their enhanced bacterial pathogen resistance.

__3. (line 278-282): the authors should elaborate on how the p38 MAPK pathway plays a permissive role. It is intriguing that ATFS-1 and ATF-7 are both bZIP transcription factors that could theoretically heterodimerize and that they share common immune gene targets. The authors do indicate that the binding sites for ATFS-1 and ATF-7 are very different and are likely acting distinctly but some speculation would nonetheless strengthen this statement.

__

While ATFS-1 and ATF-7 were shown to bind to the promoter regions of the same innate immunity genes, the apparent consensus binding sites are different suggesting that they bind to different regions of the promoter. One way in which the p38 MAPK pathway may be playing a permissive role is that ATF-7 binding and relief from its repressor activity is required for any transcription of p38-mediated innate immunity target genes to occur. This is consistent with our data showing that disruption of nsy-1, sek-1, pmk-1 or atf-7 decreases the expression of innate immunity genes in wild-type worms. In contrast, it may be that the role of ATFS-1 is for enhanced expression of innate immunity genes such that when ATFS-1 is bound to the promoter region, or perhaps enhancer elements, the baseline expression of innate immunity genes that results from the binding of ATF-7 is increased. This idea is supported by our data showing that disruption of atfs-1 does not affect the expression of innate immunity genes in wild-type worms but prevents nuo-6 mutants from having increased expression. We will update our manuscript to include these points.

__4. The authors suggest that reduced food consumption of nuo-6 and isp-1 animals may suppress ROS-induced activation of the p38 innate immune pathway. It is intriguing that dietary restriction was previously shown to increase resistance to infection, presumably through p38-independent mechanisms (PMID 30905669). It would be interesting to measure host survival of nuo-6 and isp-1 mutant animals that are dietary-restricted to see if the enhanced survival rates conferred by mitochondrial stress and DR are additive or not.

__

According to this suggestion, we will compare the bacterial pathogen resistance of wild-type, isp-1 and nuo-6 worms that have undergone dietary restriction to the same strains under ad libitum conditions. This will determine the extent to which their enhancement of pathogen resistance might be additive.

__5. Figure 2: It is intriguing that loss of p38 signaling appears to have different effects in nuo-6 versus isp-1 animals. Specifically, loss of p38 signaling in isp-1 mutants renders them more sensitive to infection than wild-type, whereas it generally suppresses survival rates back to wild-type levels in the nuo-6 mutant background. Even within the nuo-6 mutant group, loss of SEK-1 has more dramatic effects on nuo-6 mutant animals than does loss of NSY-1, PMK-1 or ATF-7(gf). This is despite the fact that the nsy-1, sek-1, and pmk-1 alleles that are used in this study are all reported to be null. Can the authors speculate on these differences?

__

While the isp-1 and nuo-6 mutations both alter mitochondrial function, they affect different components of the electron transport chain. isp-1 mutations affect Complex III (Feng et al. 2001, Dev. Cell), while nuo-6 mutations affect Complex I (Yang and Hekimi 2010, Aging Cell). Although these mutants both have increased lifespan and a similar slowing of physiologic rates, it is not uncommon to observe differences between these mutants. For example, while treatment with the antioxidant NAC completely reverts nuo-6 lifespan to wild-type, it only partially reduces isp-1 lifespan (Yang and Hekimi 2010, PLoS Biology), suggesting that nuo-6 lifespan may be more dependent on ROS than isp-1. We have recently shown that deletion of atfs-1 reduces nuo-6 lifespan, but completely prevents isp-1 worms from developing to adulthood (Wu et al. 2018, BMC Biology), suggesting that isp-1 worms are more dependent on ATFS-1 than nuo-6 worms. Disruption of sek-1 has a greater impact on pathogen resistance than nsy-1 and pmk-1 because SEK-1 is absolutely required for innate immune signaling, while some partial redundancy exists for NSY-1 and PMK-1. We will add these points to our manuscript.

__6. One of the main conclusions from this study is that ATFS-1 likely binds directly to innate immune genes that are in common with ATF-7. Since this is such a pivotal finding, the authors should validate some candidate genes from the referenced ChIP seq datasets using ChIP qPCR. Also, are there predicted ATFS-1 binding sites (PMID 25773600) in these promoters?

__

Our data shows that activation of ATFS-1 increases the expression of innate immunity genes without increasing activation of p38. The simplest explanation for this observation is that ATFS-1 can upregulate the same innate immunity genes as ATF-7. Accordingly, we hypothesized that ATFS-1 and ATF-7 can bind to the same promoter. Fortunately, two previous ChIP-Seq studies, from well-established laboratories who have extensive experience studying ATFS-1 and ATF-7, had already determined which genes are bound by these two transcription factors (Nargund et al. 2015, Molecular Cell; Fletcher et al. 2019, PLoS Genetics). Comparing the results of these two published studies confirmed our hypothesis by demonstrating that the same innate immunity genes are bound by both ATF-7 and ATFS-1 in vivo. In order to provide additional support for the conclusion that ATFS-1 and ATF-7 can bind to the same genes, we will examine the genetic sequence of innate immunity genes that were shown to be bound by both ATFS-1 and ATF-7 in the published ChIP-seq studies to identify predicted binding sites for ATFS-1 and ATF-7, while noting that the ATFS-1-associated sequence is an enriched motif and not an established binding site. If we are able to identify the predicted binding sites for these two transcription factors in the same gene, it will provide further support for the conclusion that these transcription factors can both bind to the same innate immunity genes.

__Reviewer #2:

(1) The authors state that the p38 MAPK PMK-1 is not activated in the long-lived mitochondrial mutants. However, it might be better to state that there is "no enhanced activation" of PMK-1, since they clearly show in nuo-6 and isp-1 mutants the presence of phosphorylated PMK-1 (Fig. 4A), which would indicate an activated form of PMK-1 in these mutants.__

According to this suggestion, we will change the text to indicate that there is no enhanced activation of PMK-1 in nuo-6 and isp-1 worms.

__(2) Are the food-intake behaviors of all mutants in liquid culture (Fig. 4B-F) the same as their food-intake behaviors on solid agar media, the environment where pathogen resistance was measured?

__

We previously compared assays measuring food intake on solid agar media versus the liquid culture approach used in the current study to determine which method is the most robust (Wu et al. 2019, Cell Metabolism). While both assays produced similar results, performing the food intake assay on solid agar plates was much more variable as it is challenging to scrape off all of the uneaten bacteria from solid plates in order to measure it. Since the approach of measuring food intake in liquid media produces more consistent and reliable results, we chose to use this assay for the current study. We will update our manuscript to include this justification.

(__3) Does the p38 pathway single mutant nsy-1 or sek-1 live shorter than wild type on dead E. coli OP50 (Fig. S9) than they do on live OP50 (Fig. 3)? If so, what might that mean? These mutants are also living shorter than wild type on PA14 (Fig. 2), but live as long as wild type on OP50 (Fig. 3). What is in the live OP50 that allows these mutants to live like wild type?

__In a previous publication, we found that sek-1 mutants live shorter than wild-type worms, and nsy-1 live slightly shorter than wild-type worms in a lifespan assay performed in liquid medium with dead OP50 bacteria (Wu et al. 2019, Cell Metabolism). In the current study, we performed lifespan assays on solid NGM plates with live OP50 bacteria and observed a wild-type lifespan in sek-1 and nsy-1 worms. Since there are multiple experimental variables that are different between the previous and current study, most notably liquid versus solid media, the lifespan results cannot be directly compared. In the case of measuring survival of these strains on PA14, the simplest explanation is that they are dying sooner because their innate immune signaling pathway is disrupted, and so they are less able to mount an immune response against the pathogenic bacteria. We will update our manuscript to include these points.

__At the same time, wouldn't it be simpler to call the multiple antibiotic-treated OP50 as "dead bacteria", instead of "non-proliferating bacteria"? Some of the antibiotics used to treat OP50 are bactericidal and not bacteriostatic.

__

We previously monitored the OD600 of the antibiotic-treated, cold-treated OP50 that we used in our experiment, and found that there is only a very small decrease in OD600 after 10 days (Moroz et al. 2014, Aging Cell). Since dead bacteria are rapidly broken down leading to a decrease in OD600, this result is consistent with the bacteria being alive but not proliferating. We will include this point in our manuscript.

__(4) Since nuo-6 and isp-1 do not always behave exactly the same in their dependence on certain genes (e.g., Fig. 2C vs Fig 2D), what happens in isp-1; atfs-1 double mutants? Do these mutants behave in the same manner as nuo-6; atfs-1?

__

This is an interesting question. Unfortunately, isp-1;atfs-1 mutants arrest during development (Wu et al. 2018, BMC Biology), which is why we only examined the effect of atfs-1 deletion in nuo-6 mutants. We will update the manuscript to note this point.

__Regarding nuo-6; atfs-1, why does the double mutant live shorter on PA14 than either single mutant (Fig. 6A)? Is this because atfs-1 is needed to activate the p38 MAPK-dependent and -independent pathways? __

It is possible that the nuo-6 mutation makes worms more sensitive to bacterial pathogens, perhaps due to decreased energy production, and that activation of ATFS-1 is required not only to enhance their resistance to pathogens but also to increase their resistance back to wild-type levels. In a previous study, we showed that loss of ATFS-1 slows down the rate of nuclear localization of DAF-16. Thus, loss of atfs-1 may also be decreasing resistance to bacterial pathogens by diminishing the general stress resistance imparted by the DAF-16-mediated stress response pathway. We will update the manuscript to include these points.

__In Fig. 7B, the atfs-1(gof) appears to have slightly more phosphorylated p38 compared to wild type, although it is not statistically significant?

__

While there is a trend towards a very modest increase in phosphorylated p38 in the constitutively-active atfs-1 mutant compared to wild-type, quantification of four biological replicates indicated that the difference is not significant. This result is consistent with the fact that the levels of phosphorylated p38 are not significantly increased in nuo-6 or isp-1 mutants, both of which show activation of ATSF-1. We have provided raw images of all of these Western blots in our supplementals. In addition, we will repeat these Western blots to determine if this difference becomes significant with additional replicates.

__In Fig. 6B, the atfs-1 loss-of-function single mutant also increases the expression of Y9C9A.8, but suppresses it in a nuo-6 mutant background? What might that mean?

__

It is possible that in wild-type animals disruption of atfs-1 causes a compensatory upregulation of specific stress response genes. We have previously shown that deletion of atfs-1 results in upregulation of chaperone genes involved in the cytoplasmic unfolded protein response (hsp-16.11, hsp-16.2; Wu et al. 2018; BMC Biology). Perhaps Y9C9A.8 is acting in a similar way. In nuo-6, the upregulation of Y9C9A.8 is driven by activation of ATFS-1, and thus is prevented by atfs-1 deletion. We will add these points to the manuscript.

__Reviewer #3:

1) Some studies propose that OP50 offers some toxicity to worms which is not observed in other bacterial strains like HT115. The authors should test the role of the p38-innate immune signaling pathway in nuo-6 and isp-1 lifespan using other non-pathogenic E. coli strains.

__

To determine if the effect of disrupting the p38-mediated innate immune signaling pathway on the lifespan of isp-1 and nuo-6 mutants was simply the result of losing protection against OP50 bacteria, we examined the effect of nsy-1, sek-1 and atf-7(gof) mutations on isp-1 and nuo-6 lifespan using non-proliferating bacteria. We found that even when no proliferating bacteria are present, disruption of the p38-mediated innate immune signaling pathway markedly decreases isp-1 and nuo-6 lifespan. This suggests that the p38-mediated innate immune signaling pathway is required for their long lifespan independently of its ability to protect against bacterial infection. Similarly, we have previously shown that lifespan extension resulting from dietary restriction is dependent on the p38-mediated innate immune signaling pathway even when non-proliferating bacteria are used (Wu et al. 2019, Cell Metabolism). We will clarify this important point in the manuscript.

__ 2) The authors should measure food intake in worms exposed to pathogenic bacteria, given that reduced bacterial intake may be related to reduced mortality.

__

Unfortunately, it is not feasible to perform the food intake assay using the pathogenic bacteria because the bacteria cause death thereby complicating the calculation of food consumed per worm (which requires at least 3 days to assess). As an alternative to measuring food intake, we will attempt to measure intestinal accumulation of P. aeruginosa, which is a balance between food intake and other factors. To do this we will use a P. aeruginosa strain that expresses GFP and quantify the amount of intestinal fluorescence in wild-type, isp-1 and nuo-6 worms that have been grown on the GFP-labelled P. aeruginosa.

__3) The authors should check if ROS is required for the activation of the p38-mediated innate immune signaling pathway and reduction in food intake.

__

To determine if the elevated ROS that is present in isp-1 and nuo-6 worms affects activation of the p38-mediated innate immune signaling pathway, we will treat wild-type, isp-1 and nuo-6 worms with Vitamin C and measure the ratio of phosphorylated p38 to total p38 by Western blotting. Similarly, to examine the effect of ROS on food intake, we will treat wild-type, isp-1 and nuo-6 worms with Vitamin C and then quantify its effect on food intake. For these experiments, we will use 10 mM Vitamin C as we have previously shown that this concentration is effective at reducing ROS in isp-1 worms to decrease isp-1 lifespan (Van Raamsdonk and Hekimi 2012, PNAS).

__4) Since ATFS-1 and the p38 pathway control food intake, how related to dietary restriction the phenotypes the authors are studying are?

__

While the lifespan extension that results from mild impairment of mitochondrial function and the lifespan extension resulting from dietary restriction are both dependent on the p38-mediated innate immune signaling pathway, these interventions modulate innate immunity gene expression in opposite directions. We previously reported that dietary restriction primarily downregulates innate immunity genes (Wu et al. 2019 Cell Metabolism). Here, we show that mutations in isp-1 or nuo-6 primarily result in upregulation of innate immunity genes. To more globally examine gene expression changes between dietary restriction and mild impairment of mitochondrial function, we compared differentially expressed genes. We found that there was very little overlap of either upregulated or downregulated genes between dietary restriction and isp-1/nuo-6 mutants. We will add a supplementary figure to demonstrate this, and add these points to our manuscript.

__ 5) Somewhat related to the previous points, I am not so sure whether the changes in food intake are cause or consequence of the alterations in the innate immunity-related genes. Reduced food intake is depicted in Fig. 8 as the cause of the activation of the p38 pathway, but there is not enough evidence to unequivocally prove that. In fact, food intake might be controlled by the p38 or ATFS-1 pathway or by a common regulator such as ROS.

__

We apologize that we didn’t make this clearer. In our previous work, we showed that dietary restriction results in decreased activation of the p38 pathway (Wu et al. 2019, Cell Metabolism). Here, we show that activation of ATFS-1 results in decreased food intake. Based on our previous study, this decrease in food intake should similarly decrease p38 pathway activation. In Figure 8, we have depicted ATFS-1 inhibiting food intake, and food intake activating the p38-mediated innate immune signaling pathway. Combined, our model suggests that activation of ATFS-1 should act to decrease p38-mediated innate immune signaling. We will clarify this in the figure legend.

__6) I am not so convinced of the role of DAF-16. In fact, in Fig. 5A daf-16 mutation reduces pathogen resistance and that could represent a toxic effect of the mutation. Furthermore, the results in Fig. 4D do not exclude the possibility that daf-16 and isp-1 act in parallel.

__

We agree that the role of DAF-16 could be non-specific. While we show that disruption of daf-16 leads to decreased bacterial pathogen survival in isp-1 worms, it also decreases bacterial pathogen survival in wild-type worms. Since DAF-16 is known to be required for general resistance to stress, the decreased survival when daf-16 is disrupted could be due to a general toxic effect of reducing general stress resistance. This conclusion is consistent with our observation that DAF-16 is not involved in the upregulation of innate immunity genes in isp-1 worms. We will emphasize these points in our manuscript.

__ 7) Loss of innate immunity related genes may result in toxicity and sensitize worms to pathogenic bacteria. This is further supported by an even lower resistance to pathogens in the double mutants mainly in Fig. 2D.

__

We agree. Our data confirms that disruption of the p38-mediated innate immune signaling pathway makes worms more susceptible to bacterial pathogens. We will emphasize this point.

__ 8) The blots are saturated, particularly in Fig. 4A, and this can be masking the differences in p38 phosphorylation. In fact, the fact that p38 phosphorylation is not changed is contradictory to the other results. How is p38 regulated by mitochondrial mutations then? I am concerned that p38 is actually not altered and the changes in gene expression are exclusively due to ATFS-1. The interaction with the p38 pathway demonstrated genetically could be due to the toxicity elicited by the loss of function mutations in this pathway.__

To address this concern, we will repeat the Western blotting experiment to compare the ratio of phosphorylated p38 to total p38 between wild-type, isp-1 and nuo-6 worms. We will take multiple exposures to ensure that the blots are not over-saturated. Having already completed four replicates, we believe that there is not a major change in p38 activation. Our data suggests that the p38-mediated innate immunity pathway is playing a permissive role such that it is required for baseline expression of innate immunity genes, but that activation of ATFS-1 is driving the enhanced expression of innate immunity genes that we observe in the long-lived mitochondrial mutants and constitutively active atfs-1 mutants. We will update our manuscript to clarify this.

__ **Minor concerns**

1) Lines 167 and 174: What are these p values referred to?

__

The p-values indicate the significance of the overlap between the two gene sets. Given the size of the two gene sets, this is the probability that the observed number of overlapping genes would result by picking genes at random. We will clarify this in the manuscript.

__2) Line 258: I partially agree with the conclusions, since the functions may not necessarily be associated with innate immune signaling but rather other functions of p38.

__

Since isp-1 and nuo-6 worms have extended longevity even when grown on non-proliferating bacteria this indicates that their long life is not dependent on their enhanced resistance to bacterial pathogens. Similarly, since disruption of genes in the p38-mediated innate immune signaling pathway decrease isp-1 and nuo-6 lifespan even when the worms are grown on non-proliferating bacteria, this suggests that this pathway enhances longevity independently of its ability to increase innate immunity.

__ 3) Why in figures 4D and E different mutants were used?

__

We only used isp-1 mutants to examine the effect of daf-16 because we were unable to generate nuo-6;daf-16 mutants due to close proximity of the two genes on the same chromosome. We only used nuo-6 mutants to examine the effect of atfs-1 because isp-1;atfs-1 worms arrest during development. We will include this explanation in our manuscript.

__ 4) Line 498: revise writing.

__

We will rewrite this sentence to improve clarity.

__ 5) Show blots in Fig. 7B.

__

We will provide an image of a representative Western blot in Figure 7, and will provide the raw images for all of Western blots in our supplementals.

__ 6) It would be interesting to know where the activation of the immune-related genes by the mitochondrial mutations is happening, whether this is a cell autonomous or cell non-autonomous mechanism.

__While it would be interesting to explore whether specific tissues are important in sensing mitochondrial impairment in order to upregulate genes involved in innate immunity, it is beyond the scope of this manuscript. Previous work has shown that knocking down the expression of the cytochrome c oxidase gene cco-1 in neurons can activate the ATFS-1 target gene hsp-6 in the intestine (Durieux et al., 2011). Based on this, one could hypothesize that a similar cell non-autonomous mechanism might be involved. We will note this possible future direction in our discussion.

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Reply to the reviewers

__Reviewer #1: __ __ **Major concerns:**

1) This manuscript has some overlap with another manuscript from the same group recently submitted to EMBO Reports. Although I believe both manuscripts have sufficient elements to justify publication of two papers, I strongly recommend that these publications are made back-to-back and they should be discussed in context with one-another.

__

We agree that this manuscript is distinct from but highly complementary to our manuscript on innate immunity in the long-lived mitochondrial mutants, which has been invited for revision at EMBO Reports. According to this suggestion, we have arranged for these papers to be considered for publication at the same time in EMBO Reports and Life Science Alliance. We have updated the discussions of both manuscripts to incorporate the findings of the other manuscript.

__ 2) How is ATFS-1 function regulated in long-lived worms or under multiple stress conditions? Is there a common regulator such as oxidative stress or mitochondrial dysfunction? Both manuscripts would benefit from a clear understanding on how ATFS-1 is controlled under conditions where mitochondrial function is altered. Is mitoUPR required for this activation? If so, is mitoUPR upregulated in all interventions where ATFS-1 has been shown to play a role in stress response. __

We have previously used a reporter strain to determine which external stressors activate ATFS-1. The reporter strain has a transgene that links the promoter of the ATFS-1 target gene hsp-6 to GFP (Phsp-6::GFP) such that these worms exhibit increased fluorescence whenever ATFS-1 is activated. After exposing these worms to heat, cold, osmotic stress, anoxia, oxidative stress, starvation, ER stress and bacterial pathogens, we only observed increased fluorescence after exposure to oxidative stress (Dues et al. 2016, Aging). Here, we show that constitutive activation of ATFS-1 results in increased resistance not only to oxidative stress but also ER stress, osmotic stress, anoxia and bacterial pathogens (fast kill assay). Thus, ATFS-1 activation does not just protect against stresses that lead to its activation. Notably, the constitutively active atfs-1 mutants (et15 and et17) exhibit activation of the mitoUPR under unstressed conditions (e.g. upregulation of hsp-6 in Fig. 1A; increased fluorescence of hsp-6 and hsp-60 reporter strains in Rauthan et al. 2013, PNAS; upregulation of many other stress pathway target genes Fig. 2). It is likely that the activation of the mitoUPR and downstream stress response pathways under unstressed conditions results in the increased resistance to stress that we observe. We have included these points in the revised manuscript.

__Is there any intervention that controls longevity and does not trigger ATFS-1 response?

__

When we compared RNA-seq data on a panel of long-lived mutants representing multiple pathways of lifespan extension to ATFS-1 target genes (defined as genes that are upregulated by spg-7 RNAi in an ATFS-1 dependent manner from Nargund et al. 2012, Science), we found that seven of the nine long-lived mutants that we examined showed enrichment of ATFS-1 target genes (clk-1, isp-1, nuo-6, daf-2, glp-1, ife-2) while two did not (eat-2, osm-5) (Fig. 5). Interestingly, in six of these seven strains (all except ife-2), there is an increase in reactive oxygen species (ROS) that contributes to their longevity (treatment with antioxidants decreases their lifespan; Yang and Hekimi 2010, PLoS Biology; Zarse et al. 2012, Cell Metabolism; Wei and Kenyon 2016, PNAS). This observation is consistent with the idea that ROS/oxidative stress is sufficient to activate ATFS-1/mitoUPR. We have previously shown that exposure to a mild heat stress (35°C, 2 hours) or osmotic stress (300 mM, 24 hours) can extend lifespan but does not increase expression of the ATFS-1 target gene hsp-6 (Dues et al. 2016, Aging). Thus, there are multiple examples in which a genetic mutation or intervention increases longevity but does not trigger upregulation of ATFS-1 target genes. We have updated the manuscript to include these points.

__3) In Fig. 3, some of these genes appear to be unspecifically associated with different stressors. Therefore, it is difficult to rule out the participation of ATFS-1 in specific stress responses without looking at specific stress-responsive genes or a wider range of genes. For example, the conclusion that ATFS-1 does not control osmotic stress gene expression response comes from looking at 3 genes: sod-3, gst-4 and Y9C9A.8. gst-4 does not appear to be directly controlled by ATFS-1 regardless of the stressor. sod-3 is also upregulated by oxidative stress and Y9C9A.8 by anoxia. On the other hand, somewhat contradicting the authors' conclusions that ATFS-1 does not participate in osmotic stress response based on these 3 genes, ATFS-1 appears to be required for osmotic stress resistance.

__

In this experiment, we treated wild-type and atfs-1 deletion mutants with six different stressors (oxidative stress, bacterial pathogens, heat stress, osmotic stress, anoxia, and ER stress), isolated mRNA and then examined the expression of 14 different stress response genes. To select these genes, we chose a combination of the most established target genes of the stress response pathways that we examined in Figures 1/2, and genes that we had previously shown to be upregulated by specific stresses using fluorescent reporter strains (Dues et al. 2016, Aging). These genes included hsp-6, hsp-4, hsp-16.2, sod-3, gst-4, nhr-57, Y9C9A.8, trx-2, ckb-2, gcs-1, sod-5, T24B8.5, clec-67 and dod-22. To determine if ATFS-1 is required for gene upregulation in response to any of the six different stressors, we first identified which of these stress genes is significantly upregulated in response to each stressor and then looked to see if this upregulation is reduced or prevented by atfs-1 mutation. We found that there were multiple examples of this for both oxidative stress and bacterial pathogen stress, but not for other stresses. We selected three representative genes to display in Figure 3. Nonetheless, it is possible that there are genes that we didn’t examine that are upregulated by the other four stressors in an ATFS-1-dependent manner. To definitively address this question, one would have to do RNA sequencing on wild-type and atfs-1(gk3094) worms comparing untreated and stressed, but this is beyond the scope of the current manuscript. We have updated the manuscript to include these points, and noted the possibility that there are genes, which we didn’t measure, that are upregulated by the other four stressors in an ATFS-1-dependent manner. We have also included the qPCR data for all 14 genes for each of the six external stressors in Supplemental Figures S3-S8.

__ **Minor concerns:**

1) The paragraph starting in line 107 is confusing. They write that "Constitutive activation of ATFS-1 in atfs-1(et 15) and atfs-1(et17) mutants resulted in upregulation of most of the same genes that are upregulated in nuo-6 mutants, except for gst-4" and later they state that "Activating the mitoUPR through the nuo-6 mutation, or through the constitutively-active ATFS-1 mutants did not significantly increase the expression of target genes from the ER-UPR (hsp-4; Fig. 1B) or the cyto-UPR (hsp-16.2; Fig. 1C)." I understand the upregulation of ER-UPR and cyto-UPR is not statistically significant (isn't it for hsp-16.2?), but the first sentence is not accurate if statistics is considered.

__

To clarify this, we have modified the first sentence to describe which genes are significantly upregulated in atfs-1(et15) mutants, and separately describe the findings for atfs-1(et17) mutants in the second sentence. The results for hsp-16.2 are not significant because this gene shows highly variable expression between replicates and can be induced 60-fold. We have noted this in the text as well.

__ 2) The authors should discuss why they think atfs-1(et15) gain-of-function mutant exhibited decreased resistance to chronic oxidative stress, while it is protected from acute oxidative stress. In fact, the et15 allele differs in many aspects in relation to the et17 and in some cases it behaves similarly to the gk3094 loss-of-function allele.

__

While atfs-1(et15) and atfs-1(et17) mutants generally show similar results, they also exhibit differences. We previously used RNA sequencing to examine gene expression in these two strains. We found that atfs-1(et15) mutants have far more extensive changes in gene expression than atfs-1(et17) mutants (6227 differentially expressed genes versus 958 differentially expressed genes). It is possible that the et15 mutation is more disruptive to the mitochondrial targeting sequence than et17, thereby resulting in increased nuclear localization and more gene expression changes. The additional gene expression changes in the atfs-1(et15) mutant may contribute to their decreased resistance to chronic oxidative stress. We have included these points in the revised manuscript.

__ 3) Fig 4I is very similar to Fig. 6A of the other manuscript which strengthen the notion that ATFS-1 is not required (it is rather detrimental) for bacterial pathogen response when no underlying stress (most likely oxidative) occurs.

__

Yes, our results indicate that ATFS-1 is not required for wild-type survival of bacterial pathogen exposure. This is consistent with our findings in the other manuscript that baseline expression of innate immunity genes does not depend on ATFS-1 (innate immunity gene expression is similar between wild-type and atfs-1(gk3094) mutants). We have updated the manuscript to emphasize these points.

__ 4) In the paragraph starting in line 213, the authors conclude that "ATFS-1 is sufficient to protect against oxidative stress, osmotic stress, anoxia, and bacterial pathogens but not heat stress". The results do not unequivocally support a participation of ATFS-1 in oxidative stress or bacterial pathogen response, given the responses vary depending on the allele or condition.

__

We have modified this sentence by replacing “activation of ATFS-1 is sufficient to protect” with “activation of ATFS-1 can protect” to indicate that we didn’t observe protection in all cases.

__ 5) "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." It actually does, since ATFS-1 gain-of-function decreases lifespan.

__

We have rewritten this sentence to say that constitutive activation of ATFS-1 does not extend lifespan, despite increasing resistance to multiple stresses.

__

__

__ __

__6) Paragraph starting in line 359 needs to be discussed in light of the results of the other manuscript submitted by the authors to EMBO.

__

Combined these two manuscripts indicate that baseline levels of innate immunity are dependent on the p38-mediated innate immune signaling pathway, and not dependent on ATFS-1. This idea is supported by the fact that deletion of atfs-1 does not decrease resistance to bacterial pathogens and does not reduce the expression of innate immunity genes. In contrast, disrupting genes involved in the p38-mediated innate immune signaling pathway does decrease resistance to bacterial pathogens and does decrease the expression of innate immunity genes. We have updated this paragraph to include these points and reference the findings from our manuscript on innate immunity in the long-lived mitochondrial mutants.

__ 7) In Fig. 1C, it appears that atfs-1 loss of function increases hsp-16.2. Is that significant?

__

While there is a strong trend towards increased hsp-16.2 expression in atfs-1(gk3094) mutants, this difference did not reach significance because this gene shows highly variable expression and can be induced 60-fold.

__ 8) In Fig. 2, 5 and S1, it would be interesting to build one single Venn Diagram with all the lists of genes to see if there are common genes associated with multiple pathways and if there are many ATFS-1 target genes not associated with these classical stress or longevity pathways.

__

While we would be very interested in performing this type of visualization, weighted Venn diagrams with more than 3 or 4 groups are challenging to generate and more challenging to interpret. Instead, we have generated an UpSetR plot to demonstrate the number of overlapping genes between each of the stress response pathways, as well as how many ATFS-1 target genes are not involved in stress response. We have included this plot in Figure 2, Panel I. We have also generated simpler figure to show the overlap between pairs of stress response pathways (Figure S1). In addition, we have also added Table S4 with these gene lists.

__ 9) In Fig. 2, 5 and S1: What are the p values referred to?

__

The p-values indicate the significance of the difference between the observed number of overlapping genes between the two gene sets, and the expected number of overlapping genes if the genes were picked at random. We have clarified this in the manuscript.

__ 10) In paragraph starting in line 85, the authors should include references that evidence the genes are bona fide markers of the stress response pathways.

__

We have added references for each of the genes that we examined to link it to the associated stress response pathway.

__ 11) Tables S2 and S3 are missing. __

Tables S2 and S3 were uploaded as Excel spreadsheets, not included with the supplemental figures as the other supplementary Tables were. We apologize that these were difficult to locate. In the revision, Table S1 is in the manuscript file, while Table S2 to S6 will be uploaded as separate files.

__ __

__Reviewer #2:

**Major comments:**

The only major conclusion that I would qualify is "ATFS-1 serves a vital role in organismal survival of acute stresses through its ability to activate multiple stress response pathways"-the data, as presented, does not make clear whether ATFS-1 directly activates these pathways (ie, by binding response elements in genes in those pathways), or indirectly influences them by altering the physiology of the worm).

__

We agree that our data does not determine precisely how ATFS-1 acts to modulate the expression of the different stress response pathways. To determine the extent to which ATFS-1 might be able to bind directly to the target genes of other stress response pathways, we have compared the ChIP-seq results for ATFS-1 to ChIP-seq studies for other stress responsive transcription factors (DAF-16, SKN-1, HSF-1, HIF-1, ATF-7). We found that in each case there are sets of genes that can be bound by both transcription factors. This suggests that ATFS-1 may be direct regulating at least some of the target genes from other stress response pathways. We have updated our manuscript to include these points and included the ChIP-seq data comparisons in Figure S2.

__ **Minor comments:**

In abstract, consider broadening/re-wording "Gene expression changes resulting from the activation of the mitoUPR are mediated by the transcription factor ATFS-1/ATF-5." Because a naïve reader may understand this to suggest that ATFS-1 is activated only by mitochondrial protein misfolding.

__

In this sentence we are describing the role of ATFS-1 in mediating the gene expression changes resulting from the activation of the mitoUPR. We would be happy to modify the sentence if this is unclear.

__Please indicate whether strains were outcrossed, and how often.

__

We have added these details to our materials and methods.

__ How was "young adult" defined? Were worms synchronized, and if so, how?

__

Young adult worms are picked on day 1 of adulthood before egg laying begins. The worms were not synchronized, but picked visually as close to the L4-adult transition as possible. We have added these details to our method section.

__ For the gene expression experiments, do I understand correctly that FUDR was used only for oxidative stress and adult day 2 experiments? Please clarify.__

Yes, that is correct. FUdR was used for these samples because (1) with the 2-day duration of this stress, worms can produce progeny which would complicate the collection of the experimental worms; and (2) 4 mM paraquat often results in internal hatching of progeny when FUdR is absent, which might have affected the results. The control worms for the 48-hour 4 mm paraquat stress were also treated with FUdR. We have clarified this in the manuscript and noted that the presence of FUdR has the potential to alter gene expression.

__ Important: Please make clear how many replicates were performed for each experiment, and where relevant, how many worms were measured per replicate (e.g., stress survival and lifespan). __

We have added a spreadsheet (Table S6) to include the number of replicates and number of worms per replicate for all experiments.__

For 2-way ANOVA analyses, please specify p values of both main factors as well as interaction terms and posthoc analyses where relevant.

__

We have included these additional details from our statistical analyses in Table S6.

__ In the second paragraph of the introduction, I suggest broadening slightly the description of why normal mitochondrial function is required for ATFS-1 important and degradation, because this helps the reader understand that any one of many perturbations to mitochondrial function (decreased bioenergetics, membrane potential, protein degradation, protein import; increased ROS; etc.) could prevent or reduce ATFS-1 import and degradation.

__

We have added these additional factors that might prevent ATFS-1 import and degradation in paragraph one of our introduction and broadened the description in paragraph two.

__ For Figure 1: The authors present their choice of genes to analyze as if, and interpret their results assuming, that each of these gene is ONLY regulated by the indicated stress response pathways. I think this is very unlikely. For example: is it certain that sod-3 and trx-2 are not also skn-1 regulated? How is "antioxidant" distinguished from the skn-1 pathway? Further clouding the water is the likelihood that nuo-6 and atfs-1 manipulations alter physiology in such a way that there are secondary/indirect stress pathways activated (for example: the authors show that ATFS-1 overexpression shortens lifespan. Perhaps this is why it appears that ATFS-1 overexpression also appears to cause a strong, although variable, upregulation of the cytosolic UPR?). The likelihood (in my opinion) that these genes are in fact regulated by more than one type of response element, and that the manipulations used to study these relationships have pleiotropic effects, do not invalidate the general conclusion that these pathways interact-but they do mean that the results should be discussed with more caveats regarding HOW they interact.

__

These are excellent points. The genes that we selected for Figure 1 are the genetic targets that in our reading of the literature have been most often used to represent a particular stress response pathway. We have added references to justify the association of each gene with the indicated stress response pathway. We have also noted that in at least some cases the stress response genes that have been typically used to represent a specific pathway can be activated by multiple pathways. We agree that the selection of genes for Figure 1 is not a comprehensive approach, and that it is possible that if we chose a different gene from each of these pathways, the results might be different. We have updated our manuscript to specifically note these limitations. To avoid these limitations, we examined the overlap between all of the genes significantly upregulated by ATFS-1 activation and all of the genes significantly upregulated by the different stress response pathways in Figure 2. In addition, to gain a better understanding of the overlap between these different stress response pathways globally, we have compared gene expression between each of the stress response pathways studied in Figure S1.

__Figure 1 also illustrates why a more detailed description of sample size and statistical analysis should be provided. What was the "n"? What were the main effects and interaction terms of each 2-way ANOVA? The design is not full factorial and therefore does not permit a simple 2-way ANOVA (i.e., not all condition combinations are performed)-which responses precisely were compared to which? Were 2 2-way ANOVAs performed per mRNA?

__

For Figure 1 we used a one-way ANOVA to compare all of the groups to wild-type with a Bonferroni’s Multiple Comparison post-hoc test. We have updated the manuscript to include the sample size and statistical details in Table S6.

__ The work shown in Figure 2 is a very nice way to leverage previous data to further explore this idea of cross-talk. I would suggest including a bit more meta-data in the supplemental data files related to each dataset. For example, what lifestages were used (were they all young adult?), was FUDR used, etc.

__

We have added these details to Table S3, which includes the lists of target genes from each stress response pathway.

__ However, again, I don't understand how the authors can reach this conclusion: "Combined, this indicates that activation of ATFS-1 is sufficient to upregulate genes in multiple stress response pathways." (lines 152-153 but similar phrasing occurs multiple times) Could it not simply be that one form of cellular stress often eventually triggers broader cellular dysfunction, thus activating other cell stress pathways? Ie-how do we know whether these genes are directly regulated by atfs-1 binding regulatory elements, as implied by this phrasing?

__

This conclusion is derived from our data showing that constitutively active ATFS-1 mutants have significant upregulation of target genes from multiple stress response pathways (Figure 2). As the worms in those experiments were not exposed to stress, we don’t have reason to believe that they are experiencing cellular stress or dysfunction. We think it is more plausible that activation of ATFS-1, which normally occurs in response to stress, leads to the activation of other stress response pathways, either directly or indirectly, and that these pathways are recruited to help regain mitochondrial homeostasis. We don’t mean to imply that activated ATFS-1 binds directly to the target genes of other stress response pathways. We have clarified this in the revised manuscript.

__ The stress response experiments are very nicely done and very interesting. I appreciate that the authors did not shy away from describing counterintuitive results (eg et15 mutants showing increased sensitivity to chronic oxidative stress), and think that these results should also be briefly considered in the Discussion.

__

We have updated our manuscript to discuss the observation that atfs-1(et15) mutants have increased sensitivity to chronic oxidative stress.

__

__

__ __

__Figure 3: please report ANOVA interaction terms-these are what tell whether the inductions are in fact dependent on atfs-1 (not the post-hoc analyses). Again, it also appears that in some cases, there is an upregulation of certain genes with atfs-1 knockdown-please report all p-values (because there will be many, I recommend a supplemental table with all main and interaction and posthoc analyses). Again, the "n" also needs to be specified.

__

We have added Table S6 to include all of these statistical details.

__ Figure 4 A-C appear to be lacking error bars? Please add. Perhaps relatedly-the effect size for 4A looks much larger than for 4B, but this does not come across in the text.

__

We have added error bars to Figure 4A-C. We think the difference in effect size might result from the fact that 4A is an acute assay and 4B is a chronic assay. We speculate that the negative effect of the et15 and et17 mutations on lifespan might be a stronger factor in the chronic assay. We have updated the text to comment on the relative effect sizes.

__ For Figures 4 and 6, please indicate sample size-number of independent experimental replicates, and number of worms per replicate (or range per replicate).

__

We have added the number of replicates and sample size in Table S6.

__ Lines 224-225 re. sod-2 mutants: these may also act by decreasing ROS signaling (less conversion of superoxide anon to hydrogen peroxide); also, why would this strain not be considered another long-lived mitochondrial mutant (like clk-1, isp-1 and nuo-6, to which it is contrasted)?

__

We think the sod-2 mutation extends lifespan by increasing ROS signaling, as treatment with antioxidants decreases their lifespan. The increased superoxide from the loss of sod-2 may be converted to H2O2 by sod-3 or sod-1, which are also present in the mitochondria. We don’t include sod-2 with the mitochondrial mutants because the mutation does not directly impact the mitochondrial electron transport chain, but may do so secondarily due to elevated ROS.

__ The confirmation that atfs-1 overexpressing strains are short-lived is very interesting. However, I think this statement "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." (lines 265-267 and similar in several places throughout the Discussion, eg line 279) should be altered to indicate that this was observed under controlled laboratory conditions. Eg, "...this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background under optimized laboratory conditions..."

__

This is an interesting point. It is possible that constitutive activation of ATFS-1 may be beneficial for lifespan in an environment where worms are exposed to external stressors. We have noted that our lifespan results were obtained under lab conditions, which are believed to be relatively unstressful.

__

__

__ __

__Discussion: consider adding in a consideration of dose-response, both of knockdown of mitochondrial genes (eg, k/d of many mitochondrial genes promotes lifespan at low levels, but decreases lifespan with greater knockdown) and of stressors (chemicals, heat, etc; for chemicals, at the least, dose-response is very important, with low levels not infrequently triggering apparently beneficial stress responses, and higher levels causing toxicity).

__

It is possible that the magnitude of ATFS-1 activation will impact its effect on stress resistance and lifespan. Perhaps, a milder activation of ATFS-1 will be more beneficial with respect to lifespan. The degree of ATFS-1 activation may also account for differences that we observe between atfs-1(et15) and atfs-1(et17) mutants. atfs-1(et15) has more differentially expressed genes than atfs-1(et17) suggesting the possibility that it has more ATFS-1 activation. We have updated our manuscript to include these points.

__ Section beginning on line 384 "ATFS-1 upregulates target genes of multiple stress response pathways"-again, please revise to make clear that this work does not demonstrate direct regulation.

__

We have clarified that our results don’t demonstrate direct regulation. In addition, we have examined published ChIP-seq datasets to determine if there is evidence of direct regulation.

__ It seems to me that our reviews are in pretty good agreement. I agree with Reviewers 1 and 3 where they commented on things that I did not. While I did not consider the manuscripts as overlapping in the sense of being redundant, I very much like Reviewer 1's suggestion that they be published back to back and that the Discussion of each incorporate consideration of the Results of the other.

__According to this suggestion, we have arranged for these papers to be considered for publication at the same time in EMBO Reports and Life Science Alliance. We have updated the discussions of both manuscripts to incorporate the findings of the other manuscript.

__ Reviewer #3:

**Major comments**

1.The authors mention that activation of the UPRmt by nuo-6 mutants or atfs-1(gf) do not activate the ER UPR or cyto-UPR gene expression targets (lines 111-113). However, they also find that atfs-1(gf) animals have 25% overlap with the ER UPR pathway (line 146-147). Is 25% overlap not substantial?

__

The genes that we are referring to in lines 111-113 are the genetic targets that in our reading of the literature have been most often used to represent the ER-UPR or Cyto-UPR. This is not a comprehensive approach, and it is possible that if we chose a different gene from each of these pathways, the result might be different. We have updated our manuscript to include this limitation. To avoid this limitation, we examined the overlap between all of the genes significantly upregulated by ATFS-1 activation and all of the genes significantly upregulated by the ER-UPR or Cyto-UPR in Figure 2. In both cases, we find the overlap is significant, indicating that activation of ATFS-1 leads to activation of ER-UPR and Cyto-UPR target genes.

__

__

__ __

__To determine whether ATFS-1 mediates any protective effect during ER stress, authors should test atfs-1(gf) and atfs-1(lf) animals' resistance to ER stress.

__

To examine the effect of ATFS-1 on resistance to ER stress, we exposed wild-type, atfs-1(gk3094), atfs-1(et15) and atfs-1(et17) worms to 50 µM tunicamycin beginning at young adulthood and monitor survival daily. We found that both constitutively active atfs-1 mutants, et15 and et17, have increased resistance to ER stress compared to wild-type worms, while atfs-1 deletion mutants have a similar survival to wild-type. We have added this new data to Figure 4.

__ Authors should comment on the difference in outcomes with atfs-1(et17) and atfs-1(et15) animals to chronic oxidative stress (line 184-187).

__

We have updated our manuscript to discuss the observation that atfs-1(et15) mutants have increased sensitivity to chronic oxidative stress.

__ Lines 258-260. The authors should make clear in this section that a previous study had already measured lifespans of atfs-1(gf) animals and found that it was reduced (PMID 24662282). Also, an elaboration on why this experiment was repeated would be warranted.

__

We have referenced the lifespan results from this previous study in our introduction (line 53-54, Bennett et al), in our results section (lines 342-343; “which is consistent with a previous study finding shortened lifespan in atfs-1(et17) and atfs-1(et18) worms”) and in our discussion (lines 429-431; “as well as previous results using constitutively active atfs-1 mutants (et17 and et18) show that constitutive activation of ATFS-1 in wild-type worms results in decreased lifespan”). The reasons that we repeated this result are (1) because the lifespan of the atfs-1(et15) mutant had not been measured and this was the allele that we used in our paper; and (2) because the shortened lifespan is a surprising result given the beneficial effect of ATFS-1 on stress resistance, we thought it was important to repeat this experiment under the same conditions that we measured stress resistance.

__ The authors find that atfs-1(gk3094) animals lived longer during infection with PA14 (line 208-211). Another study found that atfs-1(gk3094) animals died faster on PA14 (PMID 28283579), which should be mentioned and commented on.

__

We have added this finding to our discussion. We have also compared the protocols used by Jeong et al. (who observed decreased survival in atfs-1(gk3094) deletion mutants), Pellegrino et al. (who observed wild-type survival in atfs-1(tm4919) deletion mutants and our manuscript (in which we observed slightly increased survival in atfs-1(gk3094) deletion mutants), to see which parameters might account for the observed differences.

__**Minor comments**

Line 38: "Inside the mitochondria, ATFS-1 is degraded by the Lon protease CLPP-1/CLP1". The phrasing suggests that CLPP-1/CLP1 is a Lon protease, when in fact they are independent proteases.

__

We have removed the word “Lon” to clarify this.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Soo et al. investigates the role of the mitochondrial unfolded protein response (UPRmt) during different organismal stresses. Using both loss-of-function and gain-of -function alleles of atfs-1, the gene encoding the transcription factor and main regulator of the UPRmt, the authors discover that ATFS-1 is both required and sufficient for the expression of genes associated with different types of cellular stresses including hypoxia, innate immunity, and antioxidant defense. Consistent with these gene regulations, gain-of-function atfs-1 animals were more resistant to specific cellular stresses, while loss of ATFS-1 animals were generally more sensitive.

Major comments

1.The authors mention that activation of the UPRmt by nuo-6 mutants or atfs-1(gf) do not activate the ER UPR or cyto-UPR gene expression targets (lines 111-113). However, they also find that atfs-1(gf) animals have 25% overlap with the ER UPR pathway (line 146-147). Is 25% overlap not substantial?

To determine whether ATFS-1 mediates any protective effect during ER stress, authors should test atfs-1(gf) and atfs-1(lf) animals' resistance to ER stress.

1. Authors should comment on the difference in outcomes with atfs-1(et17) and atfs-1(et15) animals to chronic oxidative stress (line 184-187).
2. Lines 258-260. The authors should make clear in this section that a previous study had already measured lifespans of atfs-1(gf) animals and found that it was reduced (PMID 24662282). Also, an elaboration on why this experiment was repeated would be warranted.
3. The authors find that atfs-1(gk3094) animals lived longer during infection with PA14 (line 208-211). Another study found that atfs-1(gk3094) animals died faster on PA14 (PMID 28283579), which should be mentioned and commented on.
4. At the request of the Editor, I was asked to comment on potential overlap between this manuscript and a recently submitted article submitted by the current authors (RC-2021-00651). There is only minor overlap in my opinion, with the finding in the current manuscript that the UPRmt is associated with stimulation of a pathogen defense program (innate immunity). Manuscript RC-2021-00651 goes into more detail regarding the mechanism of the UPRmt/innate immunity association and regulation.

Minor comments

Line 38: "Inside the mitochondria, ATFS-1 is degraded by the Lon protease CLPP-1/CLP1". The phrasing suggests that CLPP-1/CLP1 is a Lon protease, when in fact they are independent proteases.

Significance

The finding that the UPRmt regulates other cellular stress response pathways which provides resistance to a variety of stressors is of interest. However, associations of the UPRmt with increased resistance to exogenous stresses such as hypoxia and pathogen infection have been reported before (PMID 26234215, 25274306, 28283579), which might reduce the impact of the current manuscript to some degree.

This work would be interest to those in the fields of mitochondria, stress responses, and longevity.

My expertise is in stress responses, longevity, and host-pathogen interactions.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors carried out experiments, and mine published datasets, to further characterize the role of the ATFS1 transcription factor in mediating survival and lifespan in laboratory or stressed conditions. The role of ATFS-1 was assessed by using a loss-of-function deletion and two constitutive gain-of function mutants in which the mitochondrial leader sequence is not functional, resulting in continual nuclear translocation. The effect of ATFS1 loss or constitutive activation was assessed in both wild-type and mutant (mitochondrial function and long-lived mutants) strains, and either under standard laboratory conditions or in the context of a variety of physical, chemical, and pathogen stressors. Constitutive ATFS-1 activation upregulated genes from a number of stress-response pathways, and the loss of atfs-1 blocked upregulation of some stress-response genes by a variety of exogenous stressors, with little or no effect on baseline expression of those genes. Loss of atfs-1 also increased sensitivity to many exogenous stressors (not all mitochondria-targeting), and overexpression was generally protective. However, overexpression also decreased lifespan in the absence of exogenous stressor.

Major comments:

• Are the key conclusions convincing? Mostly, assuming sample size was adequate (see below). The only major conclusion that I would qualify is "ATFS-1 serves a vital role in organismal survival of acute stresses through its ability to activate multiple stress response pathways"-the data, as presented, does not make clear whether ATFS-1 directly activates these pathways (ie, by binding response elements in genes in those pathways), or indirectly influences them by altering the physiology of the worm).
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? No.
• 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. No.
• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. N/A
• Are the data and the methods presented in such a way that they can be reproduced? Mostly; see below.
• Are the experiments adequately replicated and statistical analysis adequate? Unclear; see below.

Minor comments:

• Specific experimental issues that are easily addressable:

In abstract, consider broadening/re-wording "Gene expression changes resulting from the activation of the mitoUPR are mediated by the transcription factor ATFS-1/ATF-5." Because a naïve reader may understand this to suggest that ATFS-1 is activated only by mitochondrial protein misfolding. Please indicate whether strains were outcrossed, and how often.

How was "young adult" defined? Were worms synchronized, and if so, how?

For the gene expression experiments, do I understand correctly that FUDR was used only for oxidative stress and adult day 2 experiments? Please clarify. Important: Please make clear how many replicates were performed for each experiment, and where relevant, how many worms were measured per replicate (e.g., stress survival and lifespan).

For 2-way ANOVA analyses, please specify p values of both main factors as well as interaction terms and posthoc analyses where relevant. - Are prior studies referenced appropriately? Yes. - Are the text and figures clear and accurate? Yes. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Yes:

In the second paragraph of the introduction, I suggest broadening slightly the description of why normal mitochondrial function is required for ATFS-1 important and degradation, because this helps the reader understand that any one of many perturbations to mitochondrial function (decreased bioenergetics, membrane potential, protein degradation, protein import; increased ROS; etc.) could prevent or reduce ATFS-1 import and degradation.

For Figure 1: The authors present their choice of genes to analyze as if, and interpret their results assuming, that each of these gene is ONLY regulated by the indicated stress response pathways. I think this is very unlikely. For example: is it certain that sod-3 and trx-2 are not also skn-1 regulated? How is "antioxidant" distinguished from the skn-1 pathway? Further clouding the water is the likelihood that nuo-6 and atfs-1 manipulations alter physiology in such a way that there are secondary/indirect stress pathways activated (for example: the authors show that ATFS-1 overexpression shortens lifespan. Perhaps this is why it appears that ATFS-1 overexpression also appears to cause a strong, although variable, upregulation of the cytosolic UPR?). The likelihood (in my opinion) that these genes are in fact regulated by more than one type of response element, and that the manipulations used to study these relationships have pleiotropic effects, do not invalidate the general conclusion that these pathways interact-but they do mean that the results should be discussed with more caveats regarding HOW they interact.

Figure 1 also illustrates why a more detailed description of sample size and statistical analysis should be provided. What was the "n"? What were the main effects and interaction terms of each 2-way ANOVA? The design is not full factorial and therefore does not permit a simple 2-way ANOVA (i.e., not all condition combinations are performed)-which responses precisely were compared to which? Were 2 2-way ANOVAs performed per mRNA?

The work shown in Figure 2 is a very nice way to leverage previous data to further explore this idea of cross-talk. I would suggest including a bit more meta-data in the supplemental data files related to each dataset. For example, what lifestages were used (were they all young adult?), was FUDR used, etc.

However, again, I don't understand how the authors can reach this conclusion: "Combined, this indicates that activation of ATFS-1 is sufficient to upregulate genes in multiple stress response pathways." (lines 152-153 but similar phrasing occurs multiple times) Could it not simply be that one form of cellular stress often eventually triggers broader cellular dysfunction, thus activating other cell stress pathways? Ie-how do we know whether these genes are directly regulated by atfs-1 binding regulatory elements, as implied by this phrasing?

The stress response experiments are very nicely done and very interesting. I appreciate that the authors did not shy away from describing counterintuitive results (eg et15 mutants showing increased sensitivity to chronic oxidative stress), and think that these results should also be briefly considered in the Discussion.

Figure 3: please report ANOVA interaction terms-these are what tell whether the inductions are in fact dependent on atfs-1 (not the post-hoc analyses). Again, it also appears that in some cases, there is an upregulation of certain genes with atfs-1 knockdown-please report all p-values (because there will be many, I recommend a supplemental table with all main and interaction and posthoc analyses). Again, the "n" also needs to be specified.

Figure 4 A-C appear to be lacking error bars? Please add. Perhaps relatedly-the effect size for 4A looks much larger than for 4B, but this does not come across in the text.

For Figures 4 and 6, please indicate sample size-number of independent experimental replicates, and number of worms per replicate (or range per replicate).

Lines 224-225 re. sod-2 mutants: these may also act by decreasing ROS signaling (less conversion of superoxide anon to hydrogen peroxide); also, why would this strain not be considered another long-lived mitochondrial mutant (like clk-1, isp-1 and nuo-6, to which it is contrasted)?

The confirmation that atfs-1 overexpressing strains are short-lived is very interesting. However, I think this statement "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." (lines 265-267 and similar in several places throughout the Discussion, eg line 279) should be altered to indicate that this was observed under controlled laboratory conditions. Eg, "...this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background under optimized laboratory conditions..."

Discussion: consider adding in a consideration of dose-response, both of knockdown of mitochondrial genes (eg, k/d of many mitochondrial genes promotes lifespan at low levels, but decreases lifespan with greater knockdown) and of stressors (chemicals, heat, etc; for chemicals, at the least, dose-response is very important, with low levels not infrequently triggering apparently beneficial stress responses, and higher levels causing toxicity).

Section beginning on line 384 "ATFS-1 upregulates target genes of multiple stress response pathways"-again, please revise to make clear that this work does not demonstrate direct regulation.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The mitoUPR has generally been viewed and tested as an isolated mitochondrial stress-specific response; the authors have built upon previous work to convincingly show that it is integrated with a variety of other stress response pathways. This is an important contribution to the field.
• Place the work in the context of the existing literature (provide references, where appropriate). The authors have done a nice job of this in their discussion.
• State what audience might be interested in and influenced by the reported findings. Researchers interested in stress response in general, and mitochondrial homeostasis and stress response in particular, as well as the relation of these to lifespan.
• 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. Mitochondrial response to exogenous stressors, particularly pollutants.

Referees cross-commenting

It seems to me that our reviews are in pretty good agreement. I agree with Reviewers 1 and 3 where they commented on things that I did not. While I did not consider the manuscripts as overlapping in the sense of being redundant, I very much like Reviewer 1's suggestion that they be published back to back and that the Discussion of each incorporate consideration of the Results of the other.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, Soo et al explore the role of the mitoUPR-associated transcription factor ATFS-1 as a hub in multiple stress response pathways controlling gene expression changes and resistance to a variety of exogenous and endogenous stressors. They found that ATFS-1 gain-of-function is sufficient to upregulate a number of genes involved in oxidative stress response, DAF-16-related response, hypoxia and innate immunity. Moreover, they found that many ATFS-1-responsive genes are upregulated under multiple stress conditions and by interventions that prolong lifespan. They also showed that ATFS-1 is required for stress response and resistance under different stress conditions. Finally, they demonstrate that ATFS-1 is not necessary for normal lifespan, but ATFS-1 gain-of-function decreases lifespan.

Major concerns:

1) This manuscript has some overlap with another manuscript from the same group recently submitted to EMBO J. Although I believe both manuscripts have sufficient elements to justify publication of two papers, I strongly recommend that these publications are made back-to-back and they should be discussed in context with one-another. While the main focus of the other manuscript is how mitochondrial mutations lead to improved bacterial pathogen response, it concludes ATFS-1 is key to explain how genes involved in this particular stress response are upregulated upon mitochondrial dysfunction. Their model is that mitochondrial mutations lead to upregulation of innate immunity genes via ATFS-1-mediated transcriptional activation. Here they show that ATFS-1 controls many other stress response pathways in addition to the innate immunity response. Somewhat contradicting their model in the other manuscript, here they show that ATFS-1 is not necessarily required for bacterial pathogen response. In contrast, they even found protection against PA in atfs-1 loss-of-function mutants. This could be explained in light of the fact that ATFS-1 appears to have a protective role under oxidative stress conditions (e.g., mitomutants or paraquat) whereas in worms that have no underlying stress, high ATFS-1 levels may be detrimental. This is consistent with the results in Figure 6. These aspects considered, I believe both manuscripts need to be revised back-to-back so that the data can be reconciled and discuss in context.

2) How is ATFS-1 function regulated in long-lived worms or under multiple stress conditions? Is there a common regulator such as oxidative stress or mitochondrial dysfunction? Both manuscripts would benefit from a clear understanding on how ATFS-1 is controlled under conditions where mitochondrial function is altered. Is mitoUPR required for this activation? If so, is mitoUPR upregulated in all interventions where ATFS-1 has been shown to play a role in stress response. Is there any intervention that controls longevity and does not trigger ATFS-1 response?

3) In Fig. 3, some of these genes appear to be unspecifically associated with different stressors. Therefore, it is difficult to rule out the participation of ATFS-1 in specific stress responses without looking at specific stress-responsive genes or a wider range of genes. For example, the conclusion that ATFS-1 does not control osmotic stress gene expression response comes from looking at 3 genes: sod-3, gst-4 and Y9C9A.8. gst-4 does not appear to be directly controlled by ATFS-1 regardless of the stressor. sod-3 is also upregulated by oxidative stress and Y9C9A.8 by anoxia. On the other hand, somewhat contradicting the authors' conclusions that ATFS-1 does not participate in osmotic stress response based on these 3 genes, ATFS-1 appears to be required for osmotic stress resistance.

Minor concerns:

1) The paragraph starting in line 107 is confusing. They write that "Constitutive activation of ATFS-1 in atfs-1(et 15) and atfs-1(et17) mutants resulted in upregulation of most of the same genes that are upregulated in nuo-6 mutants, except for gst-4" and later they state that "Activating the mitoUPR through the nuo-6 mutation, or through the constitutively-active ATFS-1 mutants did not significantly increase the expression of target genes from the ER-UPR (hsp-4; Fig. 1B) or the cyto-UPR (hsp-16.2; Fig. 1C)." I understand the upregulation of ER-UPR and cyto-UPR is not statistically significant (isn't it for hsp-16.2?), but the first sentence is not accurate if statistics is considered.

2) The authors should discuss why they think atfs-1(et15) gain-of-function mutant exhibited decreased resistance to chronic oxidative stress, while it is protected from acute oxidative stress. In fact, the et15 allele differs in many aspects in relation to the et17 and in some cases it behaves similarly to the gk3094 loss-of-function allele.

3) Fig 4I is very similar to Fig. 6A of the other manuscript which strengthen the notion that ATFS-1 is not required (it is rather detrimental) for bacterial pathogen response when no underlying stress (most likely oxidative) occurs.

4) In the paragraph starting in line 213, the authors conclude that "ATFS-1 is sufficient to protect against oxidative stress, osmotic stress, anoxia, and bacterial pathogens but not heat stress". The results do not unequivocally support a participation of ATFS-1 in oxidative stress or bacterial pathogen response, given the responses vary depending on the allele or condition.

5) "Combined, this indicates that ATFS-1 does not play a major role in lifespan determination in a wild-type background despite having an important role in stress resistance." It actually does, since ATFS-1 gain-of-function decreases lifespan.

6) Paragraph starting in line 359 needs to be discussed in light of the results of the other manuscript submitted by the authors to EMBO.

7) In Fig. 1C, it appears that atfs-1 loss of function increases hsp-16.2. Is that significant?

8) In Fig. 2, 4 and S1, it would be interesting to build one single Venn Diagram with all the lists of genes to see if there are common genes associated with multiple pathways and if there are many ATFS-1 target genes not associated with these classical stress or longevity pathways.

9) In Fig. 2, 4 and S1: What are the p values referred to?

10) In paragraph starting in line 85, the authors should include references that evidence the genes are bona fide markers of the stress response pathways.

11) Tables S2 and S3 are missing.

Significance

Nature and significance of the advance:

The study advances our knowledge about the role of ATFS-1 - a transcription factor involved in mitoUPR - in multiple stress response pathways.

Compare to existing published knowledge:

The role of ATFS-1 has been previously studied in the context of mitoUPR, although the present manuscript expands it to a variety of other stress response pathways. It is yet to be defined whether mitoUPR itself is promiscuously activated in response to different kinds of stressors or ATFS-1 may be activated independently of mitoUPR. As mentioned before, the present manuscript has considerable overlap with a manuscript from the same group under review in EMBO J. These manuscripts need to be discussed in light of one-another.

Audience:

The audience interested in this study is expected to be aging biologists, mitochondrial biologists, as well as researchers using C. elegans as a model organism.

Expertise:

I am interested in mechanisms of aging and their association with metabolism.

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Reply to the reviewers

Reviewer comments:

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

In this paper, the authors examine the relationship between the transcription factor Ribbon, its ribosomal protein gene (RPG) targets, and cell growth during the process of salivary gland tubulogenesis in the Drosophila embryo. This study builds upon previous work they published in 2016 (Loganathan et al., 2016). While the previous study identified RPGs as potential targets of Ribbon from ChIP-Seq analysis, they did not delve into the role of these targets in salivary gland morphogenesis. Here, the authors demonstrate that mutation of ribbon results in decreased cell volumes via immunostaining and image analysis. They identify and confirm RPGs as ribbon transcriptional targets using ChIP-SEQ, Microarray data, in situ hybridization, and qRT-PCR. They analyze these targets in an effort to identify a Rib consensus binding sites by MEME and find that Rib binding is not specific using EMSA. They suggest specificity arises from association with transcriptional cofactors. Binding with cofactors was confirmed by CO-IP and in vivo RNAi experiments demonstrated the requirement of these cofactors in mediating changes in cell volume during salivary gland tubulogenesis. They demonstrate that Ribbon regulation of cell growth via transcription of RPGs is not a universal mechanism for Ribbon function, as Ribbon regulates transcription of other genes in the context of tracheal development.

**Major comments:**

Results of all experiments are conclusive, and significant numbers of samples were noted for most figure panels. For a few panels the sample number/number of replicates was not noted, and it is recommended that the authors add this information (Figure 1F; 5B,C; 7B).

Additional experiments are not needed to support the conclusions presented in this work. The data and methods are presented clearly and the statistical analyses performed were appropriate.

In regard to microarray data, Figure 4E shows fold change as log2 values, but it is unclear if this is the case for Table S2. This should be clarified. The authors note in the text on page 7 that few targets show a greater than 1.5-fold change. Based on Figure 4E, this is a log2 value, and should be specified as such.

As the Rib antibody was generated in this study, it would be helpful to include data illustrating a confirmation of antibody specificity. This could include Rib antibody staining on rib mutant embryos, or showing a lack of band for ribbon in ribbon mutants on a Western blot. If the specificity has been published elsewhere, please add a reference.

**Minor Comments:**

As the microarray data was previously published in Loganathan et al 2016, as mentioned in the results section, this citation should also be included in the Methods section describing the Microarray data.

In the discussion section on page 15, a list of factors in the gene network are listed. What is viz.?

Reviewer #1 (Significance (Required)):

•As described in the introduction, the role of cell growth during embryonic tissue morphogenesis is a relatively unexplored topic. The authors point out that most previous studies describing regulation of tissue growth have focused on the role of mitosis and increased polyploidy, as in the gut (https://doi.org/10.1016/S0925-4773(00)00512-8 ), as primary mechanisms. In the case of the salivary gland, only a single endocycle occurs during embryogenesis and cells are post-mitotic, suggesting another mechanism is at play. This study identifies Ribbon as a mediator of cell growth and demonstrates that Ribbon mediates this function through transcriptional regulation of RPGs. In addition, they identify Ribbon cofactors that are important for salivary gland cell growth and tissue morphogenesis. Interestingly, they find that this mechanism for cell growth may be tissue specific, as Ribbon appears to regulate different genes in the trachea.

•This work has implications for the regulation of cell growth in other tissues and organisms and would be of broad interest to those studying organ development.

•In order to contextualize my review, I am a developmental biologist that works with Drosophila.

**Referees cross-commenting**

In regard to the comments by reviewer #2: I agree that point # 2 should be addressed to more thoroughly describe the method, but as the authors have looked at DNA Amplification at a time point following the normal endocycle, which occurs at stage 12, and DNA content is not significantly different, I don't think analysis of earlier stages would influence their conclusions.

Given that the authors do include some RNAi data for RPGs and Trf2, it would enhance the paper further to include M1BP and Dref RNAi data if quality reagents are available as described in point 5. Point 6 can be easily addressed. In regard to point 8, the effects of rib overexpression alone would be interesting to see given the ability of this construct to rescue the phenotype.

While I think points 3 and 7 are excellent ideas for a follow up study, I think they are outside of the scope of this paper. I do not view point 4 as essential to this study, as the study focuses on the regulation of transcription of the RPGs by Rib.

In regard to the comments by reviewer #3, I agree that points 1 and 2 should be addressed. It would be extremely difficult to address point #3 by dissecting out the tissue, but it could be addressed via further explanation in the text, as could point #4. I don't think minor points 4-6 need to be addressed, but the minor points 1-3 should addressed to improve the paper. For minor point #3, I would suggest the number of genes be included in Supplementary Table 1.

As reviewer #1, I think my comments should be addressed to improve the quality and clarity of the paper.

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

This paper reported a role for the BTB/POZ-domain transcription factor rib in mediating early cell growth of embryonic salivary gland (SG) cells. the authors show that during tubulogenesis of the salivary glands, rib binds the transcription start site of almost all SG-expressed ribosomal protein gene (RPG) and promotes their transcription, thus providing a material foundation for cell growth. Interestingly, in embryo trachea cells, rib targets do not include RPGs, which indicates that rib may use different mechanisms to regulate cell growth of different organs. In general, this is a well-written, well designed research article with many conclusions well-supported by experimental evidence. Listed below are a few issues (mostly minor/unessential) for the authors to consider.

**Major comments:**

1.Although in Figure 1G, the nucleus size is indistinct in rib mutant and wt cells at stage 15 and 16, Figure 1C appeared to look like that the rib mutant nuclei at stage 11, 13 and 14 are significantly smaller than those in wild type cells. The authors need to make sure that the rib phenotype has nothing to do with DNA amplification.

2.Please describe the details on calculating DNA volume by DAPI staining in the method session.

3.The authors have demonstrated weak DNA binding ability of Rib, and physical interactions between Rib with the known regulators of RPG transcription (Trf2, M1BP, and Dref), but what is the functional relationships between Rib and the known RPG regulators? e.g., does Rib function to promote DNA binding and transcriptional activity of Trf2, M1BP, and Dref, or vice versa?

4.To confirm the rib function on RPG translation, it is recommended to examine ribosomal proteins by western, and comparing the total protein content would also be helpful.

5.As Trf2, M1BP and Dref are physically interacted with Rib, it would be helpful to determine Whether M1BP and Dref knockdown can phenocopy the cell growth deficit observed in rib mutant SGs.

6.Page12, paragraph 3, "Thus, despite the shared requirement for Rib in embryonic cell growth of both tubular organs, Rib-dependent growth in the trachea is likely through regulation of alternative growth-promoting factors." Please list the potential growth-promoting factors targeted by Rib according to the Chip-seq data, if possible.

7.It would be interesting to determine whether rib mutation differently affect the secretory function of salivary gland at embryo, larva, pupa or adult stage.

8.Does Rib overexpression have any effects to SG development? Considering the authors adopted GAL4-UAS system to rescue Rib under Rib-KO, it would be interesting to see if Rib overexpression could cause an opposite overgrowth phenotype.

Reviewer #2 (Significance (Required)):

This paper discovered a new mechanism underlying organ-specific cell growth regulation during a specific time-window of animal development, which should be of interest to the field of cell and developmental biology.

Drosophila genetics; Developmental biology

**Referees cross-commenting**

I agree with all the other referees that the comments raised by reviewer #1 should be addressed entirely.

In regard to the comments by reviewer #3, all of the 4 major points are excellent and should be addressed, but it is okay to address points #3 and 4 by simple explanation or re-wording. I find the minor point #6 is nice to have but not essential, the rest should be addressed.

In case of my comments (reviewer 2), points #1,2,5,8 should be addressed, others are nice to have.

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

In the manuscript "The Ribb-osome: Ribbon boosts ribosomal protein gene expression to coordinate organ form and function" the authors show evidence that Ribbon mediates early cell growth in Drosophila embryonic salivary gland through direct interaction with ribosomal protein genes. The manuscript is well written while presenting novel and solid data. The data could be strengthened by some further analysis and clarification, but none of the issues raised represent major flaws.

**Key points:**

1.Cell segmentations: The way the cell segmentations / volume quantifications are presented it is impossible to judge their quality. The authors should provide the extracted geometries as Supplementary Data. The methods could be clearer on how the segmentations for cell and DNA volume were done; were the surfaces done manually, were there any image preprocessing steps etc.? In Figure 7C, it is not clear from the images whether cells or nuclei were segmented. Also, it would strengthen the work if the authors analysed the cell shapes (in particular cell height, and apical cell shape bias), considering that they mention it to be different in the Rib mutant. In addition, it would add to the manuscript if the authors could quantify the volume of the luminal space, of the epithelial layer in wt and mutant, and the bias in tube outgrowth.

2.The authors show nicely that the rib mutants have a smaller overall cell size, can this be the reason why the secretory tube in figure is smaller? In addition, if the overall size of the mutant and the WT is the same as suggested in figure 1H then why does the mutant larvae in figure 1f appear so much smaller than the WT in the same panel?

3.In figure 4f the authors see 4 out of 7 RPGs been significantly down-regulated, do they have an explanation for that? Why are not all 7 tested RPGs significantly down-regulated? Can it be that the results will be significantly improved by dissecting the tissue of interest instead of using whole embryos? Finally with what criteria were these 7 genes selected?

4.The authors state in their manuscript the limitations of the chip-seq and the fact that the 11 unbound RPGs are essentially a technical artifact. I suggest that the authors either perform ChIP on some of these RPGs to prove their point or that they ton down their statements about chip-seq limitations and Rib binding all SG-expressed RPGs

**Minor points**

The authors need to clarify in the text what is early and late stage of tubulogenisis.

In figure 1c the Mipp1 staining is of low quality and although the white lines help the reader on where to focus, noise vs signal is almost indistinguishable. Furthermore, the authors claim that they only take under consideration SG cells that show uniform membrane staining but Figure 1c does not show such uniform staining.

Figure 1d needs the addition of statistical analysis WT vs rib mutant st12 look very similar.

In their ChIP-seq data the authors identify 436 peaks that correspond to 413 genes. It is worth to add a pie chart depicting how many of those 413 are RPGs and how may are non-ribosomal.

Throughout the manuscript the authors exhibit nicely the effects of rib mutants. What happens to the tested genes in panel 4f when rib is overexpressed?

RPls are known to be involved in size regulation. If the authors use another driver than fkh to express Rib, Rpl19 etc will they still see similar phenotypes or not?

Figure 7b is hard to follow, the IP panels should be in agreement with the order that they appear in the text e.g., first experiment then controls

Reviewer #3 (Significance (Required)):

In the manuscript "The Ribb-osome: Ribbon boosts ribosomal protein gene expression to coordinate organ form and function" the authors show evidence that Ribbon mediates early cell growth in Drosophila embryonic salivary gland through direct interaction with ribosomal protein genes. As I am only vaguely familiar with the field, I would leave it to someone who is closer to judge the advance and relevance. But with the additional quantifications, the paper should be of interest more generally to developmental biologists who are interested in tubulogenesis, and if the authors make the 3D cell geometries available, the work should also be of interest to computational modellers with an interest in epithelial organization as segmented 3D cell geometries are still rare.

**Referees cross commenting**

Looking at all 3 referee reports, I find all points made by referee 1 either essential and/or easy to fix. As such, I would insist on all points made.

With regard to referee 2, I see points 1,5,8 as essential, and point 2 is too easy to do to not request it. The others I would consider nice-to-have, but not essential.

In case of my own report, I would insist on points 1 & 2. Among the minor points, points 4 & 6 are NOT essential. The others are either important or easy enough to fix.

I look forward to the views of my colleagues.

Our response to reviewer comments

We thank the reviewers for their very positive comments regarding the importance of this paper and for the constructive feedback they have provided. Indeed, we would be delighted to address every suggestion raised, but since we would also like to have this work published in a timely manner, it is quite helpful to have consensus among the three reviewers regarding which changes and experiments are the most important to include. Since all three reviewers felt it important to address all of the comments from Reviewer #1, we will do so. For the comments raised by reviewers #2 and #3, we will follow the consensus opinion and address those comments by changes in the text or by including more experiments. In this revision plan, we also address the comments that were considered to be beyond the scope of the current study.

Points raised by Reviewer #1

Include N values for all the figure panels: We will provide sample number information for those panels currently missing that information: Figures 1F; 5B, C; and 7B.

Microarray fold-change clarification: We will clarify that we are reporting the fold-change values in Table S2. As is standard with Volcano plots for reporting microarray data, Figure 4E is plotted as Log2 data.

Antibody validation: We will provide a supplemental figure with information about the Rib antiserum and its specificity.

Add citation regarding the microarray data: We will add the citation referring to the microarray data to the Methods section.

Uncommon word usage pg 15: We will remove “viz.”—contraction of a Latin phrase “videre licet” to mean “namely” or “specifically”—from the discussion of factors in the gene network, since it was clearly distracting.

Points raised by Reviewer #2

Appearance of Nuclei and Calculation of DNA volume: The rib mutant nuclei shown in Fig. 1C depict CrebA staining and were used only for identification of SG secretory cells – we did not measure nuclear volume in these samples. To eliminate any potential confusion, we have re-labelled the last column “3D cell volume”. All of the calculations of nuclear size (as a measure of DNA amplification) were carried out with DAPI-staining as shown In Fig 1G, which revealed no difference between WT and rib mutant SG secretory cells. Measurement of entire nuclear volume is critical, since, in any single focal plane, how much of the nucleus is captured varies. We will provide information detailing how DNA volume was obtained in the methods section.

SG cell size phenotypes of M1BP and Dref RNAi Knockdowns: We agree with the reviewers that determining if M1BP and Dref SG-specific RNAi also phenocopy the cell growth deficit observed in the rib mutant SGs is a meaningful experiment and could strengthen our conclusions. We will, therefore, perform this experiment. It should be noted, however, that whereas rib and Trf2 do not have significant levels of maternal mRNA or protein, both M1BP and Dref have high levels of both [based on ModEncode data; Flybase]. Thus, it may be challenging to deplete these genes with only SG driven expression of the RNAi constructs.

List of potential Rib-dependent growth promoting factors in the trachea: In the revised version, we provide the list of candidate growth genes bound by Rib from the tracheal Chip-Seq data as requested by reviewer #2 (and agreed upon by reviewer #1 as important) in the supplement.

Effects of Rib overexpression on SG cell growth: All of the reviewers agree that testing for a SG secretory cell over-growth phenotype with Rib overexpression is worthwhile and we will do this experiment. Nonetheless, we recognize that we may not see overgrowth phenotypes based on a few observations. Our ChIP-Seq data indicate that Rib binds neither the promoters of ribosomal RNAs [rRNAs; the other essential component of ribosomes] nor the promoters of known rRNA transcription factors. Based on a study from another group, it seems likely that Myc upregulates rRNA expression (Grewal et al., 2005). Correspondingly, myc is transcriptionally upregulated in the embryonic SG (supplemental panel 7C) and myc expression in the SG is independent of rib (i.e. Rib does not bind the myc gene based on the SG ChIP-Seq and myc levels in the embryonic SG do not change in rib null embryos based on microarray and whole mount in situs). Also based on ChIP-Seq, Rib binds its own promoter and, based on qRT-PCR experiments, represses its own expression (Loganathan et al., 2016). Thus, over-expression of Rib with GAL4:UAS driven expression may reduce rib transcription from the endogenous locus. Nonetheless, this experiment is still worth doing.

Points raised by Reviewer #3

Information on cell segmentations: In the revised manuscript, we will provide sample 3D views of cell volume quantifications as movie files. In the methods section, we will also make it clear that the surfaces were manually segmented and that no image preprocessing steps were performed. We will also provide the excel spread sheets on size calculations in a supplement. We will provide information in the legend for figure 7 that whole secretory cells were segmented for the calculations done for panel C. The information on cell shapes, apical membrane dynamics, and luminal volumes (including the assessment of developmental dynamics of tube elongation based on live-imaging construction of computational elastic and analytical viscoelastic models) has been presented in previous publications from our lab (Cheshire et al., 2008; Loganathan et al., 2016) and from work in other labs (Blake et al., 1998). We will include this information in the revised discussion and will include the appropriate citations.

Panel 1F and comment on the apparent smaller size of the rib mutant shown: rib mutant embryos show characteristic head invagination defects along with amioserosa and dorsal closure defects [Bradley and Andrew, 2001]. The partial embryo image in Panel 1F captures the head invagination defect making the embryo appear smaller. We will include images of whole embryos in the revised version to clarify that whole embryo volumes of rib mutants are comparable to WT for the representations shown in Fig. 1F.

Clarify early vs. late Tubulogenesis: Early SGs are stage 11, 12 – when the SG cells are internalizing. Late SGs are stages 13 – 16, when the glands are fully internalized. We will clarify this in the figure legend.

Statistics on Panel 1D: We will perform statistical analysis of growth profiles shown in Fig 1D as suggested by the reviewer and include the results in the figure or figure legend.

Pie-chart for RPG fraction: Given how crowded the figures currently are, instead of providing pie charts, we simply provide the fraction of the bound genes that are RP genes in the text. Using our set cut-off of 4.0: 12.9% of genes bound by Rib (with both drivers) were RP genes. Using the IDR platform for peak calling, 12.8% of bound genes were RP genes. In Fig 4A, we also include genes above the cut-off with one GAL4 driver, but not the other, as described in the legend.

Effects of Rib Overexpression: As discussed earlier, we will perform this experiment (please also see our response to the last comment by reviewer #2)

Order of presentation of co-IP results in Panel 7B: As requested, we will reorder the IP results in Fig. 7B as suggested by the reviewer to present first the results from the experiments and then the results from controls in accord with how we discuss the data in the results section.

Testing the functional relationships between Rib and known RPG regulators: We will not determine if Rib promotes DNA binding and transcriptional activity of Trf2, M1BP, and Dref, as this experiment was considered to not be critical for this paper by any of the three reviewers.

Panel 4F and tissue-specific RT-qPCR: We agree that it would be ideal to have tissue-specific qRT-PCR, but it is not technically feasible to dissect out enough embryonic SGs for analysis (as acknowledged by Reviewer 1). In future studies, we do plan to get that kind of information from single cell RNA sequencing (scRNA-Seq) of WT and rib mutant embryos, but there are a few hurdles to overcome before those experiments. In selecting the RP genes for qRT-PCR, we chose sample RpL and RpS genes, making sure to include at least one gene (RpS9) that was “not bound” by Rib based on ChIP-Seq criteria.

Determine Rib function on RPG translation: We will not examine levels of RP proteins by Western since this experiment was deemed be unnecessary for the current study by the three reviewers.

Effects of rib on the secretory function of the SG at the embryo, larva, pupa, or adult stage: We agree with the reviewer that these data would be interesting to have; as pointed out by reviewer #1, however, it’s a question for a future follow-up study.

Chip-Seq technical artifact / limitations: We don’t think we are incorrect in suggesting that the failure to detect Rib binding to all RP genes could be a technical artifact because of the following: (1) a direct examination of the binding tracts associated with every RP gene reveals a peak at/near the TSS. The values associated with those peaks do not always reach the cut-off, but when the peak values are lower than the cut-off, the signals in the flanking DNA are often also much lower than average (for details, see Supplemental Figure 1). (2) Among the RP genes whose expression went down significantly by qRT-PCR is RpS9 – an RP gene “not bound” by Rib, based on the cut-offs we followed.

Using another SG driver: We agree with reviewer #1 that the results obtained using the fkh-GAL4 driver for RNAi of RP regulators and RP genes are robust and sufficient to support the conclusion that Rib binds RPGs to regulate SG secretory cell size. Thus, we will not redo these experiments using another SG driver.

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Referee #3

Evidence, reproducibility and clarity

In the manuscript "The Ribb-osome: Ribbon boosts ribosomal protein gene expression to coordinate organ form and function" the authors show evidence that Ribbon mediates early cell growth in Drosophila embryonic salivary gland through direct interaction with ribosomal protein genes. The manuscript is well written while presenting novel and solid data. The data could be strengthened by some further analysis and clarification, but none of the issues raised represent major flaws.

Key points:

1.Cell segmentations: The way the cell segmentations / volume quantifications are presented it is impossible to judge their quality. The authors should provide the extracted geometries as Supplementary Data. The methods could be clearer on how the segmentations for cell and DNA volume were done; were the surfaces done manually, were there any image preprocessing steps etc.? In Figure 7C, it is not clear from the images whether cells or nuclei were segmented. Also, it would strengthen the work if the authors analysed the cell shapes (in particular cell height, and apical cell shape bias), considering that they mention it to be different in the Rib mutant. In addition, it would add to the manuscript if the authors could quantify the volume of the luminal space, of the epithelial layer in wt and mutant, and the bias in tube outgrowth.

2.The authors show nicely that the rib mutants have a smaller overall cell size, can this be the reason why the secretory tube in figure is smaller? In addition, if the overall size of the mutant and the WT is the same as suggested in figure 1H then why does the mutant larvae in figure 1f appear so much smaller than the WT in the same panel?

3.In figure 4f the authors see 4 out of 7 RPGs been significantly down-regulated, do they have an explanation for that? Why are not all 7 tested RPGs significantly down-regulated? Can it be that the results will be significantly improved by dissecting the tissue of interest instead of using whole embryos? Finally with what criteria were these 7 genes selected?

4.The authors state in their manuscript the limitations of the chip-seq and the fact that the 11 unbound RPGs are essentially a technical artifact. I suggest that the authors either perform ChIP on some of these RPGs to prove their point or that they ton down their statements about chip-seq limitations and Rib binding all SG-expressed RPGs

Minor points

The authors need to clarify in the text what is early and late stage of tubulogenisis.

In figure 1c the Mipp1 staining is of low quality and although the white lines help the reader on where to focus, noise vs signal is almost indistinguishable. Furthermore, the authors claim that they only take under consideration SG cells that show uniform membrane staining but Figure 1c does not show such uniform staining.

Figure 1d needs the addition of statistical analysis WT vs rib mutant st12 look very similar.

In their ChIP-seq data the authors identify 436 peaks that correspond to 413 genes. It is worth to add a pie chart depicting how many of those 413 are RPGs and how may are non-ribosomal.

Throughout the manuscript the authors exhibit nicely the effects of rib mutants. What happens to the tested genes in panel 4f when rib is overexpressed?

RPls are known to be involved in size regulation. If the authors use another driver than fkh to express Rib, Rpl19 etc will they still see similar phenotypes or not?

Figure 7b is hard to follow, the IP panels should be in agreement with the order that they appear in the text e.g., first experiment then controls

Significance

In the manuscript "The Ribb-osome: Ribbon boosts ribosomal protein gene expression to coordinate organ form and function" the authors show evidence that Ribbon mediates early cell growth in Drosophila embryonic salivary gland through direct interaction with ribosomal protein genes. As I am only vaguely familiar with the field, I would leave it to someone who is closer to judge the advance and relevance. But with the additional quantifications, the paper should be of interest more generally to developmental biologists who are interested in tubulogenesis, and if the authors make the 3D cell geometries available, the work should also be of interest to computational modellers with an interest in epithelial organization as segmented 3D cell geometries are still rare.

Referees cross commenting

Looking at all 3 referee reports, I find all points made by referee 1 either essential and/or easy to fix. As such, I would insist on all points made.

With regard to referee 2, I see points 1,5,8 as essential, and point 2 is too easy to do to not request it. The others I would consider nice-to-have, but not essential.

In case of my own report, I would insist on points 1 & 2. Among the minor points, points 4 & 6 are NOT essential. The others are either important or easy enough to fix.

I look forward to the views of my colleagues.

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

This paper reported a role for the BTB/POZ-domain transcription factor rib in mediating early cell growth of embryonic salivary gland (SG) cells. the authors show that during tubulogenesis of the salivary glands, rib binds the transcription start site of almost all SG-expressed ribosomal protein gene (RPG) and promotes their transcription, thus providing a material foundation for cell growth. Interestingly, in embryo trachea cells, rib targets do not include RPGs, which indicates that rib may use different mechanisms to regulate cell growth of different organs. In general, this is a well-written, well designed research article with many conclusions well-supported by experimental evidence. Listed below are a few issues (mostly minor/unessential) for the authors to consider.

Major comments:

1.Although in Figure 1G, the nucleus size is indistinct in rib mutant and wt cells at stage 15 and 16, Figure 1C appeared to look like that the rib mutant nuclei at stage 11, 13 and 14 are significantly smaller than those in wild type cells. The authors need to make sure that the rib phenotype has nothing to do with DNA amplification.

2.Please describe the details on calculating DNA volume by DAPI staining in the method session.

3.The authors have demonstrated weak DNA binding ability of Rib, and physical interactions between Rib with the known regulators of RPG transcription (Trf2, M1BP, and Dref), but what is the functional relationships between Rib and the known RPG regulators? e.g., does Rib function to promote DNA binding and transcriptional activity of Trf2, M1BP, and Dref, or vice versa?

4.To confirm the rib function on RPG translation, it is recommended to examine ribosomal proteins by western, and comparing the total protein content would also be helpful.

5.As Trf2, M1BP and Dref are physically interacted with Rib, it would be helpful to determine Whether M1BP and Dref knockdown can phenocopy the cell growth deficit observed in rib mutant SGs.

6.Page12, paragraph 3, "Thus, despite the shared requirement for Rib in embryonic cell growth of both tubular organs, Rib-dependent growth in the trachea is likely through regulation of alternative growth-promoting factors." Please list the potential growth-promoting factors targeted by Rib according to the Chip-seq data, if possible.

7.It would be interesting to determine whether rib mutation differently affect the secretory function of salivary gland at embryo, larva, pupa or adult stage.

8.Does Rib overexpression have any effects to SG development? Considering the authors adopted GAL4-UAS system to rescue Rib under Rib-KO, it would be interesting to see if Rib overexpression could cause an opposite overgrowth phenotype.

Significance

This paper discovered a new mechanism underlying organ-specific cell growth regulation during a specific time-window of animal development, which should be of interest to the field of cell and developmental biology.

Drosophila genetics; Developmental biology

Referees cross-commenting

I agree with all the other referees that the comments raised by reviewer #1 should be addressed entirely.

In regard to the comments by reviewer #3, all of the 4 major points are excellent and should be addressed, but it is okay to address points #3 and 4 by simple explanation or re-wording. I find the minor point #6 is nice to have but not essential, the rest should be addressed.

In case of my comments (reviewer 2), points #1,2,5,8 should be addressed, others are nice to have.

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

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---

Referee #1

Evidence, reproducibility and clarity

In this paper, the authors examine the relationship between the transcription factor Ribbon, its ribosomal protein gene (RPG) targets, and cell growth during the process of salivary gland tubulogenesis in the Drosophila embryo. This study builds upon previous work they published in 2016 (Loganathan et al., 2016). While the previous study identified RPGs as potential targets of Ribbon from ChIP-Seq analysis, they did not delve into the role of these targets in salivary gland morphogenesis. Here, the authors demonstrate that mutation of ribbon results in decreased cell volumes via immunostaining and image analysis. They identify and confirm RPGs as ribbon transcriptional targets using ChIP-SEQ, Microarray data, in situ hybridization, and qRT-PCR. They analyze these targets in an effort to identify a Rib consensus binding sites by MEME and find that Rib binding is not specific using EMSA. They suggest specificity arises from association with transcriptional cofactors. Binding with cofactors was confirmed by CO-IP and in vivo RNAi experiments demonstrated the requirement of these cofactors in mediating changes in cell volume during salivary gland tubulogenesis. They demonstrate that Ribbon regulation of cell growth via transcription of RPGs is not a universal mechanism for Ribbon function, as Ribbon regulates transcription of other genes in the context of tracheal development.

Major comments:

Results of all experiments are conclusive, and significant numbers of samples were noted for most figure panels. For a few panels the sample number/number of replicates was not noted, and it is recommended that the authors add this information (Figure 1F; 5B,C; 7B).

Additional experiments are not needed to support the conclusions presented in this work. The data and methods are presented clearly and the statistical analyses performed were appropriate.

In regard to microarray data, Figure 4E shows fold change as log2 values, but it is unclear if this is the case for Table S2. This should be clarified. The authors note in the text on page 7 that few targets show a greater than 1.5-fold change. Based on Figure 4E, this is a log2 value, and should be specified as such.

As the Rib antibody was generated in this study, it would be helpful to include data illustrating a confirmation of antibody specificity. This could include Rib antibody staining on rib mutant embryos, or showing a lack of band for ribbon in ribbon mutants on a Western blot. If the specificity has been published elsewhere, please add a reference.

Minor Comments:

As the microarray data was previously published in Loganathan et al 2016, as mentioned in the results section, this citation should also be included in the Methods section describing the Microarray data.

In the discussion section on page 15, a list of factors in the gene network are listed. What is viz.?

Significance

•As described in the introduction, the role of cell growth during embryonic tissue morphogenesis is a relatively unexplored topic. The authors point out that most previous studies describing regulation of tissue growth have focused on the role of mitosis and increased polyploidy, as in the gut (https://doi.org/10.1016/S0925-4773(00)00512-8 ), as primary mechanisms. In the case of the salivary gland, only a single endocycle occurs during embryogenesis and cells are post-mitotic, suggesting another mechanism is at play. This study identifies Ribbon as a mediator of cell growth and demonstrates that Ribbon mediates this function through transcriptional regulation of RPGs. In addition, they identify Ribbon cofactors that are important for salivary gland cell growth and tissue morphogenesis. Interestingly, they find that this mechanism for cell growth may be tissue specific, as Ribbon appears to regulate different genes in the trachea.

•This work has implications for the regulation of cell growth in other tissues and organisms and would be of broad interest to those studying organ development.

•In order to contextualize my review, I am a developmental biologist that works with Drosophila.

Referees cross-commenting

In regard to the comments by reviewer #2: I agree that point # 2 should be addressed to more thoroughly describe the method, but as the authors have looked at DNA Amplification at a time point following the normal endocycle, which occurs at stage 12, and DNA content is not significantly different, I don't think analysis of earlier stages would influence their conclusions.

Given that the authors do include some RNAi data for RPGs and Trf2, it would enhance the paper further to include M1BP and Dref RNAi data if quality reagents are available as described in point 5. Point 6 can be easily addressed. In regard to point 8, the effects of rib overexpression alone would be interesting to see given the ability of this construct to rescue the phenotype.

While I think points 3 and 7 are excellent ideas for a follow up study, I think they are outside of the scope of this paper. I do not view point 4 as essential to this study, as the study focuses on the regulation of transcription of the RPGs by Rib.

In regard to the comments by reviewer #3, I agree that points 1 and 2 should be addressed. It would be extremely difficult to address point #3 by dissecting out the tissue, but it could be addressed via further explanation in the text, as could point #4. I don't think minor points 4-6 need to be addressed, but the minor points 1-3 should addressed to improve the paper. For minor point #3, I would suggest the number of genes be included in Supplementary Table 1.

As reviewer #1, I think my comments should be addressed to improve the quality and clarity of the paper.

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

1. General Statements [optional]

On behalf of the authors, I would like to thank the three reviewers for providing a valuable feedback on our manuscript. We appreciate that they all considered that the first part of our study conveys novelty to the field of neuroblastoma research, while being coherent with recent studies aimed at identifying the NB cells-of-origin through transcriptomics and single-cell RNA-sequencing approaches. We indeed identified a transcriptional signature that distinguishes LR-NBs from HR-NBs, revealing that these two NB subgroups are better discriminated by the core transcriptional signature shared by the distinct SA cell types, rather than by the transcriptional specificities of any of these cell types, as recently debated. Of note, our findings unveil that the sympatho-adrenal transcriptional program facilitates NB formation but concomitantly restricts its malignant potential. We also wish to thank the reviewers for acknowledging that, in contrast to previous studies, we pursued further by testing the functional relevance of this signature through a combination of in vitro and in vivo experiments. We thereby identified NXPH1 and its receptor α-NRXN1 as ones of the very first factors showing an anti-metastatic activity in the context of NB. Uncovering NXPH1/α-NRXN signaling as a possible target to treat metastatic HR-NBs gives our study considerable clinical relevance.

We consider that the critics and recommendations provided by the three reviewers are positive and pertinent. We are thus willing to address nearly all the reviewers’ concerns and suggestions within the scope of a revision, including performing additional in vivo experiments, as explained in details in the following section. We hope that the planned revisions will be sufficient to make our manuscript suitable for publication.

__ __

2. Description of the planned revisions

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

**Summary:**

In the reviewed manuscript, the authors aimed to characterize the sympathoadrenal (SA) transcriptional landscape that defines low- and high-risk neuroblastomas (LR-NBs and HR-NBs respectively). In particular, they analyze previously published Affymetrix U219 expression profiles of 18 low- (n=8) and high-risk (n=10) neuroblastomas, and 2 fetal human adrenal glands. The authors define transcriptional signatures of LR- and HR-NBs, and further unbiasedly classified them in 4 clusters defining groups of patients with different prognosis (as tested using the 498 SEQC cohort). Within these transcriptional signatures, the authors delineated a SA signature using a human fetal adrenal gland transcriptional profile recently published (Kildisiute et al. 2021), that can discriminate low-risk neuroblastomas. From these genes, the authors further select NXPH1 and NRNX1-2 as promising targets for extensive experimental in vitro and in vivo validation, including validation in cell cultures, and xenografts, to determine that NXPH1/alpha-NRXN1-2 signaling is sufficient for NB tumor growth, and that the expression of either stimulates the metastatic potential of NB cells.

**Major comments:**

1- The cohorts and data used by the authors to conduct the main analysis of the paper are already published, and thus the contribution of the analysis is incremental. In particular, the authors analyzed arrays from a limited cohort size, in comparison with others available sequenced with RNA-seq (e.g. 176 HR- and 322 non-HR NB in 498 SEQC; 224 HR- and 342 non-HR NBs included in the Westermann-genecode19 cohort; and 80 HR- and 20 non-HR in the Jagannathan cohort). Furthermore, the 12,000 most-expressed genes (out of ~20,000 available) were analyzed by the authors, as opposed to more than 40,000 (coding and non-coding) included in a normal RNA-seq study. Only the 498 SEQC dataset provides 12,000 genes significantly up-regulated in either high-risk (n~5,500) or non-high-risk (n~7,000). The differences between datasets could influence the results of the study. For example, in the reviewed manuscript, genes with a high expression in LR-NB (compared to fAG) included DNMT3B, SEMA5A, SOX5, and TET1, all of which have a significantly higher expression in HR-NBs of the 498 SEQC cohort. The quality of the manuscript will be enhanced with consistent results obtained by conducting the same reported analysis in larger cohorts.

Reply: To define the transcriptional signatures associated to the aetiology of LR- and HR-NBs and to the malignant behavior of HR-NBs, we first needed to compare the transcriptomic signatures of LR-NB and HR-NB samples to the one of a non-tumoral, healthy tissue such as the fetal adrenal gland. The online databases cited by the reviewer #1 do not contain any healthy samples, thus precluding the possibility to use it for the first step of our analysis. This is why we decided to use as a starting point the cohort of samples from the Hospital Sant Joan de Déu (HSJD cohort), which further provided the advantage of comparing samples from patients all diagnosed and treated at the same facility. We then used the SEQC database in different steps of our analytic strategy (Fig.S1F, 2F-H, 3A-B, S3) to test the relevance and coherence of the results obtained with the HSJD cohort in the context of a larger cohort. As mentioned by the reviewer #1, we indeed focused our analysis on the 12,000 most-expressed genes. We did so to follow the recommendations of the software Phantasus for transriptomic analyses of mammalian datasets.

2- In the reviewed manuscript, PHOX2A and PHOX2B are significantly more expressed in both LR-NB and HR-NB compared to fAG. This is also the case for other adrenergic markers including TH and DBH. Oppositely, the expression of cortex markers (i.e. STAR and CYP11A1) is significantly higher in fAG. Nevertheless PNMT is not significantly up-regulated in fAG in comparison to LR-NB nor HR-NB. Is it possible that the fetal adrenal glands analyzed include a large proportion of cortex that confounds the transcriptional signals? The quality of the manuscript will be enhance if the authors could establish what proportion of the fAG transcriptional signal belongs to cortex, and if they account for its influence in the analysis.

Reply: The samples of human fetal adrenal gland from which RNA was extracted were obtained from donations (samples staged at 22 weeks post-conception or 2 days after birth) and evaluated by a pathologist who confirmed their correct preservation before sample processing. As fetal adrenal glands are very small tissues, successfully separating the cortical and adrenal regions requires micro-dissection, which was not applied. These samples were instead processed entirely, presenting a ratio of medulla/cortex tissue according to their developmental stage.

3- A recent published paper (Bedoya-Reina et al. 2021) study the differences of HR-NB and LR-NB from a single-cell perspective. In the published manuscript, the authors conclude that LR-NBs are enriched in cells that resemble chromaffin and sympathoblast cells, while the high-risk neuroblastomas are enriched in undifferentiated cells that resemble cells with progenitor characteristics in post-natal adrenal gland. This is broadly consistent with the conclusion reached by the authors in the manuscript under review. It will enhance the content of the reviewed manuscript if the authors compare their transcriptional signatures with the recently published transcriptional signatures in this paper to answer the following questions:

-1) to what extent the transcriptional signatures for HR-NBs (4 hierarchical clusters incl.) in the manuscript under review resembles that from the published undifferentiated cluster (nC3) enriched in HR-NBs, and the progenitor cluster (hC1) in post-natal adrenal gland;

-2) to what extent the transcriptional signatures for LR-NBs (4 hierarchical clusters incl.) in the manuscript under review resembles that from the published NOR (nC7, nC8, and nC9) enriched in LR-NBs, and that from the chromaffin cells (hC4) enriched in post-natal adrenal gland;

-3) how is the expression of NXPH1 and alpha-NRXN1-2 in the reported LR- and HR-NBs, and adrenal gland.

Reply: As stated by the reviewer #1, our findings are indeed in agreement with the main conclusions recently reported by Bedoya-Reina et al (Bedoya-Reina et al, 2021). We agree with the reviewer #1’s suggestion that a detailed comparison of our transcriptomic signatures with those of Bedoya-Reina et al would be interesting. We will thus perform this comparison and provide these complementary results in the revised version of the manuscript.

4- In the discussion, the authors indicate that they do not aim to identify the transcriptional signature associated to NB origin but rather use the component of the SA lineage that distinguish LR- and HR-NBs. This statement implies that neuroblastoma can originate from any cell in the developing SA lineage (i.e. SCP, bridge, chromaffin and sympathoblast), a controversial assumption that requires further proof. In particular, when discussing about the core sympathoadrenal signatures enriched in LR-NBs and HR-NBs, the authors obtained a SA signature of genes shared by at least 3 of the 4 SA cell signatures. Further justification needs to be provided as for why (in particular) one of these SA cell signatures exclude the sympathoblast/neuroblast contribution.

Reply: We decided to use as a core SA signature the genes shared by at least 3 of the 4 SA cell types to avoid being too restrictive, the SCP signature being particularly distant from the 3 others. As such, the list of genes shared by all 4 cell types consists of 663 genes, of which only 51 are retrieved in our list of 503 LR vs HR DEGs. Conversely, the list of genes shared by Bridge cells, Chromaffin cells and Sympathoblasts (but not shared by SCPs) consists 3,530 genes, of which 199 are retrieved in the list of 503 LRvsHR DEGs. These complementary results, which can be discussed and provided if required, therefore suggest that the core SA signature discriminating LR-NBs from HR-NBs represents mostly the Bridge-Chromaffin-Sympathoblast lineage and excludes the SCP identity. They are therefore in agreement with the recent notion that NB cells-of-origin derive from the sympathoblast-chromaffin lineage.

5- Some of the most interesting results in the paper are limited to proportions in a subset of top-ranked genes. It will be valuable to set the analysis in an hypothesis driven context, add probabilities, test names, and corrected p-values to the results.

Reply: Our study is based on the initial hypothesis that LR- and HR-NBs might differ in the way they exploit the transcriptional program underlying their developmental origin. To get a deeper insight into this notion we performed a sequential differential expression analysis of primary samples of LR-NBs, HR-NBs and human fetal adrenal gland using the web-based Phantasus software. This software identifies differentially expressed genes between groups using the Limma R package, as detailed in the Methods section. As such, basic statistics for significance analysis were performed using a modetared T-test (as specified in the Limma R package) and FDR-adjusted P-values were set to PAdditionally, top-ranked genes of SA clusters were selected as part of a heuristic approach aimed at highlighting the clinical implication of the transcriptional clusters retrieved in our analysis. The relationship between their expression levels and patient survival was further analyzed using the SEQC database (Fig. S1E). Next, and in contrast to previous studies, we tested experimentally the validity of our analytical findings correlating the expression of SA-c1 genes with a better patient prognosis. To this aim, we selected the candidate gene NXPH1, one of the top-ranked genes from the SA-c1 subset, on the basis of several complementary arguments (listed in response to the reviewer #2’ comment #4). We thereby analyzed how modulating the expression of NXPH1 or that of its receptor α-NRXN1 affect the growth and metastatic potential of human NB cells. The results obtained argue for the validity of our model, by proposing that the neural crest-derived sympatho-adrenal developmental program, in particular the SA-c1 signature, plays a complex role in NB tumorigenesis: it facilitates tumor growth but blocks metastasis formation, hence opposing NB malignancy.

**Minor comments.**

6- In comparison with other cohorts that include low- and intermediate-risk NBs as non-HR NBs, the reviewed data specifically includes low- and high- risk NBs. It is important that the authors include a characterization of intermediate-risk neuroblastomas in their analysis.

Reply: The samples forming the HSDJ cohort were all obtained from NB patients diagnosed and treated at the Hospital Sant Joan de Déu. Several clinical and biological parameters were used for classification, among which the age of the patient. If we apply the cut-off point of 1 year (used at the time the samples were obtained), our cohort does not include any intermediate-risk NB. If we apply the cut-off of 18 months which is now more usual, our cohort would contain only one case (#HSJD-NB14 - aged 16 months at the time of diagnosis) that could be classified as intermediate-risk.

7- Further details and figures on what precise criteria was used to remove the sample #LR-08 is required. How including this sample changes the reported results?

Reply: As explained in the Methods section, before comparing the transcriptomic landscapes of LR-NBs and HR-NBs, we first assessed the sample dispersion by performing a principal component analysis. This analysis identified one outlier (#LR-08) that was clearly distant from all the other NB samples (both LR- and HR-NBs). We thus removed this sample to limit the dispersion and variability that would have impacted the subsequent analyses, as recommended by the Phantasus guidelines. We will provide an illustration of the PCA including this outlier. We believe that performing de novo the whole bioinformatical analysis including this outlier would not bring any novel significant conclusion.

8- GO-term distribution was assessed using the 50 most-enriched GO-terms. How would the results change if all the significant GO terms were analyzed?

Reply: We will re-analyse the GO-term distribution by including all the significant terms.

9- Was the SEQC 498 (GSE62564) dataset obtained with microarrays (as indicated in the methods) or with RNA-seq (i.e. Illumina HiSeq 2000)?

Reply: Similar results were obtained using either the SEQC database obtained with microarrays or the one obtained with RNAseq. The data presented in our manuscript correspond to the ones obtained with the RNA-seq SEQC database.

10- In methods, the first quartile (Q1) in SA-c1 has a higher limit in 487 samples and the fourth quartile the lowest limit in 4, how many samples (out of 498 NBs) were excluded and why?

Reply: As explained in the Methods section and in Fig. 2F, the complete SEQC cohort was included in this survival analysis. To subdivide the 498 samples of the SEQC cohort into 4 expression quartiles, we evaluated whether the expression level of each of the 242 SA-c1 genes (corresponding to 573 ref-seq IDs) in a given patient sample was above or below the mean expression of that gene in the complete cohort. Samples were then distributed into quartiles based on the number of genes presenting an expression level above the mean. As detailed in the Methods section, the resulting sample distribution was as follows: 487≤Q1≤360 (124 patients); 359≤Q2≤250 (125 patients); 249≤Q3≤135 (126 patients) and 134≤Q4≤4 (123 patients).

11- In the 503 DEGs between LR-HR NBs, NTRK2 and MYCN are not included, even if the HR samples included MYCN amplified tumors. Can the authors comment on this?

Reply: MYCN did not pass the cut-off when comparing its expression levels in LR-NB and HR-NB samples (showing an adjusted P=0.10226 for a cut-off of adjusted PNTRK2 was present in our initial 12,000 gene dataset, but it was not differentially expressed in any of the comparisons made (LR vs fAG: adj-P=0.4916; HR vs fAG: adj-P=0.63757; HRvsLR: adj-P=0.90431)

12- The authors mention that the top 30 genes found in cluster c1 (and also in c2) are correlated with favorable patient prognosis. Is it the case that *all* the genes in c1 (and also c2, c3 and c4) are significantly associated with a favorable or else unfavorable prognosis?

Reply: As presented in the datasheet “KM analyses” of Table S3:

• 32 out of the 33 genes (97%) of the cluster c2 correlate to an unfavorable prognosis, the 33th gene showing no particular correlation.

• 29 out of the 32 genes (91%) of the cluster c3 correlate to a favorable prognosis, 1 gene correlates to an unfavorable prognosis and the last 2 do not show any particular correlation.

For the clusters c1 and c4, we focused on the top 30 genes because these clusters contain numerous genes (338 and 100, respectively). The results obtained showed:

• All the top 30 genes (100% of the genes tested) of the cluster c1 correlate to a favorable prognosis

• 23 out of the top 30 genes (77% of the genes tested) of the cluster c4 correlate to an unfavorable prognosis, whereas the other 7 genes do not show any particular correlation

We believe that these results are convincing enough. However, if considered mandatory we will assess the prognosis of all the genes found in clusters c1 and c4.

13- The high expression of a (significant?) number of genes in cluster c4 is observed in patients with worst outcome (i.e. lower event-free survival), including ATR, HIF1A, ING2, POLR2L, SRPRB (498 SEQC, analyzed with R2).

Reply: Indeed, 23 out of the top 30 genes (77% of the genes tested) of the cluster c4 correlate to an unfavorable prognosis, which appears to us as a significant number of genes. We will test whether the expression of the remaining genes forming the cluster c4 also correlate to an unfavorable prognosis.

14- Regarding the 242 genes in the core SA signature, although its a smaller number, the expression of several genes in the core SA signature with a higher expression in HR compared to LR belonging to clusters 2, 3, and 4 is observed in worst outcome patients in the 498 SEQC cohort (CHD7, DNMT1, HMGA1, HSD17B12, LBR, LSM7, MCM4, NKAP, POLA1, and others). Is this small fraction significant?

Reply: The genes presenting a higher expression in HR-NBs than in LR-NBs are found either in cluster c2 or cluster c4. The core SA signature retrieved 262 genes of the 503 LR vs HR DEGs, of which 14 belong to cluster c2 (including CHD7, DNMT1, HMGA1, LBR, LSM7, MCM4, and POLA1) and 3 to cluster c4 (UQCRFS1, NKAP and HSD17B12). As shown in the “KM analyses” datasheet of Table S6, these 17 genes all correlated with an unfavorable prognosis.

15- In Kildisiute et al. 2021, NRXN1 is expressed in SCPs, while NXPH1 is expressed in bridge, chromaffin and sympathoblastic cells. How are the microenviroment of these cells regulating the expression of these genes in a developmental context (particularly as sympathoblastic cells are know to have larger proliferative capabilities than SCPs)? how is this cell heterogeneity replicated by a NB cell line? are mesenchymal and adrenergic cells expressing differentially NRXN1 and NXPH1?

Reply: Unfortunately, the literature about NXPH1 remains very limited (less than 40 articles referenced in Pubmed) and nothing is known about the regulation of its expression during development. The data from Kildisiute et al (Kildisiute et al, 2021) indeed identified NXPH1 in the signatures of bridge cells, chromaffin cells and sympathoblasts, while its receptors NRXN1 and NRXN2 were found in the transcriptomic signatures of all 4 SA cell types. Interestingly, the data provided by Kildisiute et al further established that the expression of NXPH1, NRXN1 and NRXN2 is specifically enriched during the pseudo-time transition from bridge cells to sympathoblasts. This suggests that NXPH1/α-NRXN signaling might be particularly important at that stage and could participate in regulating this transition. But this remains purely speculative and it will need further investigation.

We initially used a panel of 10 human NB cell lines harboring distinct characteristics in terms of genetic profile and morphological properties. We did not find any specific correlation between NXPH1 or α-NRXN1/2 expression and the different types of NB cell lines. We will provide an illustration of this observation in the revised version of the manuscript.

NB cells can convert or be reprogrammed from an adrenergic state, which is less chemoresistant in vitro, to a mesenchymal state (van Groningen et al, 2019). As asked by the reviewer #1, we investigated the expression of NXPH1 and α-NRXN1 in relation with the mesenchymal vs adrenergic status of NB cells (using the dataset GSE90803 from (van Groningen et al, 2019). We found that both genes are expressed at higher levels in cells of the adrenergic phenotype, suggesting that NXPH1/α-NRXN signaling might be particularly relevant for the maintenance of this phenotype. If needed, we will provide an illustration of this observation in the revised version of the manuscript.

16- Figure 1B and C, 2B,D: might the information provided be enhanced? otherwise these inserts might be excluded.

Reply: We thought that the panels presented as Fig.1B, C and 2B, D would be helpful to the readers. We could remove them if the editors and reviewers consider it mandatory.

17- Figure 3D: Kildisiute et al. 2021 data and GTEX available at human protein atlas indicate expression of NRXN1 and NXPH1 in developing and adult adrenal gland. Might the results illustrated suggest a confounding effect in the sampled fetal adrenal glands, perhaps from cortex?

Reply: The samples of human fetal adrenal gland from which RNA was extracted were obtained from donations (samples staged at 22 weeks post-conception or 2 days after birth) and evaluated by a pathologist who confirmed their correct preservation before sample processing. As fetal adrenal glands are very small tissues, successfully separating the cortical and adrenal regions requires micro-dissection, which was not applied. These samples were instead processed entirely, presenting a ratio of medulla/cortex tissue according to their developmental stage.

18- The authors conduct extensive experiments in NRXN1, and make conclusions about its role in for instance metastasis, nevertheless the LR-NB/HR-NB SA signal only includes NRXN2. Can the authors comment on the differences between NRXN1s and NRXN2?

Reply: NRXN1 and NRXN2 were both found to be differentially expressed between LR vs fAG and HR vs fAG, and were thus retrieved among the list of 3.096 common DEGs (Table S3). NRXN2 was further found in the list of 503 LR vs HR DEGs (adjusted P=0.037), showing higher expression levels in LR-NBs than in HR-NBs (see Fig.3D). NRNX1 presented an expression profile comparable to that of NRXN2 (Fig.3D) but did not pass the cut-off (adjusted P=0.38) due to an increased variability in HR-NB samples and was thus absent from the list of LR vs HR DEGs. In vitro, the expression levels of NRXN1 and NRXN2 showed comparable patterns. When we initiated the functional experiments there was no fluorescence-conjugated antibody available to detect and sort α-NRXN2, but there was for α-NRXN1. This is the practical reason that led us to focus on α-NRXN1 in the second part of our study.

Reviewer #1 (Significance (Required)):

The significance of the study relies in investigating the role of selected targets in neuroblastomas within a risk group. In particular, HR-NBs have poor outcomes and are generally metastatic at the time of diagnosis.

The results of the manuscript are somehow consistent with a recently published manuscript analyzing LR- and HR-NBs from a single-cell perspective. The manuscript will be enhanced by conducting the suggested comparison between the reviewed and the reported results. The authors further need to comment why HR-NBs markers, particularly MYCN is not recovered in the LR-NB/HR-NB and the LR-NB/HR-NB SA signals. Also they need to comment on possible confounding effects in the fetal adrenal gland.

The paper is directed to a broader audience of cancer and developmental biologists, and computational biologist. Yet further statistical support needs to be provided.

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

**Summary:**

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2.

In this paper, Fanlo-Escudero et al., determines gene signatures differentiating low-risk (LR) neuroblastoma (NB) from high-risk neuroblastoma (HR-NB), as well as LR- and HR-NB as an entity from human fetal adrenal gland. They identify a transcriptional signature corresponding to a core sympathoadrenal lineage that can discriminate between LR-NB and HR-NB. This signature is composed of genes associated with favorable patient outcome. The authors further choose one gene, NXPH1, for functional analysis and investigates the effects this gene has on NB progression using in vitro assays, chick CAM assay and mouse in vivo models. The authors conclude that this transcriptional signature can distinguish LR-NB from HR-NB and that NXPH1 is involved in NB cell growth.

**Major comments:**

• Are the key conclusions convincing? The key conclusions are 1) a core SA lineage signature can discriminate between LR-NB and HR-NB, and 2) NXPH1 represses NB malignancy (in terms of metastatic capacity) and is a therapeutic target. The first conclusion is indeed convincing, and not contradictive to common beliefs. The second conclusion is poorly supported by data. The authors perform a range of experiments using in vitro and in vivo settings, but lack some fundamental experiments and overstate their findings.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Several claims should be softened, re-phrased and/or clearly marked as preliminary or speculative. No data nor claims need to be removed.

For example, the following statements need to be changed:

1- Page 10, second paragraph: The authors state "Remarkably, NXPH1 and α-NRXN1/2 levels increased in all the NB cell lines harbouring a sphere-forming capacity (Fig. 3E), thereby revealing a strong positive correlation between the expression of NXPH1 and α-NRXN1/2 and the acquisition of a NCC stem cell identity". The authors only show that NXPH1 is expressed in 8 out of 10 NB cell lines. Sphere-forming capacity is displayed in a relative and not absolute scale which makes it difficult to assess which cell lines that do form spheres and to what extent. The capacity to form spheres (from low to high) does not correlate to the levels of NXPH1 in the different cell lines.

Reply: In its current form, Fig.3E presents via a heatmap representation how the expression of selected genes changes after growing cell lines in sphere-forming conditions as compared to basal (normal) ones. We understand from various reviewers’ comments that this representation has been misleading. We will change it, showing more explicitly the expression levels both in basal and sphere-forming conditions and will bring further details on how the sphere-forming ability of each cell line was assessed and characterized.

2- Page 13, paragraph 1. The authors write "...these data revealed that NXPH1/α-NRXN1 signaling is necessary and sufficient for NB tumor growth in vivo". This is an overstatement. Tumors still form, meaning that NXPH1 signaling is not sufficient.

Reply: Indeed, tumors still form after xenografting sh-NXPH1 or sh-NRNX1 cells but they form with a decreased frequency. Specifically, sh-NXPH1 cells formed tumors in 4 out of 6 xenografted mice, and the 4 tumors all showed a markedly reduced volume. Tumors formed from sh-NRNX1 cells were observed in only 2 out of 5 xenografted mice, with 1 of the 2 tumors showing a markedly reduced volume. We consider that these results support the conclusion that inhibiting NXPH1/α-NRXN1 signaling impairs tumor growth, affecting both tumor initiation and tumor growth. We however understand the reviewer #2’s comment and will thus rephrase this part accordingly. In addition, we will provide complementary data showing the mean volume of the tumors generated in the distinct experimental conditions.

3- Throughout the text, the authors convert their statements. One example is page 15, first paragraph. They write "...growth of NB cells but markedly restrict their metastatic potential", but they do not show this. Instead, they only address the opposite situation - Knockdown enhances metastasis. This is not equal to their statement. See other experiments in other sections. The authors need to go through the manuscript and make sure that they explain their conclusions to actually fit their experiments.

Reply: We will follow the reviewer #2’s recommendation and will rephrase the conclusions whenever needed to better fit to the experimental results.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary to evaluate the paper as it is, and do not ask authors to open new lines of experimentation.

**Issues to respond to:**

4- The authors should more clearly explain why they choose to further study NXPH1 (second highest on the list), involved in synaptogenesis and neurotransmission, instead of SOX6, highest on the list, that is highly relevant in neural crest development.

Reply: The combination of several reasons led us to choose NXPH1 for functional studies:

• NXPH1 is a secreted factor, whose activity might be much more easy to target and modulate in future pharmacological/clinical assays than that of a transcription factor like SOX6
• NXPH1 and its receptor NRNX2 both came out in the list of SA-c1 genes, and NRXN1 presented a comparable expression profile (higher levels in LR-NBs than in HR-NBs, although it did not pass the cut-off required to appear in the SA-c1 list), emphasizing the putative importance of this signaling pathway in NB tumor biology
• The functional involvement of NXPH1 or that of its receptors has never been addressed in cancer formation or progression to date

  5- When the authors investigate the expression of NXPH1 and other genes and compare that with sphere-forming capacity (Fig. 3E and page 10) they analyze expression in cells cultured in basal medium while sphere-forming capacity is measured after 5 weeks in restricted medium. How does the expression of the analyzed genes change under these conditions?

Reply: In its current form, our Fig.3E is actually showing how the expression of the analyzed genes changes after growing cell lines in sphere-forming conditions as compared to basal (normal) ones. As explained above (reviewer #1, point #1), we understand that this representation has been misleading and we will modify it.

6- Is the subpopulation of NRXN1+ cells low (1.5%) because these samples are from aggressive ("High-risk") cell lines?

Reply: All the NB cell lines used in this study derive from HR-NB tumors. As mentioned by the reviewer #3, there is no cell line modeling low-risk neuroblastoma to date. We indeed observed that the proportion α-NRXN1+ cells, as detected by FACS, was very low in all three cell lines tested. A similar observation was made using cells dissociated from three different patient-derived xenografts. We believe that a similar observation made in 6 samples of distinct origins highlights the consistency of finding a low proportion of α-NRXN1+ cells in NB samples.

7- The authors state "...the number of cells quantified per tumor section was decreased by ~50% for the α-NRXN1+-deprived cells relative to their control (Fig. 3J, K), thus revealing that α-NRXN1+ cells are required to support NB tumor growth in vivo". This is not a correct conclusion. This experiment shows that a-NRXN1- cells do not grow and expand to the same extent as control cells. They cannot say that a-NRXN1+ cells support NB growth without comparing growth between a pure a-NRXN1+ and control cells.

Reply: Unfortunately we could not assess the growth of purified α-NRXN1+ cells, given the low number of α-NRXN1+ cells that could be sorted as compared to the numbers of cells required to perform a CAM assay. We thus opted for comparing the growth of total SK-N-SH cells with that of SK-N-SH cells in which the α-NRXN1+ subpopulation had been experimentally removed. We believe that the results obtained convincingly argue for the importance of the α-NRXN1+ subpopulation in promoting NB proliferation and growth. Nevertheless, we understand the reviewer #2’s comment and will rephrase the conclusion.

8- The authors use shRNAs to knock down NXPH1. They enrich their cells by two means - puromycin or doxocycline. This results in equal cell populations. The authors however state that they use doxocycline to circumvent the growth arrest they observe with puromycin selection. They need to elaborate on this and show why this would be the case and what difference the two methods do and show.

Reply: We generated two types of knock-downs: a constitutive one and an inducible one. Puromycin was used to select constitutive knock-downs, whereas doxycycline was used to trigger sh-RNA production in an inducible manner, in stable clones previously established through neomycin selection. We apologize if this was not stated clearly enough in the manuscript and we will correct it.

9- The major flaw of this paper is that the authors use one cell line in total, and even more that they use the same cell line for both knockdown and activation. Since they do show that different NB cell lines have different expression levels (ranging from high to absent), they should choose one cell line for KD and one for overexpression. The authors could also do a rescue experiment with knockout and gain-of-function (e.g., construct that will not be targeted by the shRNA) in the same cells.

Reply: Since NXPH1 is a secreted protein, we needed a cell line that expresses both NXPH1 and its receptors to expect noticing effects on NB cell behavior when their expression is reduced. We reasoned that performing a gain-of-function of NXPH1 in a cell line that does not express its receptors would have no interest, and vice versa. We also believe that it is more conclusive to perform gain- and loss-of-function experiments in the same cell line, because of the likely differences in cell behavior and aggressiveness of distinct cell lines. We however agree that our conclusions would be strengthened if similar conclusions were reached using different cell lines. We will thus perform growth and metastasis assays both in vivo and in the CAM using NXPH1 and α-NRXN1 shRNAs in an additional cell line. We will moreover consider performing rescue experiments and will think about the best methodology to do so.

10- They only use one shRNA after trying several (Fig. S4). The efficiency is substantially variable and not convincing. As stated also elsewhere in this review, they need to check protein level. And to ensure that their results are not off-target they should perform at least some crucial experiments with two shRNAs.

Reply: We agree that the decreased mRNA levels caused by NXPH1 and α-NRXN1 shRNAs showed variability. Yet, they were sufficient to significantly reduce cell viability, which was impaired by two distinct shRNA constructs, both for NXPH1 and α-NRXN1. To complete these experiments as recommended by the reviewer #2, we will assess how NXPH1 and NRXN1 expression is altered at the protein level by western-blotting. We will moreover address possible off-target effects by RT-qPCR.

11- Why don't the authors add BrdU post-implantation? This is easily done in the egg considering the accessibility and would better reflect the proliferation in vivo.

Reply: Adding BrdU pre-implantation allowed us to get a read-out of the global proliferative behavior of NB cells over the whole post-implantation duration. Adding it at the end of the post-implantation would have only allowed us to assess the proliferative behavior of cells at the end of the experiment. We believe that this would have been less informative.

12- Why do the authors switch between CAM and mouse xenografts? I understand that the mouse model must be employed for "metastasis", but can it be explained why and when they perform the different "tumor growth" experiments?

Reply: The CAM assay was used for 2 reasons: 1) when cell numbers were limiting (i.e. testing the importance of the α-NRXN1+ subpopulation for tumor growth), and 2) to perform a gain-of-function strategy using a recombinant rNXPH1 protein and testing its effects on tumor growth over a duration of 1 week. Such experiment would not have been possible using mouse xenografts, due to the extended experimental duration (7-8 weeks) of this assay and to the need for repeated rNXPH1 injections. The rNXPH1 gain of function experiment in the CAM and the NXPH1/α-NRXN1 loss-of-function experiment using mouse xenografts were performed concomitantly.

13- Why do the authors do left ventricle injections for metastatic studies and not AG implantations?

Reply: We reasoned that cell injections into the left ventricle were ideal to test the organotropism of metastatic NBs, as this methodology facilitates cell dissemination and colonization of organs targeted by NB metastasis such as the liver and bone marrow. Cell implantation into the adrenal gland is especially useful to study cell growth in one of the primary sites of NB growth, which was not our experimental purpose at that stage of the study.

14- The measurement of bioluminescence is very difficult to interpret. The authors discuss metastatic spread, but the images show only large blobs covering the heart and areas surrounding it, especially for the sh-αNRXN1. To be able to say that the cells have colonized specific organs the authors need to dissect these organs and perform staining. I see it as tumors recur rather than particularly metastasize when they re-appear after 6 weeks.

Reply: The parameters for bioluminescence detection were set equally for all experimental conditions. The differences in bioluminescence intensities observed in mice injected with control cells compared to those injected with shNXPH1 and shNRXN1 cells explain why it is so intense in the case of shNXPH1 and shNRXN1 cells.

As suggested by the reviewer #2, we had further dissected the mice and recovered the organs of interest. We will provide additional data confirming that an intense bioluminescent signal was effectively detected in the liver and hind legs (containing bone marrow) of mice injected with shNXPH1 and shNRXN1 cells, but not in those injected with control cells.

15- How do the authors explain results presented in Fig. S5: There are more HuNu+ cells but tumor size is unchanged?

Reply: In our experimental CAM setup, 5·105 SK-N-SH cells were embedded in 10μl of Matrigel, which served as a matrix facilitating tridimensional NB cell proliferation. The addition of rNXPH1 increased the number of HuNu+ (NB) cells per section and per mm3 (Fig.4G, H and Fig.S5C), without significantly increasing the tumor area (Fig.S5D) nor the tumor/matrigel volume (data not shown in the current version, but it will be included in the revised version). As illustrated in Fig. 4G, the matrigel was not totally filled with NB cells, even at the time of recovery. We thus deduced from these observations that more NB cells progressively filled the matrigel, without reaching the point where they significantly altered the tumor/matrigel volume. Nevertheless, we can provide additional data revealing that the addition of rNXPH1 caused a slight, yet reproducible increase in the tumor/matrigel weight, in agreement with the increased cell density already shown in Fig.S5C.

• Are the suggested experiments realistic for the authors? It would help if you could add an estimated cost and time investment for substantial experiments.

Some suggested experiments take time (orthotopic implantations, rescue experiments, adding cell lines and # of shRNAs).

However, as long as the authors discuss and address their methods for in vivo growth (in ovo vs in vivo vs their choice of metastasis model), an orthotopic AG model is not necessary. The authors should however consider it for future studies.

Experiments required to support their conclusions: A rescue experiment and use of different cell lines for KD and overexpression is somewhat time-consuming, as well as ensuring KD at protein level and include an additional shRNA in crucial experiment. I expect that this would take 2-4 months.

• Are the data and the methods presented in such a way that they can be reproduced? 16- The authors should elaborate on their methods, but in general they are reproducible.

Reply: As requested, we will bring further details on the experimental setups.

Are the experiments adequately replicated and statistical analysis adequate?

17- In several places the number of replicates is questionable. Especially at the end of page 26, the authors state that they have performed n=1-4 replicates. N=1 replicate is never ok. In several instances they do n=2 replicates. This can be acceptable but the authors could address this.

Reply: When assessing the sphere-forming capacity of the different NB cell lines, some cell lines only produced spheroids in 1 of the 4 replicates tested. This is a result in itself, which helped us classifying cell lines based on their sphere-forming capacity. We understand that this Methods paragraph was elusive. We apologize for it and will clarify this aspect.

**Minor comments:**

• Specific experimental issues that are easily addressable. Mainly text changes can be seen as minor. For experiments and other issues, see other sections.

• Are prior studies referenced appropriately? Yes. 18- The reference list is not coherently styled.

Reply: We understand that using numbered references can be annoying. We will adapt the reference format to stick to the guidelines of the specific journal to which the manuscript will be addressed.

• Are the text and figures clear and accurate?

19- Overall, the paper is written in a complex way and difficult to easily comprehend. For example, the authors need to clarify several issues on the material they use and experiments they perform. I suggest substantial re-writing to better convey their messages. Sentences should be short and clear, data explained in the context of it was derived.

Reply: We will take into consideration the reviewer #2’s suggestion and modify the manuscript to facilitate its comprehension.

The following text edits and clarifications are required:

20- Page 3. The authors write "cell-of-origin" in several places, this should be changed to "cells-of-origin" (i.e., plural). The view that all NBs originate from only one cell is too simplistic, and the authors should definitely edit this considering that they are investigating different subgroups of NB.

Reply: We will correct this mistake.

21- Page 5. The authors MUST define where the material from the 18 NB patients as well as fetal AG derive from. There is no reference, and taken from the material&methods section, the transcriptome data from these data has not been generated by the authors themselves?

Reply: The transcriptomic data used herein have indeed been previously generated by two co-authors of the study, and the corresponding reference is cited (ref #20; (Gomez et al, 2015). All the NB samples included in our transcriptomic analysis were obtained at the time of diagnosis from patients attended at Hospital Sant Joan de Déu (HSJD, Barcelona, Spain). Tumors were evaluated by a pathologist and only the snap-frozen pre-treatment samples showing at least 70% of viable tumor content were included for analysis. Neuroblastoma risk assessment was defined by the International Neuroblastoma Staging System (INSS). Samples of normal fetal adrenal gland (n=2) were used as a non-tumoral reference tissue. Total RNA from frozen samples was extracted by TRIzol® Reagent. High quality RNA (RINe>7.00) was hybridized to Human Genome U219 microarray plates at the Functional Genomic Unit, Institut d’Investigacions Biomèdiques August Pi i Sunyer (IDIBAPS, Barcelona, Spain) according to Affymetrix standard protocols. Microarray data are deposited in NCBI (#GSE54720). We will include this information in the Methods section of the revised version of the manuscript.

22- Why do the authors choose to work with the data set from Jansky et al in particular?

Reply: Actually, we chose to work with the data from Kildisiute et al. (ref #16 (Kildisiute et al, 2021). We selected this study because: 1) they identified the transcriptional signatures of the 4 SA subtypes relevant to our study and additional related signatures of interest (adrenal cortex, mesenchyme…), 2) these data were obtained from human tissues, and 3) these signatures were easily accessible from their supplementary data.

23- Page 7, paragraph 1. The authors write "Remarkably, 67% of the 503 genes found in this signature, which formed the cluster c1, are both associated with a neural identity and a better patient outcome". I do not agree that this is remarkable and the authors should remove this word.

Reply: We will remove the term “Remarkably”.

24- Page 10, second paragraph. The authors should clarify that the expression levels of the displayed genes are derived from qPCR analysis (if I have understood that correctly, I had to find and guess this from the M&M section), as well as explain how they have set the scale for sphere-forming capacity and what this corresponds to. What do the colors actually represent?

Reply: We apologize for this information lacking in the Results section. We will precise that the expression levels were assessed by RT-qPCR, we will add a representation of their expression levels in basal culture conditions and will improve the explanation of the assessment of the sphere-forming capacity of the NB cell lines.

25- Page 11 and onwards. The authors write "deprived of their a-NRXN1+ subpopulation". This is highly confusing and difficult to read. The authors should write "a-NRXN1- subpopulation"

Reply: We will follow the reviewer #2’s recommendation and change the text for "α-NRXN1- subpopulation".

26- Page 11, end of paragraph 2. The authors write "...arguing that NXPH1/α-NRXN signaling could control NB growth and/or aggressiveness". Number of cells do not directly correlate to aggressiveness, and this needs to be re-phrased to only state what the experiment actually shows - proliferation of a-NRXN1- cells.

Reply: We will rephrase this sentence according to the reviewer #2’s recommendation.

27- I am in favor of using the CAM assay as a complementary system. The authors however use this to define "...required to support tumor growth in vivo". The CAM assay using NB (i.e., transformed cells) shows the growth of these cells in response to presence of blood vessels and not a full tumor micro-environment. This should be clarified.

Reply: We will clarify this aspect.

28- As stated in the previous comment, the authors write "...required to support tumor growth in vivo". The next paragraph has the following headline "NXPH1/α-NRXN signaling stimulates NB growth". This is to me the same thing. The authors should elaborate on how these differ, or if they use them to show the same thing, clearly state that.

Reply: We will better explain how these distinct pieces of evidence are complementary and reinforce the conclusion that NXPH1/α-NRXN signaling stimulates NB growth.

29- The authors conclude that NXPH signaling can be used as a therapeutic target. This would however be extremely difficult considering the opposing effects shown on growth vs metastasis. I agree that it is important to find means to inhibit metastasis, but that does not mean we can allow for enhanced growth of the primary tumor. A better reflection would be to use this as a biomarker, but this can only be predictive/speculative since the authors do not perform for example a tissue microarray to show this at IHC protein level, something that is currently the practice in the clinic.

Reply: While we agree with reviewer #2 that we cannot allow for enhanced growth of the primary tumor, we believe that having identified a secreted factor whose activity inhibits NB metastatic potential is a novel and important finding. We did not wish to suggest that our experimental setup could be directly applied to inhibit the metastatic dissemination of HR-NB tumors. However, we believe that our findings can set the basis of a therapeutic design in which NXPH1/α-NRXN signaling would be enhanced locally to prevent/block metastases from HR-NB tumors.

As mentioned in the Discussion section (page 17), one study reported that NXPH1 can be used as a DNA methylation biomarker associated with a good prognosis for NB patients (reference #54, (Decock et al, 2016).

**Material and Methods:**

30- The authors have misspelled the cell line SK-N-BE(2)c.

Reply: Indeed. We will correct this mistake.

31- Why are some cell lines grown in 20% FBS? This is not standard and could impact the results.

Reply: The 3 cell lines of our panel which were grown in 20% FBS correspond to the 3 cell lines of the mixed subtype, including SK-N-SH, SK-N-Be(2)c and IMR-32 cells. These cell lines have been established and originally grown in presence of a high FBS content (Tumilowicz et al, 1970; Biedler et al, 1973; Ciccarone et al, 1989). In our hands and as recommended by the colleagues that provided us with these cell lines, growing the cell lines in presence of 20% FBS was indeed crucial to sustain their morphological heterogeneity. While we agree with the reviewer #2 that culture conditions could affect cell behavior in vitro, we wish to emphasize that our main conclusions are derived from in vivo experiments. We are thus convinced that our main findings were not impacted by in vitro culture conditions.

32- The authors should state what the tumor volume limit in their ethical permit is (page 30).

Reply: The tumor volume limit was set at 1,500 mm3 as specified by our ethical committee.

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

33- Fig. 3E. As discussed elsewhere, the authors should clarify the scale/meaning for sphere-forming capacity

Reply: As explained above, we will modify the representation of the results shown in Fig.3E to improve their clarity and facilitate their comprehension.

34- Fig. 4D. What do the numbers (i - vi) refer to? I cannot find this in the figure, figure legend, text or material&methods.

Reply: These numbers were used to call different tumors and show their GFP content, as appearing in the lower part of this panel. We will precise this information in the corresponding figure legend.

35- The authors do not present the tumor volume in Fig. 4. The authors discuss tumor growth in the text and this data should be included.

Reply: We agree with the reviewer #2’ suggestion and will present tumor volumes in the revised version of the manuscript.

36- Fig. S4. Knockdown efficiency is variable, and efficiency does not correlate to growth capacity. Especially because of this, the authors need to investigate this at protein level.

Reply: As requested by the reviewer #2, we will investigate the knockdown efficiency at the protein level.

Reviewer #2 (Significance (Required)):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. This paper is partly within the scope of the ongoing debate of NB origin (see references below). This paper is however not as extensive, provides no new patient material (applies data from Jansky et al), and do not address the actual cell-of-origin (which the authors themselves also clearly states). This paper provides new gene signatures that can be used to define low-risk vs high-risk patients which is highly important to the field, but these signatures are not unexpected and does not add a significant advance to the field. The authors also do not address how these signatures could be applied clinically. The authors do not use any new methodology. With this said, with revision of the paper, it will still add to the current focus on NB biology research.

• Place the work in the context of the existing literature (provide references, where appropriate). 37- There is a recently initiated, important and extensive debate about the cells-of-origin for NB. The authors indeed bring this up in the paper and also state that they do not intend to add to this debate. They use data from one paper from referenced debate above, and I would argue that because of this fact, and that they extract gene signatures from it, they do, at least partly, touch on the NB cells-of-origin debate, and the authors should put their results into context, from a big picture perspective. As of now, they dodge this complex issue.

References: Dong et al., Cancer Cell 2020; Hanemaaijer et al., PNAS 2021; Jansky et al., Nat Genet 2021; Kameneva et al., Nat Genet 2021; Kildisiute et al., Sci Adv 2021; Furlan et al., Science 2017).

Reply: We understand the reviewer #2’s argument. We will thus try to put our results in perspective regarding the NB cells-of-origin.

• State what audience might be interested in and influenced by the reported findings.

This paper will be interesting for scientists within the neuroblastoma field, in particular those working on defining NB subgroups in correlation to developmental stages.

• 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. Reviewer's expertise: Neuroblastoma, neural crest, trunk neural crest, chick embryos, mouse models, in vitro models

Parts of paper outside expertise of the reviewer: Analysis of the bioinformatics data (i.e., extracting signatures).

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

**Summary: short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).**

Dr. Le Dréau and colleagues provide a transcriptional analysis comparing low versus high-risk neuroblastomas using a cohort of 18 patients. By comparing them to normal transcriptional signatures obtained from human fetal adrenal glands, they conclude that low risk tumors share a specific core sympatho-adrenal developmental program, which is associated with favorable patient prognosis. Among this signature, they specifically assess the role of NXPH1/a-NRXN in vitro and in vivo using different models (cell lines, PDX-derived cell lines, mouse and chick xenografts). They propose that NXPH1/a-NRXN axis promotes neuroblastoma tumor growth via cell proliferation, and inhibits metastases.

**Major comments:**

• Are the key conclusions convincing?

There are major points that need to be addressed before being convinced by the conclusions.

1- The choice for using the SKNSH cell line, among others, to study the role of NXPH1/a-NRXN axis need to be explained. Indeed, whereas there is no cell line modeling low-risk neuroblastoma, authors should properly illustrate the basal expression of NXPH1/a-NRXN in the cell lines and not the ratio provided in Fig3E. If I understood well, according to Fig3F, only 1.5% of SKNSH cells express NRXN1. Could the authors provide FACS plots? And explain how they can sort high and low expressing cells among 1.5%? And then how do they justify using shRNA approach in a cell line in which only 1.5% are concerned cells? Also, the authors should prove the efficiency of the shRNA used on each specific target for both in vitro and in vivo studies by WB.

Reply: We chose the SK-N-SH cell line for experimental assays based on the following facts: 1) the expression levels of NXPH1 and α-NRXN1/2, 2) this cell line showed the highest sphere-forming capacity, 3) this cell line harbored the highest percentage of α-NRXN1+ cells detected by FACS among the different cell lines tested, and 4) this cell line is of a mixed type, which is supposed to encompass more cell heterogeneity than other (N, I and S) types, thus reproducing more faithfully the complex heterogeneity of primary NB tumors.

In a revised version of the manuscript we will provide data on NXPH1 and a-NRNX1/2 expression levels in basal culture conditions, and will improve the representation of Fig.3E to facilitate its comprehension. The method used to sort α-NRXN1+high, α-NRXN1+low and α-NRXN1- cells is explained in the Methods section (page 25). As requested by the reviewer #3, we will provide FACs plots to illustrate the sorting method.

As requested by the reviewers #2 and #3, we will assess the shRNA efficiency by testing the knockdown at the protein level.

2- The conclusion of inhibition of metastatic process is not supported by enough data. To achieve such a conclusion, authors should provide more than one in vivo experiment (which need to be completed already with the proof of protein deregulation). Some in vitro characterization of metastatic properties such as invasion and migration assays and/or transcriptional analyses could be done.

Reply: We agree with the reviewer #3 that that our conclusion on the anti-metastatic ability of NXPH1/α-NRXN signaling would be reinforced by complementary experiments. To this aim, we propose to test how NXPH1/α-NRXN knockdown affects the metastatic potential of the SK-N-SH cell line and of another cell line in the CAM assay. This assay can indeed be used to assess not only NB tumor growth (as we already did), but also NB cell invasion in target organs (such as the liver and the bone marrow), thus mimicking a metastatic dissemination.

3- Why don't the authors use the transcriptome dataset of 498 patients to realize a more powerful comparative study of low versus high risk tumors (Zhang et al, Genome biology, 2015)? The authors should show the expression plot of NXPH1/a-NRXN in low versus high risk patients, in their cohort of 18 patients but also in the cohort of 498 patients. How do the authors reconciliate the idea that NXPH1/a-NRXN could be associated to stem cell identity but low risk tumors?

Reply: As explained in response to the reviewer #1’ (comment #1), our strategy entailed comparing the transcriptomic signatures of LR-NB and HR-NB samples to the one of a non-tumoral, healthy tissue such as the fetal adrenal gland. The online SEQC database cited by reviewers #1 and #3 does not contain healthy samples, and therefore could not be used for this initial step of the analysis. This is why we decided to use as a starting point the cohort of samples from the Hospital Sant Joan de Déu, which further provided the advantage of comparing samples from patients all diagnosed and treated at the same facility. We then used the SEQC database at different steps of our analytic strategy (Fig.S1F, 2F-H, 3A-B, S3) to test the relevance and coherence of the results obtained with the HSJD cohort in the context of a larger cohort.

As requested by the reviewer #3, we will provide a dot-plot representation of the expression levels of NXPH1 and its receptors in both the HSDJ and SEQC cohorts.

At this point we can only speculate on the association between NXPH1/α-NRXN expression and stem cell identity. This correlation might simply reflect the fact that cells from human NB cell lines return to a transcriptional program closer to their neural crest-derived identity when grown in sphere-forming conditions (as suggested by the increased expression of p75/NTR). Alternatively, this correlation might reflect the ability of NXPH1/α-NRXN signaling to retain cells in an immature state. Such ability could explain how NXPH1/α-NRXN signaling participates in promoting primary tumor growth, and the fact that their expression is increased in LR-NBs as compared to normal fetal adrenal gland. On the other hand, NXPH1/α-NRXN expression is higher in LR-NBs than in HR-NBs, and our findings suggest that this is linked to the anti-metastatic ability of NXPH1/α-NRXN. We could further imagine that by favoring stem cell identity NXPH1/α-NRXN signaling might also provide LR-NB cells with an enhanced ability to “re-enter” a normal developmental path or to be eliminated. In this regard, it is worth reminding that LR-NBs are detected earlier during development than HR-NBs, and sometimes show the puzzling ability to regress spontaneously.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

Details of experiments and supplementary experiments have to be provided (see previous question).

• 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.

4- Additional details of the experiments have to be provided (cf above): levels of expression of NXPH1/a-NRXN in cell lines, FACS analyses to prove enrichment and/or depletion, WB for validation of shRNA knock-down etc...Moreover, the conclusion that NXPH1/a-NRXN axis inhibits metastatic potential of neuroblastoma is supported by only one in vivo experiment using SKNSH cell line with shRNAs anti-NXPH1/a-NRXN. It should be completed with invasion/migration assays in vitro for example, and/or transcriptional signature of tumors obtained +/- shRNAs anti-NXPH1/a-NRXN. Ideally, these results could be validated in an additional model.

Reply: As mentioned above, we will perform additional experiments following the reviewer #3’s recommendations, including assessing NXPH1 and α-NRXN1 knockdown efficiency at the protein level, assessing how knocking down NXPH1 and α-NRXN1 expression alters the in vivo growth and metastatic potential of an additional cell line, and studying how knocking down NXPH1 and α-NRXN1 alters the metastatic potential of NB cells using a second and complementary metastasis assay (CAM assay).

• 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

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

Yes, Material and methods section is well described. But, several points are missing:

5- The paragraphs describing how RNAs from 18 patients and fetal adrenal glands were obtained, how good was the quality, and how transcriptomes have been realized and sequenced are missing.

Reply: The transcriptomic data used herein have indeed been previously generated by two co-authors of the study, and the corresponding reference is cited (ref #20; (Gomez et al, 2015). All the NB samples included in our transcriptomic analysis were obtained at the time of diagnosis from patients attended at Hospital Sant Joan de Déu (HSJD, Barcelona, Spain). Tumors were evaluated by a pathologist and only the snap-frozen pre-treatment samples showing at least 70% of viable tumor content were included for analysis. Neuroblastoma risk assessment was defined by the International Neuroblastoma Staging System (INSS). Samples of normal fetal adrenal gland (n=2) were used as a non-tumoral reference tissue. Total RNA from frozen samples was extracted by TRIzol® Reagent. High quality RNA (RINe>7.00) was hybridized to Human Genome U219 microarray plates at the Functional Genomic Unit, Institut d’Investigacions Biomèdiques August Pi i Sunyer (IDIBAPS, Barcelona, Spain) according to Affymetrix standard protocols. Microarray data are deposited in NCBI (#GSE54720). We will include this information in the Methods section of the revised version of the manuscript.

6- The sequences of shRNAs have to be provided.

Reply: We will provide the oligo sequences used to generate shRNAs against NXPH1 and aNRNX1.

-Are the experiments adequately replicated and statistical analysis adequate?

Yes

**Minor comments:**

• Specific experimental issues that are easily addressable.

7- The authors should show the basal expression of their genes of interest in the patients, cell lines and PDX-derived cell lines, to justify the choice to work then with SKNSH cell line. In addition to the ratio they show in Fig3.E.

Reply: As explained above, we will provide more details on the expression levels of NXPH1 and α-NRXN1/2 in the HSJD and SEQC cohorts and in the NB cell lines used in our study.

8- Authors should also illustrate the FACS analyses they realized in this study, in order to appreciate the quantity of positive cells that are either enriched or depleted.

Reply: The methodology used to sort α-NRXN1+high, α-NRXN1+low and α-NRXN1- cells is explained in the Methods section (page 25). As requested by the reviewer #3, we will provide FACs plots to illustrate this methodology.

9- Authors could precise in their schemes that DOX is maintained in vivo.

Reply: We will follow the reviewer #3’s suggestion.

10- The number of mice need to be integrated in each experiment.

Reply: The numbers of mice used to assess growth and metastasis in vivo were included in the corresponding figure legends (Figs. 4D, 4E and 5C) and appear discreetly on the panel 4D (to the right). We will follow the reviewer #3’s recommendation and add these details on the corresponding figure panels.

• Are prior studies referenced appropriately?

11- No some elements are not right in the introduction:

• Mutations of PHOX2B are not associated to poor prognosis.

• Original publications could be provided instead of reviews.

• Genetic alterations in NB are not only 16%, the authors forgot to mention TERT and ATRX.

• Maybe the NXPH1 methylation in ref 54 could be more explicit, if DNA methylation is detected on NXPH1, it would be of poor prognosis because driving low expression ..?

Reply: We will follow the reviewer #3’s critics and correct the mistakes and information lacking in the introduction and discussion sections.

• Are the text and figures clear and accurate?

Text is very clear and well written, as are the figures.

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

Already mentioned before: FACS and WB are needed.

Reviewer #3 (Significance (Required)):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. This work aimed first at better understanding the fundamental transcriptional differences between two risk groups in Neuroblastoma. The authors defend the conceptual idea that these two groups represent two distinct diseases, which is not new in the area but requires attention, and indeed supported here by distinct transcriptional signatures.

Using published signatures of fetal sympatho-adrenal system, they define a core transcriptional program that is more strongly expressed in low-risk tumors, but we already know that tumors of this category are often more differentiated, and by definition expressed strong markers of SA differentiation, whereas high-risk tumors have a more undifferentiated phenotype.

Not surprisingly, several genes as well as a specific gene signature could be associated to better prognosis, a well-known characteristic of low-risk tumors. However, among them, a novel axis (NXPH1/a-NRXN) is proposed to explain the proliferation but absence of metastasis that define the low-risk group.

• Place the work in the context of the existing literature (provide references, where appropriate).

Neuroblastoma is a rare and very heterogeneous disease, in terms of biology and clinical presentation. To try to decipher such a heterogeneity, recent works have allied single cell transcriptome analyses on tumors and on human fetal cells during development. These studies are well cited in the discussion, and I agree that they yielded discrepant conclusions concerning the cell(s) of origin of Neuroblastoma. By comparing the normal developing human adrenal gland cells to cells from series of neuroblastomas, most of the studies converge towards that the tumors resembled differentiating adrenal neuroblasts. In one study, MYCN-amplified neuroblastoma cells (high risk group) were most similar to normal neuroblasts from seven- or eight-week post-conception, while lower-risk neuroblastomas included more cells resembling late neuroblasts (Janksy et al, 2021).

During the submission of this work, another paper using single cell technologies was published and supported the idea of two distinct tumor entities (Bedoya-reina et al, 2021), with also a stronger signature of sympatho-adrenal cells in low risk tumors.

• State what audience might be interested in and influenced by the reported findings. As the current clinical classification based on various criteria already allows clinicians to identify well low-risk tumors, I think this work would mainly attract fundamental researchers on the molecular differences between low-risk and high-risk tumors.

• 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'm specialized on pediatric cancers, and especially Neuroblastoma for the past 3 years. I'm interested in tumor cell identity and cell plasticity, particularly in response to treatment. I think that I have sufficient expertise to evaluate all parts of the manuscript.

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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.

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

1: The reviewers #1 and #3 suggested using a large dataset (the SEQC database containing 498 samples) to realize a more powerful comparative transcriptomic study. However, to define the transcriptional signatures associated to the aetiology of LR- and HR-NBs and to the malignant behavior of HR-NBs, we first needed to compare the transcriptomic signatures of LR-NB and HR-NB samples to the one of a non-tumoral, healthy tissue such as the fetal adrenal gland. The online SEQC does not contain any healthy samples, thus precluding the possibility to use it for the first step of our analysis. This is why we decided to use as a starting point the cohort of samples from HSJD cohort, which further provided the advantage of comparing samples from patients all diagnosed and treated at the same facility. In different steps of our analytic strategy (Fig.S1F, 2F-H, 3A-B, S3), we already used the SEQC database to test the relevance of the results in the context of a larger cohort. In doing so we obtained coherent results. As recommended by the reviewer #1 (comment #3), we will further compare our data with the data from another study (Bedoya-Reina et al, 2021). We thus believe that the request of the reviewers #1 and #3 does not need to be addressed within the scope of a revision.

2: The reviewer #2 suggested that some crucial functional experiments should be repeated with another shRNA construct to ensure that our results are not off-target and because the knock-down efficiency of the shRNAs used was variable and not convincing. We have tested two distinct shRNA constructs for both NXPH1 and α-NRXN1, which all comparably reduced cell viability. Following this reviewer’s suggestion we will assess possible off-target effects of the sh-NXPH1 and sh-aNRXN1 constructs by RT-qPCR. Moreover, we will also test the effects of these sh-NXPH1 and sh-aNRXN1 constructs in another cell line and using a novel and complementary metastasis assay (CAM assay).

3: The reviewer #2 suggested to study the metastatic potential of NB cells by performing orthotopic implantations of NB cells into the mouse adrenal gland instead of performing cell injections into the mouse left cardiac ventricle. We reasoned that cell injections into the left cardiac ventricle were ideal to test the organo-tropism of metastatic NBs, as this methodology facilitates cell dissemination and colonization of organs targeted by NB metastasis such as the liver and bone marrow, as shown in Fig.5B. Cell implantation into the adrenal gland is especially useful to study cell growth in one of the primary sites of NB formation. We thus believe that our current experimental approach is more relevant to the question we wish to address within the scope of a revision.

References:

Bedoya-Reina OC, Li W, Arceo M, Plescher M, Bullova P, Pui H, Kaucka M, Kharchenko P, Martinsson T, Holmberg J, et al (2021) Single-nuclei transcriptomes from human adrenal gland reveal distinct cellular identities of low and high-risk neuroblastoma tumors. Nat Commun 12: 1–15

Biedler JL, Helson L & Spengler BA (1973) Morphology and Growth, Tumorigenicity, and Cytogenetics of Human Neuroblastoma Cells in Continuous Culture. Cancer Res 33: 2643–2652

Ciccarone V, Spengler BA, Meyers MB, Biedler JL & Ross RA (1989) Phenotypic Diversification in Human Neuroblastoma Cells: Expression of Distinct Neural Crest Lineages. Cancer Res 49: 219–225

Decock A, Ongenaert M, Cannoodt R, Verniers K, Wilde B De, Laureys G, Van Roy N, Berbegall AP, Bienertova-Vasku J, Bown N, et al (2016) Methyl-CpG-binding domain sequencing reveals a prognostic methylation signature in neuroblastoma. Oncotarget 7: 1960–72

Gomez S, Castellano G, Mayol G, Sunol M, Queiros A, Bibikova M, Nazor KL, Loring JF, Lemos I, Rodriguez E, et al (2015) DNA methylation fingerprint of neuroblastoma reveals new biological and clinical insights. Epigenomics 7: 1137–1153

van Groningen T, Akogul N, Westerhout EM, Chan A, Hasselt NE, Zwijnenburg DA, Broekmans M, Stroeken P, Haneveld F, Hooijer GKJ, et al (2019) A NOTCH feed-forward loop drives reprogramming from adrenergic to mesenchymal state in neuroblastoma. Nat Commun 10: 1–11

Kildisiute G, Kholosy WM, Young MD, Roberts K, Elmentaite R, van Hooff SR, Pacyna CN, Khabirova E, Piapi A, Thevanesan C, et al (2021) Tumor to normal single-cell mRNA comparisons reveal a pan-neuroblastoma cancer cell. Sci Adv 7: eabd3311

Tumilowicz JJ, Nichols WW, Cholon JJ & Greene AE (1970) Definition of a continuous human cell line derived from neuroblastoma. Cancer Res 30: 2110–2118

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Referee #3

Evidence, reproducibility and clarity

Summary: short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

Dr. Le Dréau and colleagues provide a transcriptional analysis comparing low versus high-risk neuroblastomas using a cohort of 18 patients. By comparing them to normal transcriptional signatures obtained from human fetal adrenal glands, they conclude that low risk tumors share a specific core sympatho-adrenal developmental program, which is associated with favorable patient prognosis. Among this signature, they specifically assess the role of NXPH1/a-NRXN in vitro and in vivo using different models (cell lines, PDX-derived cell lines, mouse and chick xenografts). They propose that NXPH1/a-NRXN axis promotes neuroblastoma tumor growth via cell proliferation, and inhibits metastases.

Major comments:

• Are the key conclusions convincing? There are major points that need to be addressed before being convinced by the conclusions. • The choice for using the SKNSH cell line, among others, to study the role of NXPH1/a-NRXN axis need to be explained. Indeed, whereas there is no cell line modeling low-risk neuroblastoma, authors should properly illustrate the basal expression of NXPH1/a-NRXN in the cell lines and not the ratio provided in Fig3E. If I understood well, according to Fig3F, only 1.5% of SKNSH cells express NRXN1. Could the authors provide FACS plots? And explain how they can sort high and low expressing cells among 1.5%? And then how do they justify using shRNA approach in a cell line in which only 1.5% are concerned cells? Also, the authors should prove the efficiency of the shRNA used on each specific target for both in vitro and in vivo studies by WB. • The conclusion of inhibition of metastatic process is not supported by enough data. To achieve such a conclusion, authors should provide more than one in vivo experiment (which need to be completed already with the proof of protein deregulation). Some in vitro characterization of metastatic properties such as invasion and migration assays and/or transcriptional analyses could be done. • Why don't the authors use the transcriptome dataset of 498 patients to realize a more powerful comparative study of low versus high risk tumors (Zhang et al, Genome biology, 2015)? The authors should show the expression plot of NXPH1/a-NRXN in low versus high risk patients, in their cohort of 18 patients but also in the cohort of 498 patients. How do the authors reconciliate the idea that NXPH1/a-NRXN could be associated to stem cell identity but low risk tumors?
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Details of experiments and supplementary experiments have to be provided (see previous question).
• 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. Additional details of the experiments have to be provided (cf above): levels of expression of NXPH1/a-NRXN in cell lines, FACS analyses to prove enrichment and/or depletion, WB for validation of shRNA knock-down etc...

Moreover, the conclusion that NXPH1/a-NRXN axis inhibits metastatic potential of neuroblastoma is supported by only one in vivo experiment using SKNSH cell line with shRNAs anti-NXPH1/a-NRXN. It should be completed with invasion/migration assays in vitro for example, and/or transcriptional signature of tumors obtained +/- shRNAs anti-NXPH1/a-NRXN.

Ideally, these results could be validated in an additional model.

• 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
• Are the data and the methods presented in such a way that they can be reproduced? Yes, Material and methods section is well described. But, several points are missing:
• The paragraphs describing how RNAs from 18 patients and fetal adrenal glands were obtained, how good was the quality, and how transcriptomes have been realized and sequenced are missing.
• The sequences of shRNAs have to be provided.
• Are the experiments adequately replicated and statistical analysis adequate? Yes

Minor comments:

• Specific experimental issues that are easily addressable. The authors should show the basal expression of their genes of interest in the patients, cell lines and PDX-derived cell lines, to justify the choice to work then with SKNSH cell line. In addition to the ratio they show in Fig3.E.

Authors should also illustrate the FACS analyses they realized in this study, in order to appreciate the quantity of positive cells that are either enriched or depleted.

Authors could precise in their schemes that DOX is maintained in vivo. The number of mice need to be integrated in each experiment. - Are prior studies referenced appropriately? No some elements are not right in the introduction: - Mutations of PHOX2B are not associated to poor prognosis. - Original publications could be provided instead of reviews. - Genetic alterations in NB are not only 16%, the authors forgot to mention TERT and ATRX. - Maybe the NXPH1 methylation in ref 54 could be more explicit, if DNA methylation is detected on NXPH1, it would be of poor prognosis because driving low expression ..? - Are the text and figures clear and accurate? Text is very clear and well written, as are the figures. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions? Already mentioned before: FACS and WB are needed.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.. This work aimed first at better understanding the fundamental transcriptional differences between two risk groups in Neuroblastoma. The authors defend the conceptual idea that these two groups represent two distinct diseases, which is not new in the area but requires attention, and indeed supported here by distinct transcriptional signatures.

Using published signatures of fetal sympatho-adrenal system, they define a core transcriptional program that is more strongly expressed in low-risk tumors, but we already know that tumors of this category are often more differentiated, and by definition expressed strong markers of SA differentiation, whereas high-risk tumors have a more undifferentiated phenotype.

Not surprisingly, several genes as well as a specific gene signature could be associated to better prognosis, a well-known characteristic of low-risk tumors. However, among them, a novel axis (NXPH1/a-NRXN) is proposed to explain the proliferation but absence of metastasis that define the low-risk group.

• Place the work in the context of the existing literature (provide references, where appropriate). Neuroblastoma is a rare and very heterogeneous disease, in terms of biology and clinical presentation. To try to decipher such a heterogeneity, recent works have allied single cell transcriptome analyses on tumors and on human fetal cells during development. These studies are well cited in the discussion, and I agree that they yielded discrepant conclusions concerning the cell(s) of origin of Neuroblastoma. By comparing the normal developing human adrenal gland cells to cells from series of neuroblastomas, most of the studies converge towards that the tumors resembled differentiating adrenal neuroblasts. In one study, MYCN-amplified neuroblastoma cells (high risk group) were most similar to normal neuroblasts from seven- or eight-week post-conception, while lower-risk neuroblastomas included more cells resembling late neuroblasts (Janksy et al, 2021).

During the submission of this work, another paper using single cell technologies was published and supported the idea of two distinct tumor entities (Bedoya-reina et al, 2021), with also a stronger signature of sympatho-adrenal cells in low risk tumors.

• State what audience might be interested in and influenced by the reported findings. As the current clinical classification based on various criteria already allows clinicians to identify well low-risk tumors, I think this work would mainly attract fundamental researchers on the molecular differences between low-risk and high-risk tumors.
• 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'm specialized on pediatric cancers, and especially Neuroblastoma for the past 3 years. I'm interested in tumor cell identity and cell plasticity, particularly in response to treatment. I think that I have sufficient expertise to evaluate all parts of the manuscript.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2.

In this paper, Fanlo-Escudero et al., determines gene signatures differentiating low-risk (LR) neuroblastoma (NB) from high-risk neuroblastoma (HR-NB), as well as LR- and HR-NB as an entity from human fetal adrenal gland. They identify a transcriptional signature corresponding to a core sympathoadrenal lineage that can discriminate between LR-NB and HR-NB. This signature is composed of genes associated with favorable patient outcome. The authors further choose one gene, NXPH1, for functional analysis and investigates the effects this gene has on NB progression using in vitro assays, chick CAM assay and mouse in vivo models. The authors conclude that this transcriptional signature can distinguish LR-NB from HR-NB and that NXPH1 is involved in NB cell growth.

Major comments:

• Are the key conclusions convincing?

The key conclusions are 1) a core SA lineage signature can discriminate between LR-NB and HR-NB, and 2) NXPH1 represses NB malignancy (in terms of metastatic capacity) and is a therapeutic target. The first conclusion is indeed convincing, and not contradictive to common beliefs. The second conclusion is poorly supported by data. The authors perform a range of experiments using in vitro and in vivo settings, but lack some fundamental experiments and overstate their findings.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

Several claims should be softened, re-phrased and/or clearly marked as preliminary or speculative. No data nor claims need to be removed.

For example, the following statements need to be changed:

• Page 10, second paragraph: The authors state "Remarkably, NXPH1 and α-NRXN1/2 levels increased in all the NB cell lines harbouring a sphere-forming capacity (Fig. 3E), thereby revealing a strong positive correlation between the expression of NXPH1 and α-NRXN1/2 and the acquisition of a NCC stem cell identity". The authors only show that NXPH1 is expressed in 8 out of 10 NB cell lines. Sphere-forming capacity is displayed in a relative and not absolute scale which makes it difficult to assess which cell lines that do form spheres and to what extent. The capacity to form spheres (from low to high) does not correlate to the levels of NXPH1 in the different cell lines.
• Page 13, paragraph 1. The authors write "...these data revealed that NXPH1/α-NRXN1 signaling is necessary and sufficient for NB tumor growth in vivo". This is an overstatement. Tumors still form, meaning that NXPH1 signaling is not sufficient.
• Throughout the text, the authors convert their statements. One example is page 15, first paragraph. They write "...growth of NB cells but markedly restrict their metastatic potential", but they do not show this. Instead, they only address the opposite situation - Knockdown enhances metastasis. This is not equal to their statement. See other experiments in other sections. The authors need to go through the manuscript and make sure that they explain their conclusions to actually fit their experiments. • Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary to evaluate the paper as it is, and do not ask authors to open new lines of experimentation.

Issues to respond to:

• The authors should more clearly explain why they choose to further study NXPH1 (second highest on the list), involved in synaptogenesis and neurotransmission, instead of SOX6, highest on the list, that is highly relevant in neural crest development.
• When the authors investigate the expression of NXPH1 and other genes and compare that with sphere-forming capacity (Fig. 3E and page 10) they analyze expression in cells cultured in basal medium while sphere-forming capacity is measured after 5 weeks in restricted medium. How does the expression of the analyzed genes change under these conditions?
• Is the subpopulation of NRXN1+ cells low (1.5%) because these samples are from aggressive ("High-risk") cell lines?
• The authors state "...the number of cells quantified per tumor section was decreased by ~50% for the α-NRXN1+-deprived cells relative to their control (Fig. 3J, K), thus revealing that α-NRXN1+ cells are required to support NB tumor growth in vivo". This is not a correct conclusion. This experiment shows that a-NRXN1- cells do not grow and expand to the same extent as control cells. They cannot say that a-NRXN1+ cells support NB growth without comparing growth between a pure a-NRXN1+ and control cells.
• The authors use shRNAs to knock down NXPH1. They enrich their cells by two means - puromycin or doxocycline. This results in equal cell populations. The authors however state that they use doxocycline to circumvent the growth arrest they observe with puromycin selection. They need to elaborate on this and show why this would be the case and what difference the two methods do and show.
• The major flaw of this paper is that the authors use one cell line in total, and even more that they use the same cell line for both knockdown and activation. Since they do show that different NB cell lines have different expression levels (ranging from high to absent), they should choose one cell line for KD and one for overexpression. The authors could also do a rescue experiment with knockout and gain-of-function (e.g., construct that will not be targeted by the shRNA) in the same cells.
• They only use one shRNA after trying several (Fig. S4). The efficiency is substantially variable and not convincing. As stated also elsewhere in this review, they need to check protein level. And to ensure that their results are not off-target they should perform at least some crucial experiments with two shRNAs.
• Why don't the authors add BrdU post-implantation? This is easily done in the egg considering the accessibility and would better reflect the proliferation in vivo.
• Why do the authors switch between CAM and mouse xenografts? I understand that the mouse model must be employed for "metastasis", but can it be explained why and when they perform the different "tumor growth" experiments?
• Why do the authors do left ventricle injections for metastatic studies and not AG implantations?
• The measurement of bioluminescence is very difficult to interpret. The authors discuss metastatic spread, but the images show only large blobs covering the heart and areas surrounding it, especially for the sh-aNRXN1. To be able to say that the cells have colonized specific organs the authors need to dissect these organs and perform staining. I see it as tumors recur rather than particularly metastasize when they re-appear after 6 weeks.
• How do the authors explain results presented in Fig. S5: There are more HuNu+ cells but tumor size is unchanged? • Are the suggested experiments realistic for the authors? It would help if you could add an estimated cost and time investment for substantial experiments.

Some suggested experiments take time (orthotopic implantations, rescue experiments, adding cell lines and # of shRNAs).

However, as long as the authors discuss and address their methods for in vivo growth (in ovo vs in vivo vs their choice of metastasis model), an orthotopic AG model is not necessary. The authors should however consider it for future studies.

Experiments required to support their conclusions: A rescue experiment and use of different cell lines for KD and overexpression is somewhat time-consuming, as well as ensuring KD at protein level and include an additional shRNA in crucial experiment. I expect that this would take 2-4 months.

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

The authors should elaborate on their methods, but in general they are reproducible. • Are the experiments adequately replicated and statistical analysis adequate?

In several places the number of replicates is questionable. Especially at the end of page 26, the authors state that they have performed n=1-4 replicates. N=1 replicate is never ok. In several instances they do n=2 replicates. This can be acceptable but the authors could address this.

Minor comments:

• Specific experimental issues that are easily addressable.

Mainly text changes can be seen as minor. For experiments and other issues, see other sections. • Are prior studies referenced appropriately? Yes. The reference list is not coherently styled. • Are the text and figures clear and accurate?

Overall, the paper is written in a complex way and difficult to easily comprehend. For example, the authors need to clarify several issues on the material they use and experiments they perform. I suggest substantial re-writing to better convey their messages. Sentences should be short and clear, data explained in the context of it was derived.

The following text edits and clarifications are required: * Page 3. The authors write "cell-of-origin" in several places, this should be changed to "cells-of-origin" (i.e., plural). The view that all NBs originate from only one cell is too simplistic, and the authors should definitely edit this considering that they are investigating different subgroups of NB. * Page 5. The authors MUST define where the material from the 18 NB patients as well as fetal AG derive from. There is no reference, and taken from the material&methods section, the transcriptome data from these data has not been generated by the authors themselves? * Why do the authors choose to work with the data set from Jansky et al in particular? * Page 7, paragraph 1. The authors write "Remarkably, 67% of the 503 genes found in this signature, which formed the cluster c1, are both associated with a neural identity and a better patient outcome". I do not agree that this is remarkable and the authors should remove this word. * Page 10, second paragraph. The authors should clarify that the expression levels of the displayed genes are derived from qPCR analysis (if I have understood that correctly, I had to find and guess this from the M&M section), as well as explain how they have set the scale for sphere-forming capacity and what this corresponds to. What do the colors actually represent? * Page 11 and onwards. The authors write "deprived of their a-NRXN1+ subpopulation". This is highly confusing and difficult to read. The authors should write "a-NRXN1- subpopulation" * Page 11, end of paragraph 2. The authors write "...arguing that NXPH1/α-NRXN signaling could control NB growth and/or aggressiveness". Number of cells do not directly correlate to aggressiveness, and this needs to be re-phrased to only state what the experiment actually shows - proliferation of a-NRXN1- cells. * I am in favor of using the CAM assay as a complementary system. The authors however use this to define "...required to support tumor growth in vivo". The CAM assay using NB (i.e., transformed cells) shows the growth of these cells in response to presence of blood vessels and not a full tumor micro-environment. This should be clarified. * As stated in the previous comment, the authors write "...required to support tumor growth in vivo". The next paragraph has the following headline "NXPH1/α-NRXN signaling stimulates NB growth". This is to me the same thing. The authors should elaborate on how these differ, or if they use them to show the same thing, clearly state that. * The authors conclude that NXPH signaling can be used as a therapeutic target. This would however be extremely difficult considering the opposing effects shown on growth vs metastasis. I agree that it is important to find means to inhibit metastasis, but that does not mean we can allow for enhanced growth of the primary tumor. A better reflection would be to use this as a biomarker, but this can only be predictive/speculative since the authors do not perform for example a tissue microarray to show this at IHC protein level, something that is currently the practice in the clinic.

Material and Methods:

The authors have misspelled the cell line SK-N-BE(2)c. Why are some cell lines grown in 20% FBS? This is not standard and could impact the results. The authors should state what the tumor volume limit in their ethical permit is (page 30).

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? * Fig. 3E. As discussed elsewhere, the authors should clarify the scale/meaning for sphere-forming capacity * Fig. 4D. What do the numbers (i - vi) refer to? I cannot find this in the figure, figure legend, text or material&methods. * The authors do not present the tumor volume in Fig. 4. The authors discuss tumor growth in the text and this data should be included. * Fig. S4. Knockdown efficiency is variable, and efficiency does not correlate to growth capacity. Especially because of this, the authors need to investigate this at protein level.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This paper is partly within the scope of the ongoing debate of NB origin (see references below). This paper is however not as extensive, provides no new patient material (applies data from Jansky et al), and do not address the actual cell-of-origin (which the authors themselves also clearly states). This paper provides new gene signatures that can be used to define low-risk vs high-risk patients which is highly important to the field, but these signatures are not unexpected and does not add a significant advance to the field. The authors also do not address how these signatures could be applied clinically. The authors do not use any new methodology. With this said, with revision of the paper, it will still add to the current focus on NB biology research.

• Place the work in the context of the existing literature (provide references, where appropriate).

There is a recently initiated, important and extensive debate about the cells-of-origin for NB. The authors indeed bring this up in the paper and also state that they do not intend to add to this debate. They use data from one paper from referenced debate above, and I would argue that because of this fact, and that they extract gene signatures from it, they do, at least partly, touch on the NB cells-of-origin debate, and the authors should put their results into context, from a big picture perspective. As of now, they dodge this complex issue. References: Dong et al., Cancer Cell 2020; Hanemaaijer et al., PNAS 2021; Jansky et al., Nat Genet 2021; Kameneva et al., Nat Genet 2021; Kildisiute et al., Sci Adv 2021; Furlan et al., Science 2017)

• State what audience might be interested in and influenced by the reported findings.

This paper will be interesting for scientists within the neuroblastoma field, in particular those working on defining NB subgroups in correlation to developmental stages.

• 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.

Reviewer's expertise: Neuroblastoma, neural crest, trunk neural crest, chick embryos, mouse models, in vitro models

Parts of paper outside expertise of the reviewer: Analysis of the bioinformatics data (i.e., extracting signatures).

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the reviewed manuscript, the authors aimed to characterize the sympathoadrenal (SA) transcriptional landscape that defines low- and high-risk neuroblastomas (LR-NBs and HR-NBs respectively). In particular, they analyze previously published Affymetrix U219 expression profiles of 18 low- (n=8) and high-risk (n=10) neuroblastomas, and 2 fetal human adrenal glands. The authors define transcriptional signatures of LR- and HR-NBs, and further unbiasedly classified them in 4 clusters defining groups of patients with different prognosis (as tested using the 498 SEQC cohort). Within these transcriptional signatures, the authors delineated a SA signature using a human fetal adrenal gland transcriptional profile recently published (Kildisiute et al. 2021), that can discriminate low-risk neuroblastomas. From these genes, the authors further select NXPH1 and NRNX1-2 as promising targets for extensive experimental in vitro and in vivo validation, including validation in cell cultures, and xenografts, to determine that NXPH1/alpha-NRXN1-2 signaling is sufficient for NB tumor growth, and that the expression of either stimulates the metastatic potential of NB cells.

Major comments:

The cohorts and data used by the authors to conduct the main analysis of the paper are already published, and thus the contribution of the analysis is incremental. In particular, the authors analyzed arrays from a limited cohort size, in comparison with others available sequenced with RNA-seq (e.g. 176 HR- and 322 non-HR NB in 498 SEQC; 224 HR- and 342 non-HR NBs included in the Westermann-genecode19 cohort; and 80 HR- and 20 non-HR in the Jagannathan cohort). Furthermore, the 12,000 most-expressed genes (out of ~20,000 available) were analyzed by the authors, as opposed to more than 40,000 (coding and non-coding) included in a normal RNA-seq study. Only the 498 SEQC dataset provides 12,000 genes significantly up-regulated in either high-risk (n~5,500) or non-high-risk (n~7,000). The differences between datasets could influence the results of the study. For example, in the reviewed manuscript, genes with a high expression in LR-NB (compared to fAG) included DNMT3B, SEMA5A, SOX5, and TET1, all of which have a significantly higher expression in HR-NBs of the 498 SEQC cohort. The quality of the manuscript will be enhanced with consistent results obtained by conducting the same reported analysis in larger cohorts.

In the reviewed manuscript, PHOX2A and PHOX2B are significantly more expressed in both LR-NB and HR-NB compared to fAG. This is also the case for other adrenergic markers including TH and DBH. Oppositely, the expression of cortex markers (i.e. STAR and CYP11A1) is significantly higher in fAG. Nevertheless PNMT is not significantly up-regulated in fAG in comparison to LR-NB nor HR-NB. Is it possible that the fetal adrenal glands analyzed include a large proportion of cortex that confounds the transcriptional signals? The quality of the manuscript will be enhance if the authors could establish what proportion of the fAG transcriptional signal belongs to cortex, and if they account for its influence in the analysis.

A recent published paper (Bedoya-Reina et al. 2021) study the differences of HR-NB and LR-NB from a single-cell perspective. In the published manuscript, the authors conclude that LR-NBs are enriched in cells that resemble chromaffin and sympathoblast cells, while the high-risk neuroblastomas are enriched in undifferentiated cells that resemble cells with progenitor characteristics in post-natal adrenal gland. This is broadly consistent with the conclusion reached by the authors in the manuscript under review. It will enhance the content of the reviewed manuscript if the authors compare their transcriptional signatures with the recently published transcriptional signatures in this paper to answer the following questions: 1) to what extent the transcriptional signatures for HR-NBs (4 hierarchical clusters incl.) in the manuscript under review resembles that from the published undifferentiated cluster (nC3) enriched in HR-NBs, and the progenitor cluster (hC1) in post-natal adrenal gland; 2) to what extent the transcriptional signatures for LR-NBs (4 hierarchical clusters incl.) in the manuscript under review resembles that from the published NOR (nC7, nC8, and nC9) enriched in LR-NBs, and that from the chromaffin cells (hC4) enriched in post-natal adrenal gland; and 3) how is the expression of NXPH1 and alpha-NRXN1-2 in the reported LR- and HR-NBs, and adrenal gland.

In the discussion, the authors indicate that they do not aim to identify the transcriptional signature associated to NB origin but rather use the component of the SA lineage that distinguish LR- and HR-NBs. This statement implies that neuroblastoma can originate from any cell in the developing SA lineage (i.e. SCP, bridge, chromaffin and sympathoblast), a controversial assumption that requires further proof. In particular, when discussing about the core sympathoadrenal signatures enriched in LR-NBs and HR-NBs, the authors obtained a SA signature of genes shared by at least 3 of the 4 SA cell signatures. Further justification needs to be provided as for why (in particular) one of these SA cell signatures exclude the sympathoblast/neuroblast contribution.

Some of the most interesting results in the paper are limited to proportions in a subset of top-ranked genes. It will be valuable to set the analysis in an hypothesis driven context, add probabilities, test names, and corrected p-values to the results.

Minor comments.

1) In comparison with other cohorts that include low- and intermediate-risk NBs as non-HR NBs, the reviewed data specifically includes low- and high- risk NBs. It is important that the authors include a characterization of intermediate-risk neuroblastomas in their analysis.

3) Further details and figures on what precise criteria was used to remove the sample #LR-08 is required. How including this sample changes the reported results?

4) GO-term distribution was assessed using the 50 most-enriched GO-terms. How would the results change if all the significant GO terms were analyzed?

5) Was the SEQC 498 (GSE62564) dataset obtained with microarrays (as indicated in the methods) or with RNA-seq (i.e. Illumina HiSeq 2000)?

6) In methods, the first quartile (Q1) in SA-c1 has a higher limit in 487 samples and the fourth quartile the lowest limit in 4, how many samples (out of 498 NBs) were excluded and why?

7) In the 503 DEGs between LR-HR NBs, NTRK2 and MYCN are not included, even if the HR samples included MYCN amplified tumors. Can the authors comment on this?

8) The authors mention that the top 30 genes found in cluster c1 (and also in c2) are correlated with favorable patient prognosis. Is it the case that all the genes in c1 (and also c2, c3 and c4) are significantly associated with a favorable or else unfavorable prognosis?

9) The high expression of a (significant?) number of genes in cluster c4 is observed in patients with worst outcome (i.e. lower event-free survival), including ATR, HIF1A, ING2, POLR2L, SRPRB (498 SEQC, analyzed with R2).

10) Regarding the 242 genes in the core SA signature, although its a smaller number, the expression of several genes in the core SA signature with a higher expression in HR compared to LR belonging to clusters 2, 3, and 4 is observed in worst outcome patients in the 498 SEQC cohort (CHD7, DNMT1, HMGA1, HSD17B12, LBR, LSM7, MCM4, NKAP, POLA1, and others). Is this small fraction significant?

11) In Kildisiute et al. 2021, NRXN1 is expressed in SCPs, while NXPH1 is expressed in bridge, chromaffin and sympathoblastic cells. How are the microenviroment of these cells regulating the expression of these genes in a developmental context (particularly as sympathoblastic cells are know to have larger proliferative capabilities than SCPs)? how is this cell heterogeneity replicated by a NB cell line? are mesenchymal and adrenergic cells expressing differentially NRXN1 and NXPH1?

12) Figure 1B and C, 2B,D: might the information provided be enhanced? otherwise these inserts might be excluded.

13) Figure 3D: Kildisiute et al. 2021 data and GTEX available at human protein atlas indicate expression of NRXN1 and NXPH1 in developing and adult adrenal gland. Might the results illustrated suggest a confounding effect in the sampled fetal adrenal glands, perhaps from cortex?

14) The authors conduct extensive experiments in NRXN1, and make conclusions about its role in for instance metastasis, nevertheless the LR-NB/HR-NB SA signal only includes NRXN2. Can the authors comment on the differences between NRXN1s and NRXN2?

Significance

The significance of the study relies in investigating the role of selected targets in neuroblastomas within a risk group. In particular, HR-NBs have poor outcomes and are generally metastatic at the time of diagnosis.

The results of the manuscript are somehow consistent with a recently published manuscript analyzing LR- and HR-NBs from a single-cell perspective. The manuscript will be enhanced by conducting the suggested comparison between the reviewed and the reported results. The authors further need to comment why HR-NBs markers, particularly MYCN is not recovered in the LR-NB/HR-NB and the LR-NB/HR-NB SA signals. Also they need to comment on possible confounding effects in the fetal adrenal gland.

The paper is directed to a broader audience of cancer and developmental biologists, and computational biologist. Yet further statistical support needs to be provided.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, Dennis et al. identify different secretory routes and cell exit sites involved in basement membrane secretion and diversification in epithelial cells. Using the follicular epithelium of the Drosophila ovary as their model system coupled with genetics, imaging, and image analysis approaches, they show that two previously identified RabGTPases, Rab8 and Rab10, work in parallel routes for basement membrane secretion. These two small GTPases work in a partially redundant manner, where Rab8 promotes basal secretion leading to a homogenous basement membrane, while Rab10 promotes lateral and planer-polarized secretion, leading to the formation of fibrils. The authors also show that Rab10 and the dystrophin-associated protein act together to regulate lateral secretion, and dystrophin (Dys) is necessary for dystroglycan (Dg) to recruit Rab10. Furthermore, DAPC is shown to be essential for fibril formation and is sufficient to reorient Collagen IV to the Rab10-dependent secretory route. Dys was also shown to interact directly with exocyst subunit Exo70. Using overexpression and loss of function approaches the authors claim that Exo70 limits the planer polarization of Dys, and as a result, Rab10, hence limiting basement membrane fibril formation. Finally, the authors state that the Exocyst (Exo70) is also required for the Rab8-dependent basement membrane route. Overall, the data described in this manuscript are convincing and the authors' claims are supported by the presented data. We have mainly minor comments and only a few major comments that need to be addressed.

Major Comments:

• In the text for Figure 1G-H (page 4), the authors stated that the basal secretion was not restored in Rab8, 10, and 11 triple KD, in our opinion, it is unclear how the authors came to this strong conclusion from the presented data. It would be good if the authors explicitly explain how they come to this conclusion. Is it only based on the weak Coll-IV-GFP signal in the Rab8, 10, and 11 triple KD data compare to the control? If so, the authors should statistically quantify the difference with the control. In Figure 1H, no statistical analysis is provided between the control and triple KD conditions.

• From the data presented in Figure S1B, the authors state that the basement membrane mislocalization observed in Rab8/10KD has no major impact on polarity maintenance. They based this statement only on the localization of the apical marker aPKC. Although the aPKC data are convincing, it would be more compelling if the authors observe the distribution of other polarity proteins such as Dlg, E-Cadherin, and armadillo to better assess if the overall epithelial polarity is maintained in this condition.

Minor Comments:

General comments:

• In the text describing their data, we recommend that the authors clearly indicate which panel(s) they are referring to.

• The authors should also be consistent with the diction throughout the manuscript when referring to the cortical domain or region of the cell (back/rear/trailing edge/leading edge).

• Several references are missing in the manuscript.

The following specific comments are in order of appearance in the manuscript.

Introduction Section:

The following statements in the introduction should be supported by specific references:

• "BM is critical for tissue development, homeostasis and regeneration, as exemplified in humans by its implication in many congenital and chronic disorders."

• "BM is assembled from core components conserved throughout evolution: type IV collagen (Col IV), the heparan sulfate proteoglycan perlecan, and the glycoproteins laminin and nidogen."

• "During development, the dynamic interplay between cells and BM participates in sculpting organs and maintaining their shape."

• "BM protein secretion shows some specificities, mainly because of the large size of the protein complexes (e.g., procollagen) that must transit from the endoplasmic reticulum to the cell surface". This statement could be supported with references including specific Drosophila references. Additionally, the authors need to clarify what they mean by "some specifies".

Results section:

• In the text describing Fig. 2 (page 5), the authors describe two different basement membrane types: fibrils and homogenous. Moreover, the manuscript focuses on the role of Rab8 and Rab10 in the formation of these two structures. Thus, the authors must better describe the two different types of basement membrane structures and their known roles. This will be helpful for the readers to analyze the presented data, especially for those that are not familiar with the system. In Figure 2A, the authors describe stage 3 basement membrane as uniform BM, do they mean homogenous?

• In the text describing the data for Fig. 3 (page 6), the authors should clearly explain the reason to use anti-GFP antibodies in a non-permeabilized condition (i.e., to detect specifically the extracellular secretion of BM proteins). This will help the readers to interpret the data presented.

• On page 9, the authors stated that the precise localization of Dg in follicle cells is unknown. This statement is incorrect. It has been shown, using a Dg antibody, that Dg localizes at a high level at the basal side of the follicle cells and at a lower level at the apical side (Deng et al, 2003 and Denef et al. 2008).

Discussion Section:

• The following statement is not clear: "Thus, three different Rab proteins are targeted towards the three distinct domains of epithelial cells defined by apical basal polarity, and at least of them is also planar polarized". The authors should rephrase and describe specifically which Rabs they are talking about.

• This statement is vague: "These three Rab GTPases have been jointly involved in different processes (Knödler et al, 2010; Sato et al, 2014; Vogel et al, 2015; Eguchi et al, 2018; Häsler et al, 2020)". The authors could also mention the processes in which Rab8, 10, and 11 are involved.

• The following statements need to be supported by references. "Therefore, more investigations are required to define exactly how the DAPC allows the formation of BM fibrils. Nonetheless, given the importance of the DAPC and BM proteins in muscular dystrophies, our results will pave the way to determine whether a similar function is present also in muscle cells. Interestingly, the extracellular matrix is different between the myotendinous junction and the interjunctional sarcolemmal basement membrane and may provide another developmental context where several routes targeted to different subcellular domains may be implicated".

Experimental Procedure Section:

• In the dissection and immunostaining section (p14), there is a typo: it should be for "20 min" instead of "2for 0 min"

• For the GST pulldown experiments, the authors mention that they use a standard protocol to produce S35 Exo 70 and the GST pulldown experiments. The authors should provide references.

Figure and Figure Legend: • General comment: The orientation of the images showing the rotation and leading and trailing edges need to be consistent in the different figures (e.g., In Figures 3 and 7, the leading edge is oriented to the top while in Figures 4, S4, 5, 6, the leading edge is oriented to the bottom). This will help the readers to analyze the data.

• In Figure 1 C-G the scale bars are missing and should be added as Fig. 1B.

• Figure S1A: The data presented in Figure S1A is convincing. However, a control panel should be added showing the absence of apical Coll IV for comparison. This information will help with the interpretation of the data.

• In Figure 3 legend: it should be "immunostained" for GFP instead of stain for f-actin and GFP.

• In Figure 4, some scale bars are missing.

• In Figure 4 legend: it should be "(A, E)" after (i.e 0.8 µm above the basal surface) instead of "(C, G)"

• In Figure 5A-E, the authors show quantification of the fibril fraction for Dys-, Rab10 OE, and Rab10OE+Dys, Rab8KD, and Rab8KD+Dys-, and images of the collagen fibril for all the conditions except Dys-, it will be informative that the authors present a representative image of the Coll IV fibril in Dys- condition for comparison. The above comment also applies to Figure 5F-J, and it will be also informative to have a representative image of Dys- condition.

• In Figure 5 legend (p23), it should be "plane" and not "plan".

• Overall, the legend for Fig. S5 is not clear and we recommend the authors to clearly described the different panels. (e.g., it should be "(D)" instead of "(H-J)")

• In Figure 6, some scale bars are missing.

Significance

Despite the important roles of the basement membrane for mechanical support, tissue and organ development, and function, the mechanisms that control the polarized deposition of basement membrane proteins are largely unknown. The contribution of Rab 8 and Rab 10 in the polarized deposition of the basement membrane was previously shown. However, by identifying two competitive secretory routes for the basal secretion of the basement membrane proteins that required these two different RabGTPases, controlled by the DAPC and the exocyst complexes, the authors make a novel contribution to our understanding of the mechanism that leads to the polarized secretion of basement membrane proteins (in that case Collagen IV). Since the basement membrane has critical roles in tissue and organ morphogenesis and functions, and its misregulation has been associated with developmental defects and pathological conditions, this research sheds light on the mechanisms important in these morphogenetic processes and will give insights into their deregulations in pathological conditions.

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Reply to the reviewers

A detailed point wise response has been uploaded along with revised manuscript files

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Reply to the reviewers

Manuscript number: RC-2023-02157

Corresponding author(s): Satish, Mishra

1. General Statements [optional]

We thank the editor and reviewers for their helpful comments. We have successfully addressed most of the comments. We are performing some additional experiments as suggested by the reviewers and will be included if considered further. We attempted to pulldown the S14 interacting partner using anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. So, accordingly, we have toned down the conclusion.

The point-by-point response to the reviewer’s comments is given as follows.

2. Description of the planned revisions

Reviewer #1:

Figure 1F You have not formally shown that this signal corresponds to palmitoylated S14. Could be heavy chain. Response: The possibility of a heavy chain is negligible because we have used sporozoite samples and probed it with an anti-rabbit antibody conjugated to HRP. Also, the size of the S14 bands does not correspond to heavy chain. However, we have toned down the conclusion. Currently, we are performing the depalmitoylation experiment, and data will be included in the next round of revision.

Reviewer #2

Line 149: To definitively state S14 is a membrane protein, biochemical assays proving such should be performed. (or perhaps genetic mutation of the predicted palmitoylation site?) Otherwise, this should be rephrased. Response: We are performing the depalmitoylation assay, and the data will be included during the second round of revision. However, we have rephrased the sentence in the current version of the manuscript.

Lines 257-258: for yeast 2-hybrid, the controls of expressing S14, GAP45 and MTIP together with control proteins where no interaction would be predicted are absent. Response: We are performing experiments with additional controls, and data will be included in the next round of revision.

Reviewer #3

Conclusions that S14 knockout does not impact the expression and organization of two surface proteins, CSP and TRAP, and two IMC rely on a qualitative analysis only. However, quantitative analysis to support their observations is missing. Response: We are quantifying the IFA images and data will be included in the next round of revision.

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

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

Summary: The authors have identified a sporozoite gliding motility protein through bioinformatic analysis. From the main text I do not know how, or what bioinformatic analysis was performed, in order to focus on this protein which is called S14. The authors then go on to tag the protein, produce a KO and show its involvement in gliding motility. The KO shows that parasites lacking S14 fail to invade the mosquito salivary glands. This is due to a motility defect. Y2H and docking studies are used to define an interaction with MTIP and GAP45, two known components of the glideosome. Response: We identified this gene from the Kaiser et al., 2004 paper (DOI: 10.1046/j.1365-2958.2003.03909.x). The S14 was found to be highly upregulated in salivary gland sporozoites but lacked signal sequence and transmembrane domain. Next, we looked into other sporozoite proteins lacking signal sequence and transmembrane domain and found several gliding-associated proteins with similar properties. By using the guilt-by-association principle (DOI: 10.1186/gb-2009-10-4-104), we studied the following properties of existing glideosome components along with S14: (1) Classical pathway secretion using the signal peptide (SignalP, https://services.healthtech.dtu.dk/services/SignalP-5.0) (http://dx.doi.org/10.1016/j.jmb.2004.05.028). (2) Nonclassical pathway secretion (SecretomeP , https://services.healthtech.dtu.dk/services/SecretomeP-1.0/) (10.1093/protein/gzh037). (3) Presence of transmembrane domains (TMHMM , https://services.healthtech.dtu.dk/services/TMHMM-2.0/) (10.1006/jmbi.2000.4315). (4) Presence of a potential palmitoylation site (CSS-Palm, http://bioinformatics.lcd-ustc.org/css_palm) (Ren et al, 2008). This is a similar association prediction method as employed by the STRING database. However, mentioning that we identified a gliding motility protein by bioinformatic analysis was wrong, and we modified the sentence.

Major comments: The paper is sometimes hard to follow and lacks clarity. The reason: important information is omitted, or explained at the end of a section rather than at first mention; experimental details that are of essence need to be mentioned or explained in the main text; there is ample use of the word 'bioinformatic' without explaining what kind of analysis was performed in the main text. I cite from the abstract: 'In silico analysis of a novel protein, S14, which is uniquely upregulated in salivary gland sporozoites, suggested its association with glideosome-associated proteins.' I cite from the introduction: 'A study comparing transcriptome differences between sporozoites and merozoites using suppressive subtraction hybridization found several genes highly upregulated in sporozoites and named them 'S' genes (Kaiser et al, 2004). We narrowed it down to a candidate named S14, which lacked signal peptide and transmembrane domains.' From reading the main text, I do not know why Plasmodium berghei S14 was chosen in this manuscript. S14 is one of 25 transcripts identified by Kappe et al in Plasmodium yoelii (https://doi.org/10.1046/j.1365-2958.2003.03909.x) to be upregulated in sporozoites. The material and methods section does not explain either why S14 was chosen. Perhaps the authors could update Figure 2 from Kappe et al with the most recent annotations from plasmodb. Response: We have edited the manuscript for clarity and mentioned the name of the bioinformatic analysis performed. We chose S14 from Kaiser et al., 2004 (https://doi.org/10.1046/j.1365-2958.2003.03909.x) that identified transcripts in P. yoelii. We work on the rodent malaria parasite P .berghei and validated S14 transcripts by qPCR which showed its upregulation in sporozoites.

Rodent malaria parasites P. berghei and P. yoelii have been used extensively as models of human malaria. Both species have been widely used in studies on the biology of Plasmodium sporozoites and liver stages due to the availability of efficient reverse genetics technologies, and the ability to analyze these parasites throughout the life cycle stages have made these two species the preferred models for the analysis of Plasmodium gene function. A genetic screen and phenotype analysis were performed in P. berghei (DOI: 10.1016/j.cell.2017.06.030 and DOI: 10.1016/j.cell.2019.10.030) that makes in-depth characterization easier due to the availability of reagents and preliminary gene-phenotype like its dispensability in the blood. As suggested by this reviewer, we have updated the most recent annotations from PlasmoDB.

Reproducibility: None of the main Figures or Figure legends define ' N = '. For example I cite: 'The S14 KO clonal lines were first analyzed for asexual blood-stage propagation, and for this, 200 µl of iRBCs with 0.2% parasitemia was intravenously injected into a group of mice.' There are 2 mentions of 'N=' in the supplementary figures. I have not found any others.

I'm not sure what the convention is. Should unpublished data for this gene (PBANKA_0605900) found in pberghei.eu (a database for mutant berghei parasites) be cited? After all it confirms their findings.

The authors need to use more recent references for some of their statements; see some comments below. __Response: __We have mentioned N in the figures legends of the revised manuscript and also mentioned the unpublished data of RMGM. We have also added recent references in the revised manuscript.

Minor comments:

line 1-2 Add the Plasmodium species of this study.

Response: Added.

abstract Which species do you work with?

Response: We have mentioned P. berghei in the abstract of the revised manuscript.

29 mosquito salivary glands and human host hepatocytes

Response: Corrected.

30 to the glideosome, a protein complex containing [...]

Response: Corrected.

32-33 What kind of in silico analysis suggested S14 is part of the glideosome? S14 is not uniquely upregulated; there are other S-type genes identified by Kappe and Matuschewski. 25 I believe.

Response: Mentioning that in silico analysis suggested S14 is part of the glideosome was a wrong statement, and we have modified the sentence for clarity in the revised manuscript.

32 Please point out he species were S genes were identified. SGS of which species?

Response: The S genes were identified in the transcriptomic study of Plasmodium yoelii.

34 expression: change to transcription

Response: Changed.

39 What kind of in silico analysis was used here? and therefore malaria transmission

__Response: __In silico, protein-protein docking interaction analysis was used.

55 A single zygote transforms into a single ookinete, which establishes a single oocyst, which in turn can produce thousands of midgut sporozoites. Please correct the life cycle passage.

Response: Corrected. located or anchored in the IMC? And located between the IMC and plasma membrane?

Response: Glideosome is located between the plasma membrane and IMC, and the same has been corrected in the revised manuscript.

61-63 Refer to Table S1 and its contents here 64 Name the known GAPs. Response: Done.

65-67 Which transmembrane domain proteins? Please add more recent references than King 1988.

Response: We have added TRAP as a transmembrane domain protein and updated the reference.

71-72 TRAP was the first protein found to be ...

Response: Corrected.

74-76 Add additional, more recent references: for example search Frischknecht and TRAP

Response: Added.

76 S6 (TREP) is also [...]

Response: Done.

88 Some of these proteins are also expressed in ookinetes.

Response: Corrected.

89-91 The sentence needs a verb.

Response: Added.

88-96 Please add some more recent glideosome papers. After 2013.

Response: Added.

91 Why do you call it a peripheral protein?

Response: Because the GAP45 was detected at the periphery of the merozoite in P. falciparum. As there are no such reports in sporozoites hence we have removed peripheral in the revised manuscript.

91-93 There are more recent citations for GAP45 and GAP50. Response: We have added recent citations.

96 Insert a reference here.

Response: Added.

99 Please define the gliding-associated proteins. What are they? Aren't there papers on GAP40, 45 and 50? DOI: 10.1016/j.chom.2010.09.002

Response: Done.

99 .... What prompted you to identify a novel GAP? And why is S14 classified as a GAP?

Response: This was a wrong statement, which we removed in the revised manuscript.

99-102 What kind of bioinformatic study? Why was S14 chosen? Please outline how you ended up with S14. Any other proteins that came out of the bioinformatic screen from the list of S genes?

Response: We identified S14 from the Kaiser et al., 2004 paper and analyzed its properties using the “guilt-by-association” principle. The analysis showed that S14 had properties similar to GAP45 and MTIP. The S14 upregulation in sporozoites and its properties similar to known GAPs, we were prompted to study this gene's function.

How many proteins were identified in the screen for sporozoite upregulated proteins by Kappe and Matuschewski?

Response: 25 genes were identified in that paper, including the two characterized genes CSP and TRAP during that study.

102-103 Define the nonclassical secretion pathway. Please reference GAP45 and GAP50 data for the nonclassical pathway.

Response: When proteins are secreted out of the cytosol without predictable or known signal sequences or secretory motifs are classified as non-classically secreted proteins, and the pathway is called a non-classical protein secretory pathway. References: https://doi.org/10.1371/journal.pone.0125191; https://doi.org/10.1016/S0171-9335(99)80097-1; doi: 10.3389/fmicb.2016.00194

105 Please add P. berghei to the title, the abstract, the introduction.

Response: Added.

111 The results section does not outline what bioinformatic analysis was used

Response: The guilt-by-association principle was used, and it is outlined in the revised manuscript.

112-114 Please specify the exact number of upregulated in sporozoites genes. I think it was 25. And add the species the study was performed in. Why did you choose the Kappe study but not the uis genes from berghei?

Response: It was 25, and the species was P. yoellli. The domains of all 25 proteins are shown in Figure 2 of Kappe study. It intrigued us after having a glance at it. Later, we confirmed the upregulation of S14 transcripts in P. berghei sporozoites and chose to study the function of this gene.

114-115 How did you narrow it down to S14? The Kappe paper lists 25 S-type genes from P. yoelii.

Response: The domains of all 25 proteins are shown in the Kappe study. Two proteins, S14 and S15, lack signal sequence and transmembrane domain, which intrigued us after glancing at them. We chose S14 because its microarray induction is higher compared to S15.

118 Plasmodia is not the plural for a group of different Plasmodium species. Use: [...] conserved among Plasmodium spp.

Response: Corrected.

118-119 Which proteins did you analyze? And how did you analyze them? Where is the data for this analysis? Outline the amino acids that predict palmitoylation? The nonclassical pathway?

Response: The proteins we analyzed are given in Table S1. We analyzed them by the guilt-by-association principle. The data for this analysis is shown in Table S1. The amino acids predicted to be palmitoylated are C59 and C228 (S14), C5 (GAP45), C8 and C5 (MTIP). Non-classical pathway secretion was predicted by SecretomeP ( 10.1093/protein/gzh037).

119-122 Here: do you mean S14 has similar properties as GAP 45 and GAP50? Define the nonclassical pathway? How do you know S14 is in the IMC?

Response: The similar properties of S14 and GAP45 are Signal Peptide Prediction, Prediction of Non-classical pathway secretion, number of predicted transmembrane domains and prediction of Palmitoylation signal. GAP50 was wrongly mentioned here and has been removed from the revised manuscript.

When proteins are secreted out of the cytosol without predictable or known signal sequences or secretory motifs are classified as non-classically secreted proteins. The pathway is called a non-classical protein secretory pathway.

Our colocalization data of S14 with GAP45 and MTIP indicated that S14 is in the IMC.

122-123 Please reference the bioinformatic analysis plus URL that allows targeting to the IMC to be analyzed.

Response: All the URLs with references are given in the method section, lines 348-358 in the revised manuscript.

123-124 Please reference the URLs for TM, palmitoylation, and interactions analyses.

Response: All URLs with references are given in the method section, lines 348-358 in the revised manuscript.

125-127 How did you predict that S14 is secreted via the nonclassical pathway?

Response: We predicted non-classical pathway secretion of S14 using - SecretomeP (https://services.healthtech.dtu.dk/services/SecretomeP-1.0/) (10.1093/protein/gzh037).

128-130 Define the nonclassical pathway when it first appears in your manuscript.

The citation Moskes 2004 is not in the reference list

Response: The nonclassical pathway is defined in lines 105-107. The citation Moskes 2004 has been included in the revised manuscript.

132 Which membrane?

Response: Live S14-mCherry localization on the membrane does not differentiate between the outer membrane or IMC. Hence, only membrane is mentioned. Next, in Figure 4A, we confirmed S14 localization on IMC by treating sporozoites with Triton X-100 and colocalizing with IMC proteins GAP45 and MTIP.

134-135 In which species?

Response: We have mentioned P. berghei in the text in the revised manuscript.

141-142 Please include images of blood stage and liver stage parasites.

Response: Blood and liver stage images are included in the revised manuscript as Figure S2.

142-143 Which membrane?

Response: Live S14-mCherry localization on the membrane does not differentiate between the outer membrane or IMC. Hence, only membrane is mentioned. Next, in Figure 4A, we confirmed S14 localization on IMC by treating sporozoites with Triton X-100 and colocalizing with IMC proteins GAP45 and MTIP.

148-149 I cannot find the specific figure you refer to; I checked the online version of the Frenal 2010 paper.

Response: Electromobility shifts of GAP45 due to the palmitoylation have been reported in (Rees-Channer et al, 2006; DOI: 10.1016/j.molbiopara.2006.04.008). Frenal 2010 paper has stated about two bands but experimentally, it was shown in Rees-Channer et al, 2006 in Figures 1 and 2B.

175 gland, we counted [...]

Response: Corrected.

177 Compared to the

Response: Corrected.

177-179 Failed to invade (absolutely)? Or invaded in highly reduced numbers?

Response: Corrected.

182-186 Please be precise: I think you mean you let all types of mosquitoes take a blood meal; s14 knockout-infected mosquitoes did not infect mice.

Response: Corrected.

181-202 Perhaps use paragraphs to indicate the different types of experiments performed here.

Response: Done.

204 Please introduce paragraphs to identify the different experiments in this section

Response: Done.

208 Outer or inner membrane of what? IMC, the plasma membrane?

Response: We treated sporozoites with Triton X-100 to analyze whether S14 is present on the outer membrane (plasma membrane) or IMC.

228 onwards Structural models were obtained from whom? Which species did you use for the docking study? Could you use in one approach 3 berghei proteins, and confirm your docking studies with the falciparum proteins? That would strengthen your model. Should you include a negative control protein in the approach? Response: The structural models were obtained using the trROSETTA server. We used P. berghei for the docking study. In the old annotation and RMGM, the ortholog of P. berghei (PBANKA_0605900) in P.falciparum (PF3D7_1207400) was indicated. However, the updated PlasmodDB does not show PBANKA_0605900 ortholog in P. falciparum. We did try to generate structure models of P. falciparum MTIP, GAP45 and S14 using the trROSETTA server. We successfully reproduced the structure of MTIP, and GAP45 but the quality of S14 structure was unsuitable for the interaction studies. The negative control cannot be included in this kind of study because it gives a false interface, and none of the previous studies have used negative control.

250-251 Was all of the gene cloned? Please define amino acid range. discussion

Response: Full-length gene of S14, MTIP and GAP45 was cloned and the same has been mentioned in materials and methods in the revised manuscript.

Please discuss data from https://elifesciences.org/articles/77447 in relation to your protein Response: Discussed.

298-300 More recent glideosome papers exist. For example https://doi.org/10.1038/s42003-020-01283-8

Response: Included.

340 List the proteins you analysed. Add URL (websites) to the analyses tools.

Response: They are listed in Table S1. The method section gives all the URLs with references, lines 348-358 in the revised manuscript.

343 Known association from the literature: how was this done?

Response: The interactions demonstrated by different groups have been summarized in the review by Boucher & Bosch, 2015 (doi: 10.1016/j.jsb.2015.02.008).

346-349 A few glideosome components? On what basis were they selected and which are they? Response: The analysis showed that S14 had properties similar to GAP45 and MTIP. Additionally, S14 localized with GAP45 and MTIP, hence selected for interaction studies.

471 Can AlphaFold Structure Predictions be used in the docking studies?

Response: Even the Alphafold AI is trained on existing sequence/structure information despite being advertised as a de novo prediction system. That's why it can't produce good quality structures of evolutionarily unique proteins such as S14. We initially started our protein model generation by alphafold2, but the quality of the structure was very low; then we further used the trRosetta server (https://yanglab.nankai.edu.cn/trRosetta/), which shows the quality of all three protein structures above 95 after validation by using UCLA-DOE LAB-SAVES V6.0 (https://saves.mbi.ucla.edu/).

tr-Rosetta includes inter-residue distance, orientation distribution by a deep-neural network, and homologous template to improve the accuracy of models (DOI: 10.1038/s41596-021-00628-9).

We have given the model structure generated using alphafold2 for your reference.

Model generated by using AlphaFold2.ipynb (https://colab.research.google.com/github/sokrypton/ColabFold/blob/main/AlphaFold2.ipynb#scrollTo=kOblAo-xetgx).

Structure quality assessment by __http://saves.mbi.ucla.edu/.__

GAP 45

__S14 __

MTIP

487 What parts of theses genes was cloned? Define the amino acid range.

Response: The full-length protein-encoding gene was cloned.

714 Please split the table into A Mosquito bite and B haemolymph Sporozoites Response: Done.

Figure 1 For clarity, maybe write S14::mCherry

Response: Done.

Figure 1 It would be useful to show blood stage parasite images.

Response: Blood stage parasite image is included in the revised manuscript as Figure S2.

Figure 2G Haemolymph sporozoites ?

Response: Done.

Figure 8 You argued that S14 is a membrane-bound protein through palmitoylation. Here the protein is shown to be cytoplasmic. Please update our model with more recent ones. Response: We have shown that S14 colocalizes with GAP45 and MTIP, suggesting its IMC localization. We have updated our model in Figure 8.

Figure S2B It would be good to include a positive control for these PCRs.

Response: We have replaced the figure's new gel with a positive control.

Figure S3 It would be good to include a positive control for these PCRs. Response: We already have positive controls in Figure S3C and S3F for all the primer pairs used.

Tabel S1 Table S1 is only mentioned twice in the text: lines 124 and 128. There is no mention that the table contains all (??) known gliding motility proteins.

Response: The table does not contain all the gliding proteins; however, most of the proteins mentioned in the Boucher & Bosch, 2015 paper (doi: 10.1016/j.jsb.2015.02.008) were included.

Table S1 The algorithms / websites used for bioinformatic prediction need to be listed here.

Response: Included.

Table S2 Add the plasmodb gene identifiers here. The table does not show all Plasmodium spp. but a selection. Response: All the orthologs mentioned in Figure S1 and Table S2 are not shown in the updated PlasmoDB. Accordingly, we have removed the Figure S1 and Table S2 in the revised manuscript__.__

Reviewer #1 (Significance (Required)):

General assessment: The authors provide an in-depth analyses of the Plasmodium berghei protein S14 and its involvement in gliding motility. Response: Thank you.

Advance: This paper is the first analysis of the S14 protein. The authors suggest a bridging function for the protein between MTIP and GAP45. Response: Thank you.

Audience: Gliding motility is of interest to the apicomplexan field. I think this particular proteins is specific to Plasmodium spp. Response: Thank you.

Reviewer #2

Summary:

The authors tag the sporozoite protein S14 in P. berghei and show localization near the sporozoite plasma membrane. They also convincingly show, through the generation of S14 knockout lines, that S14 is required for sporozoite motility and thereby also salivary gland and hepatocyte invasion. Their bioinformatic results support possible interactions between S14 and the inner membrane complex proteins MTIP and GAP45. These analyses were performed with these specific candidate proteins rather than being unbiased searches for potential interaction partners. The yeast 2-hybrid data to support these possible protein interactions need further controls.

Lines 143-144: Unless the sporozoites were not permeablized prior to staining, it is not clear if the protein is "on" the plasma membrane or just under the plasma membrane. Furthermore, this statement anyway seems contradictory to the authors' interpretation of Figure 4A. Response: Live S14-mCherry localization on the membrane does not differentiate between the outer membrane or IMC. Next, in Figure 4A, we confirmed S14 localization on IMC by treating sporozoites with Triton X-100 and colocalizing with IMC proteins GAP45 and MTIP. Further, we ensured that mCherrey signals were bleached post-fixation and performed IFA with and without permeabilization. We revealed the mCherry and CSP signals using Alexa 488 and Alexa 594, respectively. We observed the mCherrey signal with permeablized sporozoites, not without permeabilization.

Line 218: "This result indicates that S14 is present within the inner membrane of sporozoites." While this data shows that S14 is not in the plasma membrane of the parasite, how can the authors be sure it is at the IMC? Response: S14 colocalization with MTIP and GAP45 suggested its localization on IMC.

Line 225-226: This sentence overreaches in its conclusion. There is no indication that this protein provides the power or force behind the sporozoites forward movement. Several proteins are known to be required for gliding motility, but they are not all force-providing factors. Response: We have modified the sentence, and now it states, ‘These data demonstrate that S14 is an IMC protein, essential for the sporozoite's gliding motility.

Minor comments:

Line 99: "the role of gliding-associated proteins is unexplored" There are several publications on GAP40, GAP45 and GAP50 (some of which are referenced in the previous paragraph). Response: We have included the reference for studied proteins and modified the sentence for clarity.

Line 114: "We narrowed it down to a candidate" Narrowed down how? Or rephrase. Response: We identified the S14 gene from the Kaiser et al., 2004 paper (DOI: 10.1046/j.1365-2958.2003.03909.x) and rephrased the sentence in the revised manuscript.

Lines 120-123 are strangely written, and I don't follow the logic. What "similar properties" do GAP45 and GAP50 have with S14 and are they really indicative of function? Also if palmitoylation and myristylation and nonclassical secretion are present in most eukaryotes, why would they necessarily be evidence of IMC targeting? Response: It was wrongly written, we have modified the sentence for clarity.

Line 148-149. I did not see examples of this electromobility shift of GAP45 in this publication (although I may have overlooked it).

Response: Electromobility shifts of GAP45 due to the palmitoylation have been reported in (Rees-Channer et al, 2006; DOI: 10.1016/j.molbiopara.2006.04.008). Frenal 2010 paper has stated about two bands, but experimentally it was shown in Rees-Channer et al, 2006 in Figure 1 and 2B.

Table 1 legend should preferably specify that hemolymph sporozoites were used for IV infections. Response: Done.

Line 228: Should be rephrased for accuracy. "revealed the" should be replaced with "suggests" Response: Replaced.

Lines 305-307: I don't entirely understand the logic laid out here.

Response: This was written about GAP45 and MTIP coordination; however, it has been removed in the revised manuscript.

Lines 320-322: "We hypothesize that S14 possibly plays a structural role and maintains the stability of IMC required for the activity of motors during gliding and invasion." The data about the IMC structure shown is fluorescence microscopy - and there no change is observed in the IMC in the knockout line. I suggest removing or rephrasing this point if no extra data is provided to show this. Response: We have removed this sentence in the revised manuscript.

Reviewer #2 (Significance (Required)):

The work gives insights into an unstudied, conserved Plasmodium protein, S14, which the authors show is critical for Plasmodium transmission from mosquitoes. The parasite genetics and phenotyping demonstrating this are strong. The conclusions about interactions with glideosome/inner membrane complex components need further experimental support. The work is of interest to the Plasmodium field and may be also of interest to people interested in other protozoan parasites or in cellular motility.

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

The manuscript by Gosh and colleagues demonstrates that S14 is a glideosome-associated protein in sporozoites. S14 knockout sporozoites fail to infect mosquito salivary glands and liver cells in the mammalian host. These sporozoites are also defective in gliding motility as S14 localizes to the inner membrane. S14 was shown to interact with the glideosome-associated proteins GAP45 and MTIP using the yeast two-hybrid system. The authors also provide an in-silico prediction on the S14, GAP45 and MTIP interaction.

Major issues:

Overall, there is information lacking in the manuscript, including on the figure legends, regarding experiments replication and n analyzed.

For complementation, the authors engineered an independent S14 knockout line. For this line is clear that parasites failed to infect salivary glands contrarily to the knockout line. Despite not showing it, did the authors confirm that this knockout line has no defects in infecting mosquito midguts and producing sporozoites? Response: We analyzed the midgut for sporozoite formation, which was comparable to the original KO line, and included the data (Figure 2D) in the revised manuscript.

Did the authors conduct IV injections in mice with a higher number of sporozoites? Hemolymph sporozoites are less infectious than sporozoites collected from the salivary glands and I was wondering whether patent infections with S14 ko sporozoites can be obtained by injecting a higher inoculum. The same applies to the infectivity experiments with HepG2cells. Response: We increased the sporozoites dose and infected mice with 10,000 hemolymph sporozoites, but no infection was observed (Table 1). No EEFs were observed in HepG2 cells infected with 10,000 S14 KO hemolymph sporozoites.

Please provide information on the number of sporozoites that were analyzed in the trails experiment. Response: We analyzed 210, 225, and 212 sporozoites for WT GFP, S14 KO c1, and S14 KO c2, respectively.

Minor issues:

In Figure 1. F) WB on S14-3xHA-mCherry tagged sporozoites showing two bands on the WB. The Palm-band is only inferred thus I suggest correcting the figure to S14-3xHA-mcherry. On 1D all the mcherry signal is detected on the membrane but then on WB, a smaller fraction is palm? What is the explanation for the ratio between the two bands? Why so distinct CSP intensity bands between wt and tagged line? Were very distinct amounts of protein loaded?

Response: We have corrected the Palm-S14-3xHA-mcherry to S14-3xHA-mcherry.

This reviewer raises a valid point regarding the discrepancy between IFA and Western blot. The non-palmitoylated S14-mCherrey signal was possibly corrected after deconvolution in image 1D and mainly the membrane signal was prominent. In Figure 1C, many sporozoites show some cytosolic signal, perhaps representing non-palmitoylated S14. Western blot concentrates the protein of interest as a single band, allowing more accurate visualization of protein.

The distinct CSP intensity bands between wt and the tagged line are due to the loading of a higher amount of parasite lysate in WT lane. To ensure that the western blot signal is specific to S14, we loaded a higher amount of protein in WT.

Figure 1. A) Statistical analysis is missing. Not clear if the bars represent mean values +/- standard deviation. No information on the material and methods of how the relative expression was calculated. Response: No error bars are shown in Figure 1 because it was performed once.

In the introduction lines 54 and 58 I suggest replacing humans with mammalian host. Response: Replaced.

Line 58. Not clear why the ref Ripp et al., 2021 is used for a general sentence to introduce the Plasmodium life cycle. Response: Removed.

Line 72: I suggest replacing "TRAP mutant" with "TRAP knockouts" (Sultan et al., 1997). More recently there are TRAP mutants with impaired motility and normal invasion of mosquito salivary glands (Klug et al., 2020) Response: Replaced.

Lines 78 to 86: In this paragraph, authors refer to several proteins involved in sporozoite gliding motility and host cell invasion, however for most of the studies this conclusion comes from the characterization of knockouts defective phenotype and actually a direct role for some of these molecules in the process awaits clear demonstration. Response: We have replaced involved with implicated.

Line 78: Authors do not consider that maebl knockout sporozoites display reduced adhesion, including to cultured hepatocytes, which could contribute to the defects in multiple biological processes, such as in gliding motility, hepatocyte wounding, and invasion. Response: We have corrected maebl role in the revised manuscript.

Line 80: I suggest authors reconcile the contradictory reports in the literature on the role of TRSP in sporozoites invasion. Response: We have removed this reference in the revised manuscript.

Line 82-83: Please revise it. Response: Revised.

Table 1. Correct table as when sporozoites were transmitted by mosquito bite the term "number of sporozoites injected" does not apply. Please give more details on the bite experiments. Is this the number of mosquitoes for all four animals? For how long the mosquitoes were allowed to bite? Response: For clarity, we have split the table into A Mosquito bite and B haemolymph Sporozoites. We used ten mosquitoes/mice in the bite experiment. Mosquitos were allowed to probe for blood meal for 20 minutes, and the feeding was ensured by observing mosquitoes post-blood meal; approximately 70% of mosquitoes received the blood meal in all the cages.

Line 288 and 289. There are several publications showing that maebl knockout sporozoites are impaired at invading the mosquito salivary glands and at infecting the vertebrate host contradicting Kariu et al., 2002 findings in the vertebrate host. Response: We have removed maebl from this line.

Line 290. I suggest "was most likely due to" instead of " due to" as sporozoite adhesion to cells was not evaluated. Response: Corrected.

Line 291: "Cellular transmigration and host cell invasion are prerequisites for gliding motility" please revise. Response: Revised.

Line 437: indicate which clone was used.

Response: Indicated (3D11).

Line: 463: indicate the % of the gel in the SDS-PAGE Response: We have used 10% SDS-PAGE gel and it is indicated in the revised manuscript.

Line 499: indicate the version of the GraphPad Prism software. Response: GraphPad Prism version 9.

Figure S3 legend needs to be corrected. Panels in the figure are from A to F while in legend G and H are included. Response: Corrected.

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

Reviewer #2

Line 39-41: "Using in silico and the yeast two-hybrid system, we showed the interaction of S14 with the glideosome-associated proteins GAP45 and MTIP. Together, our data show that S14 is a glideosome-associated protein" Although these interactions can be speculated based on the results shown, these interactions were not confirmed in this study. Response: We attempted to pulldown the S14 interacting partner using anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

In order to claim interaction between S14 and IMC proteins, interaction needs to be shown experimentally. Well-controlled yeast 2-hybrid would be a start - then interaction would be more than just speculative. But immunoprecipitation from sporozoites or other biochemical interactions would give more support to this idea. Response: We attempted to pulldown the S14 interacting partner using an anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

Reviewer #3

The authors provide convincing data on the S14 localization in the inner membrane of sporozoites and interaction with GAP45 and MTIP using the yeast model. Did the authors consider conducting co-IP followed by MS analysis to pull down S14 in the complex with GAP45 and MTIP? Response: We attempted to pulldown the S14 interacting partner using an anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify the interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins, MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

__Reviewer #3 (Significance (Required)):____ __ Sporozoite gliding motility is a critical feature of parasite infectivity. Impairment of this important feature has been described for several mutant/knockout parasite lines. This study goes beyond the phenotypic analysis of mutant parasites to infer the role of S14 by providing more mechanistic evidence to show S14 interaction with other glideosome-associated proteins. However, this interaction was investigated using the two-hybrid system in yeast. Still, in sporozoites, no experiments were conducted to evaluate the interaction between these proteins.

Response: We attempted to pulldown the S14 interacting partner using an anti-mCherry antibody from S14-3XHA-mCherry transgenic sporozoites and then further tried to identify interactome using mass spectrometry but failed. Hence, we selected two known IMC localized gliding proteins, MTIP and GAP45. Performing pull-down from sporozoites is challenging, so we checked this interaction using yeast 2-hybrid assay and bioinformatic analysis for protein-protein interaction.

Please consider I'm not an expert on the in-silico interaction studies.

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

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

The manuscript by Gosh and colleagues demonstrates that S14 is a glideosome-associated protein in sporozoites. S14 knockout sporozoites fail to infect mosquito salivary glands and liver cells in the mammalian host. These sporozoites are also defective in gliding motility as S14 localizes to the inner membrane. S14 was shown to interact with the glideosome-associated proteins GAP45 and MTIP using the yeast two-hybrid system. The authors also provide an in-silico prediction on the S14, GAP45 and MTIP interaction.

Major issues:

Overall, there is information lacking in the manuscript, including on the figure legends, regarding experiments replication and n analyzed.

For complementation, the authors engineered an independent S14 knockout line. For this line is clear that parasites failed to infect salivary glands contrarily to the knockout line. Despite not showing it, did the authors confirm that this knockout line has no defects in infecting mosquito midguts and producing sporozoites?

Did the authors conduct IV injections in mice with a higher number of sporozoites? Hemolymph sporozoites are less infectious than sporozoites collected from the salivary glands and I was wondering whether patent infections with S14 ko sporozoites can be obtained by injecting a higher inoculum. The same applies to the infectivity experiments with HepG2cells.

The authors provide convincing data on the S14 localization in the inner membrane of sporozoites and interaction with GAP45 and MTIP using the yeast model. Did the authors consider conducting co-IP followed by MS analysis to pull down S14 in the complex with GAP45 and MTIP?

To characterize the gliding defective phenotype authors based their assessment on trails quantifications. This analysis is very limited as the percentage of attached, waving, floating sporozoites cannot be determined. Due to their conclusion on the role of S14 for sporozoite gliding motility, I recommend a more detailed investigation using live microscopy imaging. Please provide information on the number of sporozoites that were analyzed in the trails experiment.

Conclusions that S14 knockout does not impact the expression and organization of two surface proteins, CSP and TRAP, and two IMC rely on a qualitative analysis only. However, quantitative analysis to support their observations is missing.

Minor issues:

In Figure 1. F) WB on S14-3xHA-mCherry tagged sporozoites showing two bands on the WB. The Palm-band is only inferred thus I suggest correcting the figure to S14-3xHA-mcherry. On 1D all the mcherry signal is detected on the membrane but then on WB, a smaller fraction is palm? What is the explanation for the ratio between the two bands? Why so distinct CSP intensity bands between wt and tagged line? Were very distinct amounts of protein loaded?

Figure 1. A) Statistical analysis is missing. Not clear if the bars represent mean values +/- standard deviation. No information on the material and methods of how the relative expression was calculated.

In the introduction lines 54 and 58 I suggest replacing humans with mammalian host.

Line 58. Not clear why the ref Ripp et al., 2021 is used for a general sentence to introduce the Plasmodium life cycle.

Line 72: I suggest replacing "TRAP mutant" with "TRAP knockouts" (Sultan et al., 1997). More recently there are TRAP mutants with impaired motility and normal invasion of mosquito salivary glands (Klug et al., 2020)

Lines 78 to 86: In this paragraph, authors refer to several proteins involved in sporozoite gliding motility and host cell invasion, however for most of the studies this conclusion comes from the characterization of knockouts defective phenotype and actually a direct role for some of these molecules in the process awaits clear demonstration.

Line 78: Authors do not consider that maebl knockout sporozoites display reduced adhesion, including to cultured hepatocytes, which could contribute to the defects in multiple biological processes, such as in gliding motility, hepatocyte wounding, and invasion.

Line 80: I suggest authors reconcile the contradictory reports in the literature on the role of TRSP in sporozoites invasion.

Line 82-83: Please revise it.

Table 1. Correct table as when sporozoites were transmitted by mosquito bite the term "number of sporozoites injected" does not apply. Please give more details on the bite experiments. Is this the number of mosquitoes for all four animals? For how long the mosquitoes were allowed to bite?

Line 288 and 289. There are several publications showing that maebl knockout sporozoites are impaired at invading the mosquito salivary glands and at infecting the vertebrate host contradicting Kariu et al., 2002 findings in the vertebrate host.

Line 290. I suggest "was most likely due to" instead of " due to" as sporozoite adhesion to cells was not evaluated.

Line 291: "Cellular transmigration and host cell invasion are prerequisites for gliding motility" please revise.

Line 437: indicate which clone was used.

Line: 463: indicate the % of the gel in the SDS-PAGE

Line 499: indicate the version of the GraphPad Prism software.

Figure S3 legend needs to be corrected. Panels in the figure are from A to F while in legend G and H are included.

Significance

Sporozoite gliding motility is a critical feature of parasite infectivity. Impairment of this important feature has been described for several mutant/knockout parasite lines. This study goes beyond the phenotypic analysis of mutant parasites to infer the role of S14 by providing more mechanistic evidence to show S14 interaction with other glideosome-associated proteins. However, this interaction was investigated using the two-hybrid system in yeast. Still, in sporozoites, no experiments were conducted to evaluate the interaction between these proteins.

Please consider I'm not an expert on the in-silico interaction studies.

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors tag the sporozoite protein S14 in P. berghei and show localization near the sporozoite plasma membrane. They also convincingly show, through the generation of S14 knockout lines, that S14 is required for sporozoite motility and thereby also salivary gland and hepatocyte invasion. Their bioinformatic results support possible interactions between S14 and the inner membrane complex proteins MTIP and GAP45. These analyses were performed with these specific candidate proteins rather than being unbiased searches for potential interaction partners. The yeast 2-hybrid data to support these possible protein interactions need further controls.

Major comments:

Line 39-41: "Using in silico and the yeast two-hybrid system, we showed the interaction of S14 with the glideosome-associated proteins GAP45 and MTIP. Together, our data show that S14 is a glideosome-associated protein" Although these interactions can be speculated based on the results shown, these interactions were not confirmed in this study.

Lines 143-144: Unless the sporozoites were not permeablized prior to staining, it is not clear if the protein is "on" the plasma membrane or just under the plasma membrane. Furthermore, this statement anyway seems contradictory to the authors' interpretation of Figure 4A.

Line 218: "This result indicates that S14 is present within the inner membrane of sporozoites." While this data shows that S14 is not in the plasma membrane of the parasite, how can the authors be sure it is at the IMC?

Line 149: To definitively state S14 is a membrane protein, biochemical assays proving such should be performed. (or perhaps genetic mutation of the predicted palmitoylation site?) Otherwise, this should be rephrased.

Line 225-226: This sentence overreaches in its conclusion. There is no indication that this protein provides the power or force behind the sporozoites forward movement. Several proteins are known to be required for gliding motility, but they are not all force-providing factors.

Lines 257-258: for yeast 2-hybrid, the controls of expressing S14, GAP45 and MTIP together with control proteins where no interaction would be predicted are absent.

In order to claim interaction between S14 and IMC proteins, interaction needs to be shown experimentally. Well-controlled yeast 2-hybrid would be a start - then interaction would be more than just speculative. But immunoprecipitation from sporozoites or other biochemical interactions would give more support to this idea.

Minor comments:

Line 99: "the role of gliding-associated proteins is unexplored" There are several publications on GAP40, GAP45 and GAP50 (some of which are referenced in the previous paragraph).

Line 114: "We narrowed it down to a candidate" Narrowed down how? Or rephrase.

Lines 120-123 are strangely written, and I don't follow the logic. What "similar properties" do GAP45 and GAP50 have with S14 and are they really indicative of function? Also if palmitoylation and myristylation and nonclassical secretion are present in most eukaryotes, why would they necessarily be evidence of IMC targeting?

Line 148-149. I did not see examples of this electromobility shift of GAP45 in this publication (although I may have overlooked it).

Table 1 legend should preferably specify that hemolymph sporozoites were used for IV infections.

Line 228: Should be rephrased for accuracy. "revealed the" should be replaced with "suggests"

Lines 305-307: I don't entirely understand the logic laid out here.

Lines 320-322: "We hypothesize that S14 possibly plays a structural role and maintains the stability of IMC required for the activity of motors during gliding and invasion." The data about the IMC structure shown is fluorescence microscopy - and there no change is observed in the IMC in the knockout line. I suggest removing or rephrasing this point if no extra data is provided to show this.

Significance

The work gives insights into an unstudied, conserved Plasmodium protein, S14, which the authors show is critical for Plasmodium transmission from mosquitoes. The parasite genetics and phenotyping demonstrating this are strong. The conclusions about interactions with glideosome/inner membrane complex components need further experimental support. The work is of interest to the Plasmodium field and may be also of interest to people interested in other protozoan parasites or in cellular motility.

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

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary: The authors have identified a sporozoite gliding motility protein through bioinformatic analysis. From the main text I do not know how, or what bioinformatic analysis was performed, in order to focus on this protein which is called S14. The authors then go on to tag the protein, produce a KO and show its involvement in gliding motility. The KO shows that parasites lacking S14 fail to invade the mosquito salivary glands. This is due to a motility defect. Y2H and docking studies are used to define an interaction with MTIP and GAP45, two known components of the glideosome.

Major comments: The paper is sometimes hard to follow and lacks clarity. The reason: important information is omitted, or explained at the end of a section rather than at first mention; experimental details that are of essence need to be mentioned or explained in the main text; there is ample use of the word 'bioinformatic' without explaining what kind of analysis was performed in the main text. I cite from the abstract: 'In silico analysis of a novel protein, S14, which is uniquely upregulated in salivary gland sporozoites, suggested its association with glideosome-associated proteins.' I cite from the introduction: 'A study comparing transcriptome differences between sporozoites and merozoites using suppressive subtraction hybridization found several genes highly upregulated in sporozoites and named them 'S' genes (Kaiser et al, 2004). We narrowed it down to a candidate named S14, which lacked signal peptide and transmembrane domains.' From reading the main text, I do not know why Plasmodium berghei S14 was chosen in this manuscript. S14 is one of 25 transcripts identified by Kappe et al in Plasmodium yoelii (https://doi.org/10.1046/j.1365-2958.2003.03909.x) to be upregulated in sporozoites. The material and methods section does not explain either why S14 was chosen. Perhaps the authors could update Figure 2 from Kappe et al with the most recent annotations from plasmodb.

Reproducibility: None of the main Figures or Figure legends define ' N = '. For example I cite: 'The S14 KO clonal lines were first analyzed for asexual blood-stage propagation, and for this, 200 µl of iRBCs with 0.2% parasitemia was intravenously injected into a group of mice.' There are 2 mentions of 'N=' in the supplementary figures. I have not found any others.

I'm not sure what the convention is. Should unpublished data for this gene (PBANKA_0605900) found in pberghei.eu (a database for mutant berghei parasites) be cited? After all it confirms their findings.

The authors need to use more recent references for some of their statements; see some comments below.

Minor comments:

line

1-2 Add the Plasmodium species of this study. abstract Which species do you work with? 29 mosquito salivary glands and human host hepatocytes 30 to the glideosome, a protein complex containing [...] 32-33 What kind of in silico analysis suggested S14 is part of the glideosome? S14 is not uniquely upregulated; there are other S-type genes identified by Kappe and Matuschewski. 25 I believe. 32 Please point out he species were S genes were identified. SGS of which species? 34 expression: change to transcription 39 What kind of in silico analysis was used here? and therefore malaria transmission 55 A single zygote transforms into a single ookinete, which establishes a single oocyst, which in turn can produce thousands of midgut sporozoites. Please correct the life cycle passage. located or anchored in the IMC? And located between the IMC and plasma membrane? 61-63 Refer to Table S1 and its contents here 64 Name the known GAPs.

65-67 Which transmembrane domain proteins? Please add more recent references than King 1988. 71-72 TRAP was the first protein found to be ... 74-76 Add additional, more recent references: for example search Frischknecht and TRAP 76 S6 (TREP) is also [...] 88 Some of these proteins are also expressed in ookinetes. 89-91 The sentence needs a verb. 88-96 Please add some more recent glideosome papers. After 2013. 91 Why do you call it a peripheral protein? 91-93 There are more recent citations for GAP45 andGAP50. 96 Insert a reference here. 99 Please define the gliding-associated proteins. What are they? Aren't there papers on GAP40, 45 and 50? DOI: 10.1016/j.chom.2010.09.002 99 .... What prompted you to identify a novel GAP? And why is S14 classified as a GAP? 99-102 What kind of bioinformatic study? Why was S14 chosen? Please outline how you ended up with S14. Any other proteins that came out of the bioinformatic screen from the list of S genes? How many proteins were identified in the screen for sporozoite upregulated proteins by Kappe and Matuschewski? 102-103 Define the nonclassical secretion pathway. Please reference GAP45 and GAP50 data for the nonclassical pathway. 105 Please add P. berghei to the title, the abstract, the introduction. 111 The results section does not outline what bioinformatic analysis was used 112-114 Please specify the exact number of upregulated in sporozoites genes. I think it was 25. And add the species the study was performed in. Why did you choose the Kappe study but not the uis genes from berghei? 114-115 How did you narrow it down to S14? The Kappe paper lists 25 S-type genes from P. yoelii. 118 Plasmodia is not the plural for a group of different Plasmodium species. Use: [...] conserved among Plasmodium spp. 118-119 Which proteins did you analyze? And how did you analyze them? Where is the data for this analysis? Outline the amino acids that predict palmitoylation? The nonclassical pathway? 119-122 Here: do you mean S14 has similar properties as GAP 45 and GAP50? Define the nonclassical pathway? How do you know S14 is in the IMC? 122-123 Please reference the bioinformatic analysis plus URL that allows targeting to the IMC to be analyzed. 123-124 Please reference the URLs for TM, palmitoylation, and interactions analyses. 125-127 How did you predict that S14 is secreted via the nonclassical pathway? 128-130 Define the nonclassical pathway when it first appears in your manuscript. The citation Moskes 2004 is not in the reference list 132 Which membrane? 134-135 In which species? 141-142 Please include images of blood stage and liver stage parasites. 142-143 Which membrane? 148-149 I cannot find the specific figure you refer to; I checked the online version of the Frenal 2010 paper. 175 gland, we counted [...] 177 Compared to the 177-179 Failed to invade (absolutely)? Or invaded in highly reduced numbers? 182-186 Please be precise: I think you mean you let all types of mosquitoes take a blood meal; s14 knockout-infected mosquitoes did not infect mice. 181-202 Perhaps use paragraphs to indicate the different types of experiments performed here. 204 Please introduce paragraphs to identify the different experiments in this section 208 Outer or inner membrane of what? IMC, the plasma membrane? 228 onwards Structural models were obtained from whom? Which species did you use for the docking study? Could you use in one approach 3 berghei proteins, and confirm your docking studies with the falciparum proteins? That would strengthen your model. Should you include a negative control protein in the approach? 250-251 Was all of the gene cloned? Please define amino acid range. discussion Please discuss data from https://elifesciences.org/articles/77447 in relation to your protein

298-300 More recent glideosome papers exist. For example https://doi.org/10.1038/s42003-020-01283-8 340 List the proteins you analysed. Add URL (websites) to the analyses tools. 343 Known association from the literature: how was this done? 346-349 A few glideosome components? On what basis were they selected and which are they?

471 Can AlphaFold Structure Predictions be used in the docking studies? 487 What parts of theses genes was cloned? Define the amino acid range. 714 Please split the table into A Mosquito bite and B haemolymph Sporozoites Figure 1 For clarity, maybe write S14::mCherry Figure 1 It would be useful to show blood stage parasite images. Figure 1F You have not formally shown that this signal corresponds to palmitoylated S14. Could be heavy chain. Figure 2G Haemolymph sporozoites ? Figure 8 You argued that S14 is a membrane-bound protein through palmitoylation. Here the protein is shown to be cytoplasmic. Please update our model with more recent ones.

Figure S2B It would be good to include a positive control for these PCRs. Figure S3 It would be good to include a positive control for these PCRs.

Tabel S1 Table S1 is only mentioned twice in the text: lines 124 and 128. There is no mention that the table contains all (??) known gliding motility proteins. Table S1 The algorithms / websites used for bioinformatic prediction need to be listed here. Table S2 Add the plasmodb gene identifiers here. The table does not show all Plasmodium spp. but a selection.

Significance

General assessment: The authors provide an in-depth analyses of the Plasmodium berghei protein S14 and its involvement in gliding motility.

Advance: This paper is the first analysis of the S14 protein. The authors suggest a bridging function for the protein between MTIP and GAP45.

Audience: Gliding motility is of interest to the apicomplexan field. I think this particular proteins is specific to Plasmodium spp.

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Reply to the reviewers

1. General Statements

This manuscript aimed at:

1. a) producing the evidence that supports the need for performing RNA hydrolysis and applying the appropriate nucleoside MACs for the determination of nucleoside-modified mRNA concentrations using UV spectroscopy.
2. b) Providing the m1Y MAC value and a new resource to the mRNA field community to perform the above-mentioned procedure. This piece is therefore a “resource” manuscript, rather than a biotechnological innovation or basic research manuscript.

2. Point-by-point description of the revisions

Considering that the reviewers coincided in some of their comments, we compiled them in topic and provided our response to the reviewers.

Topics:

• On the novelty in this manuscript
• On the impact of nucleoside modifications on the DFBHI-Broccoli complex.
• On the role of modified nucleosides on mRNA folding and the independent verification on a distinct mRNA.
• On the cap used for IVT in the webserver.
• On the average of Epsilon (e or MAC) values.
• Other minor comments. On the novelty in this manuscript:

Comments:

Reviewer #1

“Major Comments:

• In the introduction, the authors should discuss the novelty more by describing which techniques are currently available for quantification of modified RNA and how this study is novel.” __Reviewer #2 __

“(Significance (Required)):

The study develops an accurate method to measure RNA concentrations which can improve dosing accuracy. The methods developed here will be beneficial for a broad range of fields employing mRNA-therapies.”

__Reviewer #3 __

“(Significance (Required)):

Since 50 years, scientists that works in the field of modified nucleic acids have determined the concentration of the nucleic acids in the same way, which means by determining the epsilon values of the modified nucleosides, using the epsilon values of the natural nucleosides at same wavelength, and then calculating the concentration after measuring absorption at (for example) 260 nm (wavelength could change dependent on modified nucleoside that is incorporated). This manuscript is not really innovative.”

---

Response:

We thank the reviewers for bringing up this topic. We want to reassure to the reviewers, editors and readers that, throughout the manuscript, we have carefully selected the wording to avoid claiming any novelty on the principle of RNA hydrolysis or the use of nucleotide Molar absorption coefficients (MAC) and UV spectroscopy for the determination of RNA concentrations. We have “revised”, “assessed” and “examined” these experimental procedures, we “determined” the M1Y and we “developed” the mRNAcalc webserver.

This “resource” manuscript therefore mainly aims at introducing the mRNAcalc webserver to the community and providing the underlying biochemical principles of the methods suggested in the webserver. These articles are often published in webserver issues or as “resource” articles in certain journals, including some of the journals in Review Commons.

The authors understand that the data in our manuscript are not often provided for this type of “resource” manuscripts, and it might have led to a misunderstanding. For instance, the OligoCalc webserver was published in Nucleic Acid Research, it has become a valuable tool for the oligonucleotide research community (1621 citations in 15 years), and no experimental evidence supporting its underlying calculations is provided in the manuscript.

For our manuscript, we have cited the corresponding source of the principle of the experimental methods, and we additionally performed some experiments to reproduce the findings using nucleoside-modified mRNAs with the intention of highlighting the importance of performing RNA hydrolysis (Fig.2b) and implementing the MAC of modified nucleotides (Fig 1e and 1f) for the determination of modified-nucleoside mRNA concentration using the Beer-Lambert law. We have felt compelled to do so, despite the fact that they represent well-established science and methods, as correctly pointed out by one of the reviewers.

We have taken into account that a few dozen of non-RNA biochemistry focused laboratories around the world are currently embracing for the first time the nucleoside-modified mRNA technologies and, to our knowledge, not a single article in the nucleoside-modified mRNA field has mentioned the need of implementing a different MAC for the determination of nucleoside-modified mRNA concentration using UV spectroscopy in either its main text or Materials & Methods section. We want to reassure the reviewers that the authors, before starting the experimental investigation, performed an extensive literature search and failed to find the m1Y MAC at 260 nm. Our search included a few hundreds of research articles, several doctoral thesis (including Sister Miriam Michael Stimson’s work), classic books such as Hall, Ross “The modified nucleosides in nucleic acids” and nucleotide manufacturers’ datasheets. However, the authors cannot rule out that other investigators in the mRNA field have previously determined the m1Y MAC at 260 nm in aqueous buffered solution and this knowledge has remained hidden under the frequently used statement of “The mRNA concentrations were determined spectroscopically” or any alike statement.

Following the suggestion of Reviewer #1, we have also included a brief comment in the introduction on the fluorescence-based techniques for the determination of nucleic acid concentration (lines 87-91), as follows:

“Other non-UV-spectroscopic methods relying on the unspecific RNA binding of certain fluorophores (such as RiboGreen, Thermo Fisher Scientific) for the determination of RNA concentration may help to overcome any change in the MAC of modified nucleoside mRNA. However, the impact of RNA modifications on the binding affinity of these fluorophores also remains unknown.”

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On the impact of nucleoside modifications on the DFBHI-Broccoli complex:

Comments:

Reviewer #1

“3) The broccoli aptamer has U in it which when mutated to pseudouridine (Ψ) or N1-methylpseudouridine may change the structure minutely affecting the cis-trans transition in aptamer- DFHBI-1 complex and hence in fluorophore properties. A control which shows the effect (or lack thereof) of aptamer modifications on fluorophore properties should be carried out. The ratio of A260/F507 can get affected by the denominator although it may/may not be insignificant.”

Reviewer #2

“Specific comments:

…

In Fig. 1D, the authors normalize the absorbance on mRNA to fluorescence of DFHBI-1T when bound to dBroccoli aptamer. The aptamer will contain uridines and therefore modified uridines. Will modified uridines affect binding affinity of the substrate to the aptamer? Could the differences in fluorescence be because of stronger/weaker binding of the substrate with modified uridines?”

Response:

We thank reviewers for enquiring about the effect of U-to-Y and U-to-M1Y substitutions on the DFHBI-1T-dBroccoli interaction, RNA folding or fluorophore properties. We have indeed investigated thoroughly and observed that there was no significant difference in the binding affinity, melting point, or relative brightness across the three DFHBI-1T-Broccoli complexes. These results go in line with the previously published photophysical and biochemical properties of the Broccoli−DFHBI-1T (reference 15 in manuscript). These data are provided as supplementary Table 1 in the revised manuscript.

Supplementary Table 1: photophysical and biochemical properties of mutated Broccoli−DFHBI-1T complexes.

Complex

Max em (nm)

Relative brightness*

KD (nM)+

Tm (°C)+

U-Broc−DFHBI-1T

(ref. 15)

507

---

360

48

U-Broc−DFHBI-1T

507

1.000 ± 0.002

379.6 ± 13.89

49.13 ± 0.13

Y-Broc-DFHBI-1T

507

1.005 ± 0.004

378.7 ± 8.11

49.46 ± 0.09

m1Y-Broc-DFHBI-1T

507

1.004 ± 0.003

375.6 ± 8.17

49.23 ± 0.07

*Relative to the U-Broc-DFHBI-1T complex. Data are shown as mean ± SD.

• Data are shown as KD ± Error of the fit or Tm ± Error of the fit.

On the role of modified nucleosides on mRNA folding and the independent verification on a distinct mRNA:

Comments:

Reviewer #1

“2) Fig 1d- In this experiment, the RNA is not hydrolyzed prior to concentration measurement. The authors should discuss how nucleoside modifications in the RNA may affect structure of the RNA, how significant that effect is on the ____e ____(MAC) and how justified it is to attribute the reduction in ____e ____(MAC) entirely to the mutations.

…

4) The reduction in A260 in modified nucleosides should be accurately measured and independent of the RNA. Hence, the values determined here should be shown to be independent of at least another RNA sequence.”

Response:

We want to express our gratitude to Reviewer #1 for enquiring about the potential impact of the modified nucleosides on the mRNA folding. We have further discussed this aspect on our interpretation of the data in Fig 1d. No doubt, this reviewer’s comment has substantially enriched the discussion in our manuscript.

For the revised version of the manuscript, we have also performed the same measurements using a different mRNA. We have used an mRNA with a higher m1Y composition. We have observed a stronger reduction in mRNA UV absorption (A260) in the m1Y-modified mRNA, confirming that the MAC of the nucleobase composition is the main determinant of mRNA UV absorption. We have appended these data to the manuscript as supplementary Figure 2 and the associated text can be found in lines 141-155 of the manuscript and in the following lines:

“By normalizing the UV absorbance (A260) of each mRNA by its corresponding fluorescence (F507), it was observed that in practice the relative UV absorbance of the nucleoside-modified mRNA was significantly reduced as compared to the standard mRNA (DA260 = -10.6%, Fig. 1d and 1e). The hypochromicity was more pronounced in a second m1Y-mRNA with higher m1Y composition (DA260 = -11.8%, Supplementary Figure 1). In principle, the modified nucleosides can also promote mRNA folding and reduce its UV absorption. This is particularly relevant for the pseudouridine modification. Its N1-hydrogen can engage in additional hydrogen bonds, promoting and stabilizing RNA folding. For instance, the U-to-Y substitution in tRNA stabilizes the folded structure that is essential for translation (reviewed in ref. 16). However, the m1Y nucleobase lacks this additional hydrogen bonding capability, and it is expected to have little or no effect on the RNA folding of low CG-content (1Y-mRNAs followed the anticipated hypochromicity associated to the nucleobase hypochromicity at 260 nm wavelength and not their expected contribution to RNA folding, these data suggest that the observed reduction in nucleoside-modified mRNA UV absorption is mainly determined by the nucleobase composition and the intrinsic MAC of the nucleosides in these mRNA.”

On the cap used for IVT in the webserver:

Comment:

__Reviewer #2 __

“(Evidence, reproducibility and clarity (Required)):

Specific comments:

1. The authors should expand discussion on the effect of different caps used for IVT as the choice of the cap appears to be an important selection on the server.” Response:

We thank Reviewer #2 for spotting that we had forgotten to comment on this feature of mRNAcalc web server in the manuscript. We have included a short paragraph on the 5’ mRNA cap nucleotides and their implementation in the mRNACalc webserver (line 160-164), as follow:

*“In the mRNACalc webserver, the MACs of distinct modified nucleosides that form the capping nucleotide in the 5’ mRNA cap were also implemented for the sake of completeness. The capping nucleotide only represents one nucleotide out of thousands of nucleotides in a mRNA molecule and its contribution to the mRNA molar absorption is rather negligible.” *

On the averaged Epsilon (____e ____or____ MAC) values:

Comment:

__Reviewer #3 __

(Evidence, reproducibility and clarity (Required)):

“I find the way the authors use the epsilon value of pseudoU (and analogues), as a mean value of literature data to be incorrect. The epsilon value is absolute and can not vary from one measurement to another. In fact it is a good parameter to define concentration. When different values are obtained, it means that compound is not pure , or measured at different pH or solvent, or the compound is not weighted exactly. When publishing a methodology to determine concentration of nucleic acids, it might be good to determine the exact epsilon value you want to use, yourself.”

Response:

We thank Reviewer #3 for bringing up this topic. We had experimentally determined the MAC values when we observed that it was completely absent in the literature and it was essential to provide a valuable tool to the nucleoside-modified mRNA community, as it is the case of the m1Y nucleoside. For the Y and m5C nucleosides, we have now determined their MAC for this revised version of the manuscript and recalculated the average, this time including our own determination and the previously determined values (in aqueous buffered solution) from multiple sources in the literature or manufacturer’s product datasheets and we implemented it in the webserver. We agree that the different values may relate to distinct amount and nature of the impurities in the manufacturer’s preparation. We believe that the average of these values may reflect a better approximation to their absolute epsilon value. Detailed information on these calculations and methods are now provided in the supplementary notes (Lines 109 to 142).

Other minor comments:

Reviewer #1

“5) Fig 2c- The figure should be remade using larger symbols as it is difficult to see how different the concentration measurements are depending on the method of hydrolysis.”

Response:

Figure 2c is intended to show a schematic representation of the experimental workflow and use of the mRNAcalc webserver. We assume that Reviewer #1 referred to Fig 2b. We have enlarged the symbols to ease the visibility of the data.

“6) Lines 27, 45 and 33 have an incorrect symbol for ____e____(MAC) and for the word 'coefficient”

Response:

We thank Reviewer #1 for the interest of improving our manuscript in detail. The typos have been corrected in the revised manuscript.

We thank Reviewers for all the values comments to our manuscript; they have enriched and substantially improved its quality and readability.

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Referee #3

Evidence, reproducibility and clarity

I find the way the authors use the epsilon value of pseudoU (and analogues), as a mean value of literature data to be incorrect. The epsilon value is absolute and can not vary from one measurement to another. In fact it is a good parameter to define concentration. When different values are obtained, it means that compound is not pure , or measured at different pH or solvent, or the compound is not weighted exactly. When publishing a methodology to determine concentration of nucleic acids, it might be good to determine the exact epsilon value you want to use, yourself.

Significance

Since 50 years, scientists that works in the field of modified nucleic acids have determined the concentration of the nucleic acids in the same way, which means by determining the epsilon values of the modified nucleosides, using the epsilon values of the natural nucleosides at same wavelength, and then calculating the concentration after measuring absorption at (for example) 260 nm (wavelength could change dependent on modified nucleoside that is incorporated). This manuscript is not really innovative.

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

General Comments:

Finol and colleagues argue that uridine modifications absorb less UV light than uridine, leading to underestimation of RNA concentration for modified RNAs. Based on this observation, they created a web server for accurate calculation of RNA concentrations. This is an interesting manuscript and would benefit the field. Specific comments are listed below:

Specific comments:

1. The authors should expand discussion on the effect of different caps used for IVT as the choice of the cap appears to be an important selection on the server.
2. In Fig. 1D, the authors normalize the absorbance on mRNA to fluorescence of DFHBI-1T when bound to dBroccoli aptamer. The aptamer will contain uridines and therefore modified uridines. Will modified uridines affect binding affinity of the substrate to the aptamer? Could the differences in fluorescence be because of stronger/weaker binding of the substrate with modified uridines?

Significance

The study develops an accurate method to measure RNA concentrations which can improve dosing accuracy. The methods developed here will be beneficial for a broad range of fields employing mRNA-therapies. Reviewer expertise: Lipid nanoparticles, mRNA, self-amplifying RNA, immunoengineering

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Referee #1

Evidence, reproducibility and clarity

Summary: The study aims at developing a method of accurate quantification of concentration of self- amplifying RNA and modified RNA by determining molar absorption coefficient of modified nucleosides with higher accuracy.

Major Comments:

1. In the introduction, the authors should discuss the novelty more by describing which techniques are currently available for quantification of modified RNA and how this study is novel.
2. Fig 1d- In this experiment, the RNA is not hydrolyzed prior to concentration measurement. The authors should discuss how nucleoside modifications in the RNA may affect structure of the RNA, how significant that effect is on the (MAC) and how justified it is to attribute the reduction in (MAC) entirely to the mutations.
3. The broccoli aptamer has U in it which when mutated to pseudouridine (Ψ) or N1-methylpseudouridine may change the structure minutely affecting the cis-trans transition in aptamer- DFHBI-1 complex and hence in fluorophore properties. A control which shows the effect (or lack thereof) of aptamer modifications on fluorophore properties should be carried out. The ratio of A260/F507 can get affected by the denominator although it may/may not be insignificant.
4. The reduction in A260 in modified nucleosides should be accurately measured and independent of the RNA. Hence, the values determined here should be shown to be independent of at least another RNA sequence.

Minor comments:

1. Fig 2c- The figure should be remade using larger symbols as it is difficult to see how different the concentration measurements are depending on the method of hydrolysis.
2. Lines 27, 45 and 33 have an incorrect symbol for (MAC) and for the word 'coefficient'

Significance

Accurate measurement of RNA concentrations can be key where precise quantification of RNA is required and any error gets amplified such as RNA-based therapeutics dependent on RNA amplification or RNA modification. This study is also important for research on the effect of RNA modifications on RNA structure in vitro or in vivo.

Transparent Peer Review

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Reply to the reviewers

Manuscript number: RC-2023-02123

Corresponding author(s): Holger Sültmann

[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.

The document is important for the editors of affiliate journals when they make a first decision on the transferred manuscript. It will also be useful to readers of the preprint and help them to obtain a balanced view of the paper.

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 would like to thank the editorial team of Review Commons for sending our manuscript for peer review and all Reviewers for carefully reading our manuscript. The reviewer’s detailed and constructive feedback and comments were instrumental to improve the quality and rigor of our manuscript. We highly appreciate the thoroughness of the review and have carefully considered all suggestions and concerns. Below, we have made point-by-point responses to the reviewer’s comments, and outlined revisions we plan to make, or have made. Textual changes in the revised manuscript are marked in Red.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

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

Daum AK et al. indicated that CAFs promote TKI resistance via lipid biosynthesis in ALK-driven lung adenocarcinoma cells. This work provides novel CAF-induced drug resistant mechanisms in ALK-driven lung cancer cells, however, there are several issues to be resolved by the following.

Major critiques:

1. The authors claimed that CAF-produced HGF and NRG1 boosts AKT signaling and de novo lipogenesis to promote ALK-TKI resistance in lung cancer cells. They showed that CAF-secreted HGF and NRG1 inhibition attenuates tumor cell viability in the presence of FB2-CM, however, whether stromal HGF and NRG1 inhibition suppresses de novo lipogenesis in carcinoma cells has not yet been investigated. The authors should inhibit HGF and NRG1 expression in CAFs by shRNA prior to addition of CAF-CM onto cancer cells to evaluate AKT signaling and de novo lipogenesis.

Author response:

The necessity of demonstrating the direct impact of stromal HGF and NRG1 inhibition on de novo lipogenesis in cancer cells is a crucial aspect of our study, and appreciate the reviewer’s valuable suggestion to inhibit HGF and NRG1 expression in CAFs before assessing the effect on AKT signaling and de novo lipogenesis. To address this concern, we will conduct additional experiments to evaluate the impact of HGF and NRG1 expression knock-downs in CAFs by shRNA.

This work lacks human correlation. Are HGF and NRG1 expressions in CAFs related with de novo lipogenesis, drug resistance and poor outcomes in ALK-driven lung cancer patients?

__Author response: __

We agree with the reviewer’s point that human correlation would underline the significance of the given findings. However, conducting such analyses presents certain challenges.

1. The availability of ALK-mutated samples among TCGA samples is limited and the sample size is quite small (n = 5), making survival analyses less statistically meaningful due to low statistical power.
2. Using bulk RNA-seq data for this analysis necessitates deconvolution methods to differentiate between tumor and stromal cell compartments. While deconvolution methods are valuable, they have limitations, including potential inaccuracies in estimating cell-specific gene expression due to the inherent heterogeneity of cell populations (1). This may lead to imprecise conclusions about the specific contributions of stromal factors, such as CAF-secreted HGF and NRG1, in the tumor microenvironment. Nonetheless, we are considering leveraging the available dataset of Maynard et al.(2), to address the raised concerns by the reviewer. Here, the authors performed single-cell RNA-seq on clinical biopsies, including a number of ALK+ samples from both treatment-naive and progressive-disease patients. The analysis of this dataset could allow us to investigate whether the effects observed in our study hold true in the in vivo human tissue environment, providing a more direct and clinically relevant assessment.

The most experiments lack the appropriate control for CAFs. They would use primary isolated counterpart fibroblasts as the patient-specific control for lung cancer CAFs by extracting from non-cancerous regions of the same individual in their experiments.

__Author response: __

This point is well taken. Therefore, we will take this feedback into account and incorporate the suggested controls into our experimental design to enhance the robustness and validity of our results.

Minor issues:

In Fig 1B, coculture with TGF-b-treated MRC-5 attenuated cancer cell death with the lorlatinib treatment. However, HGF and NRG1 production is comparable between MRC-5 cells treated with or without TGF-b in Fig 5A. These data indicate that any fibroblasts but not CAFs could suppress cancer cell death with the lorlatinib treatment.

__Author response: __

We recognize the need for further clarification. To address this, we plan to include additional data to demonstrate the differences in tumor therapy response when cultured with CM derived from native fibroblasts versus TGF-β1-activated fibroblasts (CAFs). This will help elucidate the specific role of CAFs in suppressing cancer cell death with lorlatinib treatment and provide a more comprehensive understanding of the observed effects.

The pAKT induction of H3122 treated with lorlatinib in the presence of CAM-CM or HGF or NRG in Fig 7A, B is barely observed and lacks the significance.

Author response:

We acknowledge the need for more robust data to demonstrate the significance of the observed pAKT induction in H3122 cells treated with lorlatinib in the presence of CAF-CM, HGF or NRG. We will work to provide additional data that strengthens the significance of this effect.

Reviewer #1 (Significance (Required)):

The concept of this work is interesting, however, molecular mechanisms underlying CAF-medicated ALK-TKI resistance remain poorly elucidated. Characterization of human primary fibroblasts (FB1, FB2) is not clearly described, and the most experiments lack proper control. Immunoblot in Fig 6 and 7 looks snap-shot and the reviewer has concerns about the reproducibility.

Author response:

In response to the comments, we will revise our manuscript to provide a more detailed characterization of the human primary fibroblasts to ensure transparency. To address the concern regarding controls, we will implement further controls in our experimental procedures. Regarding the concern about the reproducibility of the immunoblots, we appreciate the feedback, and we will provide additional data in the manuscript to ensure the reproducibility of our results.

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

In this review, the authors describe a possible mechanism of resistance in lung tumor cells that is induced by CAFs in response to ALK-specific inhibitors. The manuscript is well written and conclusions are in general well supported by experimental data, however additional experiments are needed to fully support the conclusions stated by the authors.

1. Brigatinib and lorlatinib are used to target ALK-driven lung tumor cells. In many of the experiments described heterotypic 3D co-cultures are used. Although both inhibitors act preferentially over the cancer cells, and no effect is expected in the CAFs, it would be desirable to confirm it.

Author response:

We thank the reviewer for this endorsement of our study, and we are pleased to learn that our conclusions are generally supported by the experimental data. Regarding the use of brigatinib and lorlatinib to target ALK-driven lung tumor cells in our experiments, we acknowledge the importance of confirming the specific action of these inhibitors. While these inhibitors act preferentially on the cancer cells, we agree that it is desirable to confirm their limited effect on CAFs. Therefore, we will address the reviewer’s suggestion by performing further cell viability analyses of TKI-treated fibroblast spheriods to specifically assess the impact of brigatinib and lorlatinib on CAFs.

The authors demonstrated initial proliferation advantage and apoptosis protection of H2228 and H3122 cells in response to conditioned media (CM) of three independent CAF clones. However, once they identify lipid enzymes altered and specific ligand-receptor interaction, then they focus only in FB2. This imply that the mechanism described by authors is relevant for that particular clone, but it does not validate a general resistance mechanism induced by CAFs. In order to claim that this is a more general mechanism, other CAF clones should be tested.

Author response:

We appreciate the reviewer’s comment regarding the focus on a specific CAF clone (FB2) in our study. This point is well taken, and we understand the importance of demonstrating the generalizability of the resistance mechanism induced by CAFs.

Since our results indicated consistent therapy response across all CAF clones tested (Figure 1), with the most pronounced effect observed with FB2-CAFs, we chose to focus our efforts on conducting sc-RNAseq experiments with FB2-CAFs and subsequently performed downstream validation experiments to corroborate our findings. This approach allowed us to prioritize the CAF clone with the most robust response while acknowledging the broader therapy response observed in all tested clones. Nevertheless, as requested by the reviewer, we will perform additional experiments using other independent CAF clones to assess whether the identified mechanism is broadly applicable.

Authors show that the identified ligands secreted by CAFs (HGF, NRG1β1, etc) are found in conditioned media from CAFs. It would be good to determine if the amount of these ligands somehow is dependent on the presence of tumor cells and/or ALK-TKi. Additionally, both HGF, NRG1β1, are able to partially restore the expression of the lipogenic enzymes identified, or AKT activation pathway, but they are not able to completely restore it. Since CAF-derived CM would have both factors, maybe combination of both ligands may induce stronger rescue of the expression of these proteins.

Author response:

To provide a comprehensive understanding, we will investigate whether the levels of identified CAF-derived ligands are influenced by tumor cells and/or ALK-TKI treatment by performing additional assays on CAF-supernatants. Furthermore, we will explore the potential synergy between HGF and NRG1β1 in rescuing the expression of lipogenic enzymes and the AKT signal transduction pathway on protein level.

Does PI3K/mTOR inhibitors revert the proliferation advantage of 3D heterotypic cultures? And expression of lipid biosynthesis genes?

Author response:

To address the impact of PI3K/mTOR inhibitors on the proliferation advantage of CAFs on ALK+ lung tumor spheroids and the expression of lipid metabolic genes, we will conduct treatment experiments using agents such as alpelisib (PI3Kα inhibitor), ipatasertib (panAKT inhibitor), or everolimus (mTORC1/2 inhibitor). Cell viability will be assessed using the 3D CellTiterGlo assay, and we will investigate changes in the expression of lipid biosynthesis genes to comprehensively evaluate the effects of these inhibitors on the resistance mechanism induced by CAFs.

Reviewer #2 (Significance (Required)):

This study underscores the multifaceted nature of resistance mechanisms in ALK-rearranged lung adenocarcinomas, highlighting the pivotal role of CAFs and lipid metabolic reprogramming. Lung adenocarcinoma remains a challenge in oncology, and while targeted therapy with tyrosine kinase inhibitors (TKIs) has shown promise in treating ALK-rearranged lung adenocarcinomas, the development of resistance to these therapies is nearly inevitable. This study delves into a critical aspect of this resistance by describing an important aspect of the intricate interplay between cancer-associated fibroblasts (CAFs) and tumor cells within the tumor microenvironment.

One of the primary findings of this research is the impact of CAFs on the therapeutic response of ALK-driven lung adenocarcinoma cells. While intrinsic mechanisms within cancer cells are well-studied drivers of resistance, this study underscores the emerging importance of stromal components, particularly CAFs, in shaping therapeutic vulnerabilities. The observation that CAFs promote therapy resistance by hampering apoptotic cell death and fueling cell proliferation highlights the complexity of tumor-stroma interactions.

The study utilizes three-dimensional (3D) spheroid co-culture models, providing a more physiologically relevant platform to investigate these interactions. This approach bridges the gap between conventional monolayer cultures and in vivo models, allowing for a deeper understanding of the role of the tumor microenvironment.

Perhaps one of the most notable findings is the identification of lipogenesis-related genes as major players in TKI-treated lung tumor spheroids. This finding not only sheds light on a previously underexplored facet of cancer biology but also suggests that lipid metabolism may be a central determinant of therapeutic susceptibility in this context. Although data provided here suggests that it might not be the only mechanisms taking place in the development of resistance to ALK inhibitors, it clearly shows that it plays an important role in it.

The study proposes a potential solution to overcome CAF-driven resistance by targeting vulnerabilities downstream of oncogenic signaling. The simultaneous targeting of ALK and SREBP-1, a key regulator of lipogenesis, emerges as a promising strategy to thwart the established lipid metabolic-supportive niche within TKI-resistant lung tumor spheroids.

Author response:

We thank the reviewer for this endorsement of our study and are gratified that the reviewer recognizes the critical implications of our research in the context of ALK-rearranged lung adenocarcinomas and their treatment resistance.

One of the stronger limitations of this study is that it rely on a limited number of cell lines or patient-derived models, which may not fully capture the heterogeneity of ALK-rearranged lung adenocarcinomas. Furthermore, for most of the validatory assays performed, only a CAF cell line is used, higly limiting the significance of their conclusions to a more general resistance mechanism. Furthermore, the study provides valuable insights into the involvement of lipogenesis-related genes and AKT signaling but do not delve deeply into the precise molecular mechanisms underlying these processes. Further mechanistic studies are needed to understand the exact interactions and signaling pathways involved. In conclusion, while this study provides valuable insights into the role of CAFs and lipid metabolism in ALK-TKI resistance, its limitations underscore the need for further research, including more comprehensive in vivo models and clinical studies, to confirm and expand upon these findings.

Author response:

We appreciate the reviewer’s thoughtful assessment of our study and acknowledge the limitations highlighted in your comment. The limited number of cell lines and patient-derived models used in our study is indeed a limitation, and we agree that this may not fully capture the heterogeneity of ALK-rearranged lung adenocarcinomas. However, the number of ALK+ lung adenocarcinoma cell lines is limited (3), as is the availability of patient-derived tissue material. To address this, we are actively working on expanding our research to include a more comprehensive range of models (e.g. primary ALK+ lung cancer cells, patient-derived organoids (PDOs)) for future studies.

We also acknowledge the importance of the limitations related to the use of a single CAF cell line in many of our validation assays. We are committed to broadening our experimental scope to involve multiple CAF cell lines to strengthen the significance of our conclusions.

Regarding the need for deeper mechanistic studies to understand the precise molecular interactions and signaling pathways, we agree that this is a crucial point. To this end, we are planning additional mechanistic studies to uncover the exact molecular mechanisms underlying the described resistance processes in future studies.

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

Summary: In this manuscript the authors use a spheroid co-culture model of human EML4-ALK non-small cell lung cancer (NSCLC) cell lines and fibroblasts to investigate the mechanism by which tumor-CAF crosstalk mediates non-genetic resistance to ALK inhibition. Spheroid culture of tumor cell lines with CAFs or CAF conditioned media was sufficient to reduce apoptosis and boost proliferation in the context of ALK inhibition. Using single-cell RNA-seq (scRNA-seq) of co-cultures treated with lorlatinib, the authors show that lipogenesis-associated genes are enriched in drug-treated tumor cells co-cultured with CAFs. Specifically, the authors propose that CAF-derived HGF and NRG1 derepress lorlatinib-induced changes in oncogenic Akt and mTOR signaling to boost expression of SREBP and FASN and restore lipid composition in NSCLC cancer cells.

Major comments:

The authors' conclusion that the effect of CAF CM on lorlatinib sensitivity is mediated by HGF and NRG is somewhat weak. Nrg1B1 was sufficient to rescue cell viability in the context of lorlatinib treatment (Figure 5B) only at a concentration significantly higher than that which was produced by fibroblast lines in culture (Figure 5A). Although the authors note that the real level of NRG1 could be higher than detected, this is speculative. Neither HGF nor NRG1 blocking antibodies appear to have rescued the elevated cell viability driven by CAF CM in the context of lorlatinib treatment (Figure 5C). These results, though statistically significant, do not appear biologically relevant. To strengthen their conclusions, the authors should consider ablating HGF or NRG1 in CAFs via shRNA or CRISPRi and then testing if CAF CM is no longer sufficient to rescue the viability of lorlatinib treated cancer spheroids.

Author response:

We refer the reviewer to our response to comment #1 of reviewer 1.

In addition to the western blots used to demonstrate and effect of CAF CM or HGF/NRG1 on Akt and mTOR signaling, the authors could strengthen their conclusions by testing the effect of Akt and mTOR inhibitors on the rescue effect of CAF CM.

Author response:

We refer the reviewer to our response to comment #6 of reviewer 2.

Minor comments:

1. In addition to the cell death and proliferation assays shown in Figure 1B-E, it would be helpful to show and quantify images of spheroid co-cultures treated +/- lorlatinib (as in Figure 1A, Supplemental Figure S9). Although the effects on percent cell death and proliferation are significant, images of spheroid size and morphology would make these results more convincing.

__Author response: __

We can certainly incorporate representative images in the revised manuscript. However, we'd like to clarify that comparing spheroid mono- and direct co-cultures can be challenging due to differences in initial cell seeding numbers, variations in the growth rates of fibroblasts and tumor cells, and subsequently, differences in spheroid sizes at the initiation of treatment. These factors can confound direct comparisons between the two culture conditions upon treatment.

In Figure 5B, the effect of CAF secreted factors on cell viability should be tested in comparison to CAF CM as a biological control. This would allow the reader to understand how the effect of each factor alone compares to the effect of CM.

__Author response: __

We will incorporate a comparison to CAF-CM as a biological control to provide a clearer understanding of the individual effects of CAF-secreted factors.

**Referees cross-commenting**

I am in agreement with all of the points made by Reviewer #1. I also suggested that the authors should use shRNA to inhibit HGF and NRG1 expression in CAFs, and am similarly concerned about both human and in vivo relevance of the authors' findings. The experiments suggested by Reviewer #1 to further characterize the fibroblast subtypes and to use non-CAF control cells are also reasonable.

Author response:

The reviewers alignment on the points raised is duly noted, and we understand the importance of addressing the concerns regarding the relevance of our findings. The use of shRNA to inhibit HGF and NRG1 expression in CAFs is a valuable suggestion, and we are actively considering this approach to enhance the specificity of our findings. Furthermore, we acknowledge the need for a deeper characterization of fibroblast subtypes and the inclusion of non-CAF control cells to strengthen the robustness of our research.

I am also in agreement with the critiques presented by Reviewer #2 and find them reasonable; they would strengthen the manuscripts and better support the authors' findings. The work is indeed limited by the models used here, and mechanistic findings would be better supported by further metabolic analysis such as Seahorse or assessment of lipid synthesis.

Author response:

We greatly appreciate your alignment with Reviewer #2's critiques and your recognition of their reasonableness. Expanding our research to include additional models and conducting further metabolic analyses are valuable suggestions that we are actively considering to bolster the mechanistic underpinnings of our work.

Reviewer #3 (Significance (Required)):

As a reviewer, I have expertise in fibroblast biology and the contributions of the tumor microenvironment to pancreatic tumor development. Although my research has not focused on lung cancer specifically, I also have experience in lipid metabolism, therapy resistance, and tumor heterogeneity. In this manuscript the authors use a co-culture system to show that soluble CAF factors drive tyrosine kinase inhibitor (TKI) resistance in vitro in Alk-fusion driven NSCLC in line with prior work (Reviewed by Wong et al. 2021, Domen et al. 2021, Li et al. 2022). Mechanistically, the authors propose that CAF-secreted HGF and NRG1 restore Akt and mTor signaling pathways suppressed by lorlatinib, thus rescuing SREBP expression and the phospholipidome in TKI-treated NSCLC cells. Prior work has specifically demonstrated the ability of CAFs to rescue the effect of lorlatinib on NSCLC cell lines with ALK fusions via HGF/Met signaling (Hu et al. 2021), and the general effect of CAF-secreted HGF on therapy resistance through Akt/mTor signaling has been well characterized (CITE). The regulation of SREBP and lipid metabolism by Akt/mTOR signaling in cancer and TKI resistance have been similarly described (CITE). Thus, the authors largely connect these well-known pathways, demonstrating that CAF co-culture restores lipid-associated transcriptional programs and lipidomic profile in lorlatinib-treated cells via HGF/NRG1 activation of Akt, mTOR, and SREBP. A few points presented in the manuscript that could represent potential scientific advances include scRNA-seq analysis of CAF/NSCLC co-cultures and the implication of CAFs in TKI-resistance through the modulation of lipid metabolism. However, the scientific and clinical significance of these findings are limited by the biological systems used and by their incremental contribution in context of the current literature.

The scRNA-seq analysis of NSCLC cells co-cultured with CAFs generated here could represent a potential advance and resource for future study; however, the application of this analysis to 2D cell lines in vitro may have limited utility as the heterogeneity of these long-culture lines is likely quite narrow (CITE OTHER scRNAseq in vivo or PDOs). The authors themselves did not leverage the scRNA-seq data for a deep analysis of cancer cell heterogeneity but rather uncovered lipid-associated transcriptional programs using bulk analysis across all tumor cells in their dataset. The significance of the authors' finding that CAF conditioned media (CM) mediates lorlatinib-sensitivity through the regulation of lipid metabolism is also somewhat limited by prior work directly implicating SREBP and phospholipid remodeling in TKI resistance (Xu et al. 2021, OTHERS). Although focusing on EGFR-mutant NSCLC, Xu et al. 2021 showed that SREBP upregulation and increased lipogenesis and decreased oxidative stress was associated with resistance to gefitinib and could be reversed by treatment with the SREBP inhibitor fatostatin in vivo. TKI-resistance is often driven by the activation of convergent signaling pathways (Akt, mTOR) in both in EGFR-mutant ALK-fusion NSCLC, so it is perhaps not particularly surprising that the authors find that lipid programs are similarly important in lorlatinib-resistance. The novelty in this manuscript is limited to the connection between CAFs and these critical lipid metabolism pathways, and the implication that SREBP inhibition similarly blocks non-genetic CAF-mediated TKI resistance. The significance of this finding might be greater if the authors explored whether fatostatin could improve therapy response to lorlatinib in vivo.

Author response:

We highly appreciate the reviewer’s detailed review and expertise in the fields of fibroblast biology, tumor microenvironment, lipid metabolism, and therapy resistance.

The reviewer’s perspective on the utility of scRNA-seq analysis in our study is justified. We acknowledge that applying this analysis to 2D cell lines in vitro may have limitations due to the narrow heterogeneity of long-culture lines. We therefore attempted to enhance the relevance of our findings by applying 3D cell culture models, which are known to resemble the in vivo situation more closely than conventional monolayer cultures (4, 5). Nevertheless, we agree that incorporation of additional models (e.g. patient-derived organoids) would better capture the heterogeneity of the tumor and its surrounding microenvironment. We concur that a deeper analysis would enhance our understanding of the interactions between CAFs and tumor cell (sub)populations.

The insights into the significance of our findings in the context of prior research on SREBP-dependent phospholipid remodeling in TKI resistance are well taken. We agree that the novelty of our study lies in the connection between CAFs and lipid metabolism pathways as a non-genetic CAF-mediated TKI resistance mechanism. However, it is also important to note that no prior studies have investigated stroma-driven lipid metabolic reprogramming in EML4-ALK-positive NSCLC. This unique aspect of our research adds to its originality and potential significance in advancing the understanding of ALK-positive NSCLC and therapy resistance.

We agree with the reviewer’s point that an in vivo study would be important in exploring whether fatostatin could improve therapy response to lorlatinib. However, due to technical and timing limitations, the establishment of corresponding mouse models is beyond the scope of our present study.

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

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

Reviewer #1

Minor issues:

"----stronger in in case of-------" needs to be improved to "----stronger in case of-------", line 128, page 5.

__Author response: __

This was changed accordingly.

Reviewer #2

1. Based on sc-RNA-seq data authors then explore molecular processes facilitating survival of ALK-driven lung cancer cells under the influence of CAFs and mention that "among the enriched biological processes and pathways related to metabolic activities, the most striking terms were linked to lipid metabolism" (lines 182-184). Attending to the graph depicted in Fig. 3A, that is not true, finding other processes more significant. In fact, linked to metabolism, glycolysis is more significant than lipid metabolism. This sentence should be changed accordingly and a different rationale should be done to focus on lipid metabolism.

__Author response: __

The phrasing was changed accordingly.

Reviewer #3

Major comments:

1. Although the authors note that the scRNA-seq data generated here may be an important resource in the field, it could also be explored in greater depth to further support the conclusions of this manuscript. As is, the scRNA-seq data is primarily analyzed at a bulk level to identify lipid-associated genes and gene sets as down-regulated by lorlatinib. In this case, it would be more useful and perhaps a better resource to conduct bulk RNA-seq in triplicate to generate a stronger dataset and generate a set of genes significantly regulated by lorlatinib and CAF co-culture or CAF CM. The scRNA-seq data could be leveraged to support the conclusions of the manuscript by plotting lipid-associated genes identified in Figure XB-C by U-map. This analysis would identify which clusters are enriched for lipid-associated genes and demonstrate whether these particular clusters are depleted by lorlatinib or rescued by CAF co-culture.

__Author response: __

We opted for scRNA-seq as it allowed us to simultaneously sequence co-cultivated tumor cells and fibroblasts, without the need for sorting experiments typically required for bulk RNA-sequencing experiments. With this we intended to avoid potential biases introduced by sorting procedures, which can be challenging, particularly in the case of identifying appropriate markers for fibroblasts.

In response to the reviewer’s suggestions we have now refined our analysis to depict lipid-associated genes in a cluster-dependent manner (Supplementary Figure S9). This analysis, however, did not showcase a cluster-specific enrichment of lipid-associated genes and a demonstrated a TKI-induced depletion of these genes across all tumor cell cluster.

The authors' conclusion that CAF co-culture restores the lipid profile of lorlatinib-treated tumor cells is somewhat weak due to the representation of lipidomic data. Although the Figure legends note that lipidomic analyses were conducted at n=3 replicates, the data as represented in Figure 8A-B do not allow the reader to assess variability across samples or the significance of the fold change differences in lipid species. Although it can be useful to view the data this way, the authors should also show variability across samples in some way via PCA plot or by including a heatmap of lipid abundance across all treatment groups and replicates. Especially as some differences appear subtle, it is also difficult to understand to what extent CAF CM rescues lorlatinib-induced effects on lipid species as values are shown as fold change relative to control for the independent groups. In this way, the reader cannot assess, for example, how lipid species abundance compares in lorlatinib-treated tumor cells +/- CAF CM. Again, a heatmap across treatment groups might be helpful in addition to an analysis for statistically significant differences in lipid abundance across treatment groups. The issues outlined here make it difficult to assess whether "addition of CAF-CM to H3122 lung tumor spheroids was able to partly abrogate this shift towards higher levels of poly-unsaturated lipid". As is, the statements describing the results in Figure 8A-B are vague and don't appear to totally align with the data. To my eyes, there is no apparent general trend in SFA or MUFA reduction in lorlatinib-treated cells as implied by the authors, though particular species may be down-regulated. The authors should also calculate saturation indices across lipid species to support their conclusion that lipid saturation is modulated by lorlatinib and rescued by CAF CM.

__Author response: __

Given the reviewer’s suggestions, we have made significant improvements to the presentation of our lipidomic data in the revised manuscript. We now provide a more comprehensive view of the data to allow for a better assessment of variability across samples and the significance of saturation index differences across lipid species. Specifically, we have included a PCA plot (Figure 8A) and a heatmap of lipid abundances across all treatment groups and replicates to address the issue of variability (Supplementary Figure S11). Furthermore, we have performed additional analyses to calculate saturation indices across lipid species (Supplementary Figure S12A), which support our conclusion that lipid saturation, i.e. de novo lipogenesis, is modulated by lorlatinib and rescued by CAF-CM. These additions provide a clearer visualization of the data and enhance the robustness of our findings.

Minor comments:

The ablation of specific cell clusters upon lorlatinib treatment in Figure 2 is compelling and visually striking. To make it easier for the reader to interpret this data, it might be useful to denote the general functional annotations of each cluster in the legend (for example, "cluster 3: proliferative"). This would allow the reader to visualize which populations are preferentially depleted by the inhibitor and rescued by CAF co-culture. Further, some quantification showing the number of cells in each cluster by treatment would group (or fold-reduction per cluster upon inhibitor treatment) would more clearly show how each cluster is impacted by the inhibitor and CAF co-culture.

__Author response: __

To facilitate a clearer understanding of which populations are preferentially affected by the ALK-inhibitor and rescued by CAF co-culture, we provided the cluster-specific annotations in the legend of Figure 2.

Furthermore, we included quantifications showing the number of cells in each cluster by culture condition and treatment group (Supplementary Table S3), to provide a more comprehensive view of how each cluster is impacted by the inhibitor and CAF co-culture.

In Supplemental Figure S3A please specify which gate is being used to quantify the percentage of dead cells shown in subsequent plots. It would also be useful to show the gating strategy used to separate labelled tumor cells and CAFs in heterotypic co-cultures by FACS so it is clear that CAF cells are not included in the cell death/proliferation analysis.

__Author response: __

Gates for quantification of dead cells are now specified, while the gating strategy used for analyzing cell death rates of separated tumor cells is given as requested in Supplementary Figure S3A. This gating strategy was likewise used to separate labelled tumor cells from CAFs to analyze cell cycle distributions.

In Supplemental Figure S1B and C, please briefly clarify in the legend how fibroblast lines were cultured for collection of RNA and protein. It would be useful to know if the cells were assessed in spheroid culture and thus representative of their cell state when used for the following heterotypic co-culture experiments.

__Author response: __

Culture conditions were added in the figure legend as requested. Prior to generation of heterotypic tumor spheroids, fibroblasts were cultured as monolayers. Nevertheless, we also verified that the activation status is maintained following TGF-β1 removal and subsequent cultivation as homotypic fibroblast spheroid via WB analysis. We added the results as shown in Supplementary Figure S1D.

In Figure 8C, the authors should plot all individual values in the bar graph as done in all other panels.

__Author response: __

This was changed accordingly

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. *

Reviewer #1

Major critiques:

The concept of this work is largely based on findings in vitro culture. The authors should perform animal experiments to convince their findings in vivo. CAFs and tumor cells would be implanted into recipient mice to determine whether AKT signaling, de novo lipogenesis and ALK-TKI resistance are increased in tumor cells by the presence of CAFs.

__Author response: __

We agree with the reviewer’s point that an in vivo study would be important in interrogating the full impact of CAFs on therapy response, AKT signaling, and de novo lipogenesis of ALK-driven lung adenocarcinoma cells. However, due to technical and timing limitations, establishing and performing co-injection and treatment experiments of corresponding mouse models is beyond the scope of our present study.

The author described that human primary fibroblasts (FB1, FB2) were derived from NSCLC adenocarcinoma patients---. Have FB1 and FB2 been isolated from tumor tissues or no-tumor tissues? If these fibroblasts were isolated from tumor tissues as CAFs, why the authors added TGF-b onto the cells? The TGF-b treatment generates myofibroblastic CAFs, which is one of CAF subtypes, but fails to have inflammatory CAFs, which is another CAF subtypes.

__Author response: __

The fibroblasts FB1 and FB2 were indeed isolated from tumor tissue obtained from lung adenocarcinoma patients. In our study, the addition of TGF-β1 was employed as a strategy to maintain the CAF phenotype. It's important to note that CAFs exhibit considerable plasticity and can potentially lose their distinctive CAF characteristics during in vitro cultivation (6). The introduction of TGF-β1 was aimed at mimicking the tumor microenvironment and assisting in the preservation of the CAF phenotype, which was partially reflected in the increased expression of CAF markers such as αSMA and FAP (Supplementary Figure S1B and C).

We acknowledge the existence of various CAF subtypes, including myofibroblastic and inflammatory CAFs, which can be induced by different stimuli. While TGF-β1 treatment tends to push fibroblasts more toward a myofibroblastic phenotype, other factors like IL-1 can induce an inflammatory phenotype (7). In our study, we chose to focus on the myofibroblastic CAF subtype. This decision was based on the prevalence of myofibroblastic CAFs in lung tumors and their established roles in tumor progression, poor prognosis across different cancer types, and resistance to immunotherapy in non-small cell lung cancer (NSCLC) (8, 9).

Reviewer #2

H2228 and H3122 cells are used indistinctively through the paper as ALK-driven lung tumor cells and, although in the discussion some reference is made regarding the worst outcomes observed for v3-driven ALK+ H2228 cells, results are considered similar for both cell lines, including sc-RNA-seq data. During analysis of sc-RNA-seq data numbers of specific genes identified at the different analysis are different, similar to the clusters identified (0-6). In order to determine the degree of overlap in the identified genes on the analysis and within clusters, it would be convenient to show tables with identified genes for each of the cell lines, together with the cluster classification of those genes.

Author response:

Regarding the comparison of v1- vs. v3-driven ALK+ tumors, we would like to clarify that the primary focus of our study is on the interactions CAFs and ALK-driven lung tumor cells, particularly in the context of therapy resistance. While the different ALK fusion variants are certainly of interest, our intention is not to delve into the comparative analysis of these variants in this paper. Instead, we aim to emphasize the broader impact of CAFs on ALK-driven lung tumors.

The comparison of v1- vs. v3-driven tumors, as well as a detailed analysis of the differences between H2228 and H3122 cells, goes beyond the main focus of this paper. Incorporating a comparative analysis of specific genes for each cell line and their cluster classification would require a significantly expanded scope and could lead to a more complex and detailed study.

In order to fully validate the effect of CAF/CAF CM in lipid biosynthesis in tumor cells, seahorse analysis would be highly beneficial, providing simultaneous measurement of multiple metabolic parameters, including glycolysis, oxidative phosphorylation, and fatty acid oxidation in homo (with and without CAF's CM or secreted ligands) and heterotypic conditions. Furthermore, it should be combined with specific substrates and inhibitors (i.e. glucose to measure acetyl-CoA production, labelled fatty acids, etc), to dissect various aspects of lipid biosynthesis and lipid metabolism and assess de novo lipogenesis, fatty acid uptake, or triglyceride.

Author response:

This point is well taken and we acknowledge the potential value of such comprehensive metabolic assessments. However, we would like to clarify that the Seahorse XF Analyzer can primarily measure oxygen consumption rate (OCR) and extracellular acidification rate (ECAR), in response to different substrates to interrogate key metabolic functions such as mitochondrial respiration and glycolysis. At least to our knowledge, the Seahorse analyzer does not specifically measure de novo lipogenesis and fatty acid uptake. Therefore, incorporating these assays in the revised manuscript may not directly address the central question of CAF-driven enhanced lipid biosynthesis.

Nonetheless, we do agree with the reviewer that a more in-depth investigation of various metabolic alterations could be of interest in future studies. Given the GSEA data derived from our scRNA-seq analysis, which hints at alterations in glycolysis (Figure 3A), exploring these aspects of metabolic alterations in the context of CAF-mediated resistance effects could indeed provide valuable insights in the broader mechanisms underlying ALK-TKI resistance.

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.

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