Overall Assessment (4/5)

Summary: The authors provide a software tool NeuroVar that helps visualizing genetic variations and gene expression profiles of biomarkers in different neurological diseases.

Technical Release criteria

Is the language of sufficient quality? * The language quality of the document is of sufficient quality. I did not notice any major issues.

Is there a clear statement of need explaining what problems the software is designed to solve and who the target audience is? * Yes, authors provide a statement of need. Authors mention that there is the need for a specialized software tool to identify genes from transcriptomic data and genetic variations such as SNPs, specifically for neurological diseases. Perhaps authors could expand on how they chose the diseases. E.g. stroke is not listed among the neurological diseases. Perhaps authors could expand a bit on the diseases they chose in the introduction.

Is the source code available, and has an appropriate Open Source Initiative license been assigned to the code? * Yes the source code is available in github under the following link: https://github.com/omicscodeathon/neurovar. Additionally authors deposited the source code and additional supplementary data in a permanent depository with zenodo under the following DOI: https://zenodo.org/records/13375493. They also provided test data https://zenodo.org/records/13375591. I was able to download and access the complete set of data

As Open Source Software are there guidelines on how to contribute, report issues or seek support on the code? * I did not find any way to contribute, report issues or seek support. I would recommend that the authors add this information to the Github README file.

Is the code executable? * Yes, I could execute the code using Rstudio 4.3.3

Is the documentation provided clear and user friendly? * The documentation is provided and is user friendly. I was able to install, test and run the tool using RStudio. Authors may consider to offer also a simple website link for the RshinyTools if possible. This may enable the access also for scientists that are not familiar with R.Especially, it is great that authors provided a demonstration video. I was able to reproduce the steps. However, I would recommend to add more information into the Youtube video. E.g. reference to the preprint/ paper and Github link would be helpful to connect the data. Perhaps authors could also expand a bit on the possibilities to export data from their software. And provide different formats e.g., PDF / PNG /JPEG. I think this is important for many researchers to export their outputs e.g., from the heatmaps.

Is installation/deployment sufficiently outlined in the paper and documentation, and does it proceed as outlined? * I could follow the installation process, but perhaps authors could add few more details how to download from Github in more detail. As some scientist may have trouble with it. Also perhaps an installation video (additionally to the video demonstration of the Neurovar Shiny App might be helpful.·

Is there a clearly-stated list of dependencies, and is the core functionality of the software documented to a satisfactory level? * Yes, dependencies are listed and are installed automatically. It worked for me with Rstudio version 4.3.3. In the manuscript and in the

Have any claims of performance been sufficiently tested and compared to other commonly-used packages? * not applicable

Are there (ideally real world) examples demonstrating use of the software? * Yes, authors use the example of Epilepsy, focal epilepsy and the gene of interest DEPDC5. I replicated their search and got the same results. However, I find that the label in Figure 1 in the gene’s transcript could be a bit more clear. E.g. it is not clear to me what transcript start and end refers to. It might also be more helpful if authors provide an example dataset for the Expression data that is loaded in the software by default.Furthermore authors use a case study results using RNAseq in ALS patients with mutations in FUS, TARDBP, SOD1, VCP genes.

Is test data available, either included with the submission or openly available via cited third party sources (e.g. accession numbers, data DOIs, etc.)? * Yes the authors provide test data with dois: https://zenodo.org/records/13375591.

Is automated testing used or are there manual steps described so that the functionality of the software can be verified? * Automated testing is not used as far as I can access it.

Overall Recommendation: * Accept with revisions

Reviewer Information: Ruslan Rust is an assistant professor in neuroscience and physiology at University of Southern California working on stem cell therapies on stroke. His lab is particularly interested in working with genomic data and the development of new biomarkers for stroke, AD and other neurological diseases.

Dr. Ruslan Rust's profile on ResearchHub: https://www.researchhub.com/author/4945925

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐☆☆☆☆): The authors present an overview of uncertainty quantification for semantic segmentation. After identifying the limitations of PAvPU, propose their metric called “PAvPU Surplus”. They apply these metrics to tasks of segmenting urban settings to examine the benefits of this new metric. I think this manuscript needs to be extensively revised as much of it is disorganized or outdated. Despite the focus of this work being on uncertainty quantification of semantic segmentation, they miss much of the current approaches and literature that are key to understanding this field. The experiments included in this work and their description are extremely limited, poorly explained, and inadequately interpreted.

Impact (⭐⭐☆☆☆): The authors highlight the importance of image segmentation in several fields, including medicine and robotics. Although segmentation’s model accuracy is important, quantifying model uncertainty is equally important for properly expressing model performance under various conditions. - Class imbalances are noted to be an important feature to consider. Small regions of an image may be critically important, e.g., a stop sign for autonomous driving, and the uncertainty should be weighed accordingly. - They also emphasize the importance of accurate uncertainty assessment at segmentation class boundaries. Particularly in medical image segmentation, uncertainty quantification here is very important as many biomarkers rely on quantifying the sizes of various regions, e.g., aneurysm diameter. - There is a need for uncertainty metrics that are well-suited for expressing the pitfalls of a given segmentation. This work makes the case that current metrics are overly simplistic and fail to communicate the quality of output segmentations properly. In particular, they focus on Patch Accuracy versus Patch Uncertainty (PAvPU). The authors cite the many shortcomings of PAvPU, but I do not see any cited literature which supports these claims so I don’t know how widespread these concerns actually are. - In Section 4, a case is made for quantifying local uncertainty metrics since error likely changes over the image. The authors aim to introduce a supplementary metric to alleviate some of the shortcomings of PAvPU. While reviewing Section 2, I have taken note of many issues that should be addressed for the impact of this work to be fully realized. - The overview of uncertainty in ML is insufficient despite this being the central focus of the manuscript. The authors identify the aleatoric and epistemic components of uncertainty but provide little explanation of what influences these sources. - This section generally lacks many critical citations, including those for entropy. The authors only cite the original work by Shannon, neglecting to cite many of the more recent works that directly apply entropy quantification to image segmentation tasks. Strengths: - I appreciate that the authors are focusing on segmentation uncertainty. Understanding this space is critical for the advancement of these types of models. Weaknesses: - This work, at times, misses key citations. For example, in the introduction, the many limitations of PAvPU are outlined, but I don’t see any work cited that supports these claims. As a result, the reader doesn’t know how widespread these concerns actually are. - A review of the citations shows that most are from before 2020. Deep learning is a rapidly developing field, and only citing sources from pre-2020 demonstrates that the authors may not be up-to-date on current literature. - The information in this manuscript is not well-structured, and related information appears to be distributed across the entire manuscript. I recommend the authors condense many of these sections to increase readability.

Methods (⭐☆☆☆☆): The authors provide some information regarding how they explore the performance of the mIoU, PAvPU, and PAvPU Surplus metrics. In general, this section is extremely lacking and I recommend the authors greatly expand on the information provided. Below, I summarize the information they do provide: - In Section 9, the authors outline their experimental procedure for addressing standing questions for PAvPU, including 1) its dependence on accuracy and 2) the effects of class imbalance. They also explore the effects of window size and their impact on uncertainty estimates when crossing class boundaries. - The authors explore various uncertainty metrics on the Cityscapes Dataset which provides depictions of various urban scenes with their associated segmentations. The authors note that they perform data augmentation to expand the size of their training data. - The authors note that they include dropout at a rate of 0.5 - In Section 4, the authors introduce their metric called PAvPU Surplus, which addresses the limitations of PAvPU. In short, the authors define this metric to isolate its dependency on local uncertainty rather than accuracy. - The authors highlight the value of PAvPU in Section 6 by identifying a case where PAvPU presents invalid results.

Results (⭐⭐☆☆☆): Section 10 contains the results that compare the three metrics across different models. - The authors never provided actual background of these models in their methods section. This makes it difficult to interpret these results when comparing the performance of various metrics on “big” and “small” models. - I found it extremely difficult to interpret what the authors express regarding Tables 2 and 3. I feel that a different way of presenting the data may help this, such as some sort of line plot. Based on these tables, the authors claim that PAvPU Surplus is robust across different classes and window sizes. - The authors claim that PAvPU Suprlus outperforms PAvPU when assessing the uncertainty at boundaries. The authors provide confusion matrices to express the value of PAvPU Surplus further. - Despite calling Fig. 4 and 5 confusion matrices, they are simply called “heatmaps” in the figures themselves. This makes it extremely confusing for the readers. A core point of this work is to provide local estimates of uncertainty. Why don’t the authors demonstrate this by creating a figure showing this uncertainty in the image?

Discussion (⭐☆☆☆☆): The authors conclude this work by summarizing the applications of PAvPU, emphasizing areas where it is limited. Their metric, PAvPU Surplus, is intended to fill this gap. They point out that in their investigations they discovered that no metric alone can quantify uncertainty, rather a combination should be considered. Many of the discussion points are also scattered throughout the previous sections. This makes it very difficult for the reader to understand the key points of the work. Furthermore, the discussion section that they do provide is extremely short compared to the length of the rest of the manuscript.

Reviewer Information: Sean has an undergraduate degree in Mechanical Engineering and a PhD in Biomedical Engineering. His PhD dissertation focused on developing models for 4D flow MRI according to fluid dynamics and imaging physics. During his PhD, he authored papers that explored 4D flow MRI error sources and segmentation, published in IEEE and MRM.

Dr. Sean Rothenberger on ResearchHub: https://www.researchhub.com/author/956799

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐☆☆):

Impact (⭐⭐⭐☆☆): This manuscript presents an interesting study on the association between plant-based diet indices (PDIs) and premature mortality risk among chronic kidney disease (CKD) patients, selected from the UK Biobank population. Interest in plant-based eating (for health and/or environmental reasons) is growing and many dietary guidelines targeting general populations focus on shifting to more plant-based food consumption. Although PDIs have been studied extensively in relation to various health outcomes recently, this has – to my knowledge - not been done in a CKD patient population, and there is a need for more targeted dietary recommendations (beyond e.g. protein and salt) for this growing patient group. The rationale for focusing specifically on plant-based eating in CKD patients, and what is specific about the current study and findings for this patient group could use some more elaboration.

Suggestions to enhance impact: - Consider providing more background information on the rationale for studying plant-based eating specifically in CKD patients, also in light of current dietary guidelines for CKD patients. - Elaborate how effects of plant-based eating may relate to effects of protein intake (from animal and plant food sources), giving the importance of managing protein intake and current protein recommendations for this patient group. (please see some thoughts on adjustment for protein intake below). - Discuss how the findings compare to similar studies in non-CKD populations to highlight any specific dietary recommendations for this patient group.

Methods (⭐⭐⭐⭐☆): The study design is relatively straightforward and appropriate for addressing the research question. Strengths include the long follow-up, the use of repeated 24-hour dietary recalls (up to 5) to assess diet, and adjustment for a range of potential confounders.

Some suggestions for improvement or clarification: - Consider including the overall PDI in addition to the healthful and unhealthful PDIs for completeness and comparison with other studies. Especially because one might discuss that studying the hPDI and uPDI are very similar to studying overall healthy versus unhealthy dietary patterns and less specific to plant versus animal-based eating. - Participants with missing covariate data were excluded (line 126), but this could lead to bias. I would suggest using e.g. multiple imputation to minimize bias and preserve statistical power. - Adjustment for protein intake may be an overadjustment, as it is an inherent part of dietary patterns and - especially when studying CKD patients -, potentially an important factor when comparing plant-based eating levels in relation to health. I would not include it as a confounder, or maybe in a separate model. Maybe also consider splitting total protein by animal and plant-sourced protein. - Although results for food groups are presented separately, there are some inconsistencies with the results for the PDI, I would consider adding a 'leave one out' analysis for the PDIs to verify that the results are not driven by a single food group. - Related to this: I would interpret the analyses for individual food groups as additional/supporting evidence, to better understand and interpret the findings for the PDIs but not as main analyses on their own. The food group analyses would otherwise need consideration for multiple testing. Also, for analyses on specific food groups, one may consider different models, taking into account e.g. potential non-linearity, different confounder adjustments per food group, etc.

Some additional minor suggestions for clarification: - How many participants completed all 5 dietary recalls? And/or: what is the median number of recalls completed? - Consider modeling BMI as a continuous variable rather than in categories to preserve information. - Clarify the rationale for the age and protein intake cutoffs used in stratified analyses. Are these median values of the study population?

Results (⭐⭐⭐☆☆): The results are presented clearly in tables, showing associations between PDIs and specific food groups with mortality risk.

Some suggestions: - The quartile distribution for food groups seems uneven (Table 3). Is this because of zero consumers in the lowest quartile? This wasn’t clear to me from the description in the methods sections, in which zero consumers were added in a separate category and the remaining group was split in quartiles (i.e. 5 categories in total instead of 4?). - Although p-for-trends are presented, I would (also) present the effect estimates and 95%CIs for the PDIs as continuous variables (e.g. per SD of per 10 units) in addition to quartiles. This retains more information and provides more statistical power. If potential non-linearity is a reason for focusing on quartiles one could test e.g. splines. - Minor: In Table 1 I would suggest presenting energy intake in kJ/day in whole numbers, not with decimals, as intake was likely not estimated to that level of precision.

Discussion(⭐⭐⭐☆☆): The discussion is well-written, discusses the findings in comparison with previous studies, potential underlying mechanisms, and various strengths and limitations.

Some suggestions for improvement: - In the section on potential mechanisms, the authors focus on key nutrients in plant versus animal-based diets, with a lot of focus on fiber intake and some on flavonoids. These are relevant in the context of plant-based eating, but for this study in CKD patients I would also discuss the role of plant- and animal based protein (which also differs a lot by level of plant-based eating), and maybe sodium. Also, I would analyze associations without adjusting for protein, given its integral part in plant versus animal based dietary patterns. - In general, I would focus in the discussion more on this specific CKD population. There have been many studies on PDIs in general populations, but the authors chose to specifically select only CKD patients for their research. I would elaborate more on e.g. specific mechanisms underlying effects of PDIs on mortality in this group and what the findings mean for CKD dietary recommendations, also considering that associations between PDIs and mortality were only found for CKD patients in early stages of the disease. - As a more general discussion point in research on PDIs: it may be interesting to address the question of whether focusing on healthful and unhealthful PDIs is still evaluating plant-based eating per se, or if it's more about comparing healthier and unhealthier dietary patterns in general. - Related to this: consider discussing the null estimates for most animal food groups (except meat and animal fat) and how this relates to the overall findings for PDIs.

Reviewer Information Dr. Trudy Voortman has a PhD in nutritional epidemiology, 15+ years of research experience, focusing on the role of nutrition and lifestyle in population health across the lifecourse.

Dr. Trudy Voortman on ResearchHub: https://www.researchhub.com/user/1791011/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐☆☆): This manuscript presents a post-hoc analysis of a dietary intervention examining the short and long-term effects of a Mediterranean diet (MedDiet) versus a control diet on gestational diabetes mellitus (GDM) and metabolic syndrome (MetSyn) in overweight pregnant women. The study's focus on longer-term outcomes (3 years postpartum) is relevant and important to help understand the potential long-term effects of dietary interventions. Overall, this is a valuable contribution to the field and generally well-written. I have some suggestions for the methods and for the presentation and interpretation of the results to improve impact and clarity.

Impact (⭐⭐⭐⭐☆): The topic of this study is important, as GDM is highly prevalent and associated with not only immediate pregnancy complications but also long-term adverse health consequences for women and their offspring. Evaluating the role of diet as a modifiable risk factor could inform recommendations for prevention. A strength is also the focus on longer-term outcomes, with results for 3 years postpartum suggesting potential long-term benefits of the MedDiet intervention: not only on measures of body weight and glucose management, but also on dietary habits, as women who were part of the intervention group during pregnancy, still seemed to have a better adherence to the MedDiet at follow-up.

To enhance impact: it would be informative to read more about how this post-hoc analysis builds upon and differs from their previously reported findings on GDM reduction. Also, I would add some information on the rationale for choosing the Mediterranean diet as opposed to other healthy dietary patterns, particularly in the context of previous research focusing on carbohydrate quality and quantity.

Methods (⭐⭐⭐☆☆): - The study is a post-hoc analysis combining three studies among pregnant women. The three studies and their differences need some more clarification. Maybe they can be summarized in a figure or table? Also, it seems that only studies 1 and 3 were randomized and controlled, while study 2 was not. I would recommend to do a sensitivity analysis including only studies 1 and 3. - The specific dietary recommendations provided to both the intervention and control groups need more detail. It was not completely clear to me whether the Mediterranean diet group received dietary recommendations beyond increasing olive oil and nut consumption. Similarly, it's not clear if the control group received any standard dietary recommendations, beyond limiting olive oil and nut intake. - Information on the number of women who did not participate in the follow-up measurements or who were excluded by the researchers (e.g. with a BMI<25) should be provided for each study and study group, along with reasons if known. A flow diagram would be helpful to show how many women were included in the original studies, how many participated in the follow-up, and reasons for loss to follow-up or exclusion from the current analysis. - Remove p-values for differences in baseline values between groups in Table 1, as these can be misleading and are not useful after randomization. Although this is still often included in studies, this practice has been discouraged, also in e.g. the CONSORT statement (e.g. doi: 10.1016/j.jclinepi.2010.03.004 or doi: 10.1016/S0140-6736(00)02039-0). - Is any data on compliance available? - Minor: Write out abbreviations such as IG and CG in full the first time they appear in the main text, not just in the abstract. - Minor: In section 2.4 (analysis), I would suggest to remove the word 'adverse' when describing the outcomes assessed, as all tests were indicated to be 2-sided (so not testing only adverse effects but in either direction).

Results (⭐⭐⭐☆☆): - I would consider removing the comparison of the GDM versus the GTN group from Table 4 and the results section. This additional set of analyses does not provide evidence on the intervention and, in my opinion, does not add substantially to the main analyses and may be confusing (especially when presented in the same table as intervention results). - Minor: Please check that all variables in Table 1 include units (e.g., insulin, TG).

Discussion(☆☆☆☆☆): <br /> - In the conclusions, I would avoid emphasizing a lower risk of MetSyn at 3 years postpartum. Instead, focus on the individual components that showed significant differences (glucose regulation, BMI/Waist circumference), as the effect on the composite score for MetSyn seems to be driven by these components only. - Although loss to follow-up is discussed in the context of sample size and statistical power, I would like to also see information and discussion on whether this loss to follow-up may be selective, how this might differ across groups. - Minor: suggestion to rephrase the last sentence of the discussion regarding the use of validated questionnaires. While questionnaires are useful and acceptable, they still have limitations such as recall bias and should not be presented as overcoming all limitations or providing a fully objective quantification. - I think the observed long-term effects on dietary behavior are interesting and deserve more attention in for example the discussion section.

Reviewer Information Dr. Trudy Voortman has a PhD in nutritional epidemiology, 15+ years of research experience, focusing on the role of nutrition and lifestyle in population health across the lifecourse.

Dr. Trudy Voortman on ResearchHub: https://www.researchhub.com/user/1791011/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐☆☆☆): This manuscript addresses a relevant topic in cardiovascular health, exploring the relationship between Metabolic Syndrome (MetS) components and risk of Heart Failure (HF). The focus on a relatively understudied population is a strength. However, there are significant methodological limitations and I have several concerns about the interpretation and presentation of the findings. - The case-control design with data collected at one time point severely limits causal inference and results in high risks for reverse causation. The small sample size results in limited power. - The rationale and specific research gap addressed by this study are not clear, and there are inconsistencies between the stated aims and the actual analyses performed and findings discussed. - The reporting of the study population, data collection methods, and statistical analyses is not sufficiently clear or complete for adequate interpretation and replication of the study. Also, I’m not a native English speaker, but I would recommend textual editing as some sentences seem a bit awkward and difficult to understand (e.g. ‘diabetes or insulin resistance had the higher risk of developing heart failure” – should this be ‘patients with diabetes or IR had a higher odds of HF as compared to…. ’?).

Additional minor comments: - The introduction is rather long and could be shortened and more focused on the specific research aims. - The first line of the abstract, "Metabolic dysfunction of metabolic syndromes," is unclear to me. - The statement that cardiovascular disease is the leading cause of death in the US (first line) is true, but I would suggest expanding this to that this is true globally.- Please check consistency in terminology and use of abbreviations (e.g., insulin resistance vs. IR) throughout the manuscript.

Impact (⭐⭐☆☆☆): While the study addresses a relevant topic, giving the high and rising prevalence of risk factors included in the metabolic syndrome and HF, its potential impact is limited by several factors, as outlined above.

The specific research gap addressed and the aims of the study need further clarification throughout the manuscript. The introduction suggests that many studies have already examined MetS as a whole in relation to HF, while also implying that individual components have been less studied. This seems contradictory to the existing literature, which includes numerous studies on individual risk factors (e.g., blood pressure, cholesterol levels, obesity) and their relationship to HF. Subsequently, the authors highlight that the study of different combinations of MetS components are not well studied, but in their analyses they do not study all combinations available or test e.g. interactions. In the discussion, the authors again only focus on single MetS components. This all seems rather contradictory.

With the available data, maybe the authors could maybe include: interaction testing (additive or multiplicative) across individual MetSyn components on HF risk and/or focus on whether single components are independently associated or may mediate each other. This may help guide prevention strategies among different subgroups of patients with particular metabolic risk factors and thereby increase potential impact.

Methods (⭐⭐☆☆☆): <br /> 1. Study population: More information is needed about the source population. Are there specific patient groups or professions represented in the Marshall Health Network? Is this a population-based or patient-based sample? 2. Data collection: More information is required on how data were collected, both for HF definitions and for exposures and covariates. The timing and methods of data collection are crucial for understanding potential biases. 3. Study design: in line with this; based on the current text I understand that data are all collected at a single time point. This cross-sectional nature o the study needs to be explicitly stated and integrated in the interpretation and discussion of findings. 4. MetSyn definition: the authors should state which definition they used for MetS and provide a rationale for their choice. 5. Analyses: The description of how MetS components were included in the models needs clarification. What does "simultaneously" mean in this context? Are all five factors included in one model, or are all different combinations tested? 6. Analyses: consider including analyses of interaction effects between different MetS components on HF (as hinted to by the authors in the introduction). 7. Minor: The statement about "combinations of previously identified significant components" (lines 168-169) is unclear to me.

Results (⭐⭐☆☆☆): 1. Please provide footnotes for each table indicating the models used, confounders adjusted for, abbreviations used, etc. 2. Table 2a: The analysis for obesity is based on a very small sample size (only 10 HF cases and 5 controls are not overweight or obese). I would not do this analyses with such a small sample. Based on the text in the methods (please provide info in the footnotes as well), there are also several confounders included in these model, which makes the degrees of freedom for this analysis very low. 3. Related to this: to enhance statistical power and retain more information from this limited sample size: consider analyzing all components also as continuous variables in addition to meeting the MetSyn cutoff yes/no. E.g. include blood pressure and not only hypertension yes/no. Especially because cutoffs for MetS components are somewhat arbitrary and vary across definitions and study populations. 4. Table 2b: The rationale for selecting only these specific combinations of MetSyn components is not clear. Why were not all possible combinations tested? 5. Table 3, major: In my opinion, the results presenting odds ratios (ORs) for the number of MetSyn components do not show a clear dose-response trend. While there is a large OR for having any single MetSyn component compared to none, the ORs for having at least 2, 3, or 4 components are generally similar with almost completely overlapping confidence intervals. This observation does not support the interpretation provided in lines 216-219 of the manuscript or in lines 230-231 of the conclusion.

Discussion(⭐⭐⭐☆☆): 1. The cross-sectional nature of the study, the risk for reverse causation, residual confounding, and the limited sample size should be discussed as major limitations. 2. Related to this: please be careful with using causal language throughout the manuscript. 3. In general, the discussion is not in line with the aims, the discussion should focus more on combinations and interactions of MetS components, rather than primarily on individual factors. 4. The findings in line with the obesity paradox (seemingly protective effect of obesity) in this study are very likely largely due to reverse causation. This should be explicitly discussed. 5. Given the limitations of this observational study, the authors should be very cautious in their interpretation and in drawing clinical implications. Any conclusions or suggestions for clinical practice should be framed as hypotheses for future research rather than definitive findings or recommendations.

Reviewer Information Dr. Trudy Voortman has a PhD in nutritional epidemiology, 15+ years of research experience, focusing on the role of nutrition and lifestyle in population health across the lifecourse.

Dr. Trudy Voortman on ResearchHub: https://www.researchhub.com/user/1791011/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐☆☆): The study presents a well-written manuscript with a helpful introduction, clear methodology, and a discussion that generally makes sense. I praise the availability of the data for public access for its contribution to open science. Further, I see the conclusions regarding the alteration of epigenetic modifiers and their downstream effects on other oncogenes as clear and logical. However, there are some critical points to consider: i) Although the reader could assume that the authors write about metastatic melanoma, it is not clear what subtype is the focus of the study (Skin cutaneous melanoma (SKCM) includes low and high-grade). This would need to be further specified in the manuscript. ii) The translatability of the findings is noted, but given the effective treatment of metastatic melanoma with immunotherapy, this aspect is viewed with some skepticism and should at least be further analyzed in the discussion. ii) The introduction is too lengthy and should be more concise, with less focus on information on the results form the paper itself. iii) In whole, I see the manuscript as somewhat inflated and should be carefully reviewed for redundancies, including to reduce the amount of figures and text information.

Impact (⭐⭐⭐☆☆): The study highlights the potential of lurbinectedin, a marine-derived compound, and its derivatives ecubectedin and PM54, as promising treatments for skin cutaneous melanoma (SKCM). Despite being rare, metastatic SKCM accounts for the majority of skin cancer-related deaths. Typically, treatment options for such cancers are limited, remaining largely palliative due to their resistance to therapy. The study is particularly intriguing due to its proposed mechanism, which involves the suppression of oncogenic super-enhancer-mediated gene expression. This disruption of cancer-promoting gene expression suggests a broad impact on the disease, even though the compounds may act somewhat nonspecifically by binding many different promoters. By targeting multiple oncogenic pathways simultaneously, these compounds offer a potentially powerful approach to treating metastatic melanoma.While the research question may not be groundbreaking, the clinical implications are substantial. Jazz Pharmaceuticals' recent approval of Lurbinectedin (ZEPZELCA) for NSCLC underscores the significance of these findings for patients with other metastatic malignancies, including melanoma. However, the rationale behind why two additional compounds were synthesized remains unclear.

Methods (⭐⭐⭐⭐☆): No further questions arise that would require additional experiments or methodologies beyond those already employed. The methods section is well structured and concise. However, please add a table containing primer information for qRT-PCR.

Results (⭐⭐⭐☆☆): The results presented in the manuscript are compelling, but I have the following points the authors should address: i) abundance of figures, supplementary figures, and tables makes the manuscript hard to navigate. I strongly recommend condensing all figures to improve readability. ii) The readers might have a hard time understanding the rationale behind synthesizing new compounds that are similar to the original. The authors should clarify the benefits of using these newly synthesized compounds compared to the original compound. iii) More specifically, how do the new compounds differ from the original, and what advantages do they offer in terms of pharmacodynamics/pharmacokinetics (PD/PK)? It appears that the two new compounds have higher IC50 values than Lurbinectedin. This should be addressed in one or two sentences. vi) For Figure 1, I suggest expanding the panel to include one or two additional 'non-cancerous' cell lines. vii) Additionally, a heatmap displaying IC50 values instead of response curves might enhance the readability of the data. viii) Regarding Figure 5, I recommend omitting it from the manuscript and using only Figure 6, as it appears to be a condensed version of Figure 5. This change would greatly improve the overall readability of the results section.

Lastly, I appreciate the use of bioactive biotinylated versions of lurbinectedin and PM54, and I have no criticisms regarding this aspect of the study. Simply nice to see it works.

Discussion(⭐⭐⭐⭐⭐): The discussion is well written and sufficiently discusses the major findings of the paper. Adding a section discussing the benefit besides immunotherapy for metastatic melanoma could be helpful.

Reviewer Information Dr. Jacob Haase is a cancer scientist with 9+ years of experience in academic wet and dry lab work. His fields of expertise include CIRSPR/Cas9, but also molecular (cancer) biology in pan-cancer context and other disease. He is very familiar with many off the presented techniques and am able to interpret the shown data. His experiences include ribosomal profiling and sucrose gradients, protein purification, CRISPR/Cas9, RNA-sequencing plus its computational analysis, as well as quantitative proteomics.

Dr. Jacob Haase on ResearchHub: https://www.researchhub.com/user/991840/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐⭐): In this preprint, Jakob Trendel et al. introduce XDNAX, a 'zero-distance' photo-crosslinking method, to quantify proteins directly interacting with DNA in human cells (in the interphase of a Trizol-prep, enabling enrichment of such complexes). While the approach itself is not new, several key modifications, including combined metabolic DNA-labeling of cultured cells with 4-thiothymidine (4ST) and the use of a specialized high-intensity 365 nm LED-based irradiation system, significantly enhance efficiency. In this study, the authors identified an atlas of over 1,000 proteins directly interacting with DNA in the breast cancer-derived cell line MCF-7. Comparing DNA interactomes from cells treated with estrogen or genotoxic chemotherapy, the authors revealed changes in the recruitment of transcription factors and DNA damage proteins. They also identified potential proteins involved in overcoming cis-platin resistance, suggesting a promising translational path. The study is of the highest quality, with well-explained rationales, meticulously described experiments, and thoughtful interpretation of results. However, the manuscript is overly long and would benefit from focusing on a few key targets and interpretations, which could be moved to the discussion section for a clearer reading experience.

Considering that all points raised below are recommendations or minor concerns, and acknowledging the study's quality, promising nature and significant potential impact, I rated it 5 stars.

Impact (⭐⭐⭐⭐⭐): This manuscript has the potential to significantly impact basic research in the field of chromatin and DNA-binding proteins across various diseases. The research question is highly innovative, pushing boundaries in basic DNA-interactome analysis. It not only overcomes old hurdles but also demonstrates clinical relevance by uncovering specific vulnerabilities in the DNA repair machinery of breast cancer cells treated with conventional platinum-based chemotherapy.

Methods (⭐⭐⭐⭐☆): The study is meticulously designed, with a detailed description of the methods. - The authors provide a thorough explanation, supported by a strong understanding of physics, for why their system is effective compared to conventional UV methods for thiol-containing nucleobases. They explain their choice of 365nm LEDs, despite 4ST typically reacting to lower nm wavelengths also available in LEDs, and discuss how they mitigate the potential overheating of biological material (cells) due to the 1000-fold higher energy of their approach compared to traditional UV-crosslinkers. - One minor discrepancy is the lack of mention of the second round of TRIzol treatment of the interphase in the Methods section, which is addressed in the Results section. - The detailed protocol presented in the study is effective but may be costly, especially with the use of SILAC. Is there a way to address this point? - To aid reader understanding, it would be helpful for the authors to briefly explain why the protein-DNA complexes gets stuck in the interphase during the TRIzol preperation.

Results (⭐⭐⭐⭐☆): <br /> - The results section is lengthy, and some information could be moved to the discussion for better organization. - How and why was 4 days determined as the optimal time for cell treatment with 4ST? Would longer treatment increase efficiency? How does one outcompete standard thymidine (T)? - Providing statistics on the number of Ts that would need to be exchanged for 4ST to achieve good results in downstream applications would be informative. How would one approach cell lines that only double once every 7 days? - The term "direct proximity" is unclear. It would be helpful to define the distance at which molecules are considered to be in "direct proximity" for cross-linking. - The study primarily focuses on MCF7 and to a lesser extent U2OS cells. Including additional cell models could enhance the understanding of whether the observed results have broader biological significance or are specific to certain diseases. - The enrichment of peptides mapped against intrinsically disordered regions for DNA-binding in MCF-7 cells is intriguing. It would be valuable to investigate if this is a general observation across different cell types and if it is disease or malignancy-specific. - Comparing the proteome in enriched interphase nuclei versus enriched metaphase nuclei could provide further insights or at least discussed - Page 4: The additional TRIzol-prep step mentioned in the results section should also be included in the methods section for clarity, as outlined above. - The proposed DNA-binding of SRSF3, a well-studied RNA-binding protein and splicing factor, raises questions about the "zero-distance" protein enrichment claim. This could imply a new function or genes that are in proximity being trapped in the analysis. This should be elaborated on in the discussion, considering the possibility of a "phase-separated compartment". - Figure S3: The use of a sample-specific enrichment cut-off makes sense, but using 5 replicates may pose a challenge for researchers conducting similar experiments. Clarifying the number of replicates needed for confident conclusions would be helpful. - For the estradiol-treatment of MCF-7 cells, clarification on the number of replicates used per condition would be beneficial. - The rationale behind using 100µM of each compound is unclear and should be further explained, as this concentration is very unusual in cell culture experiments. - Figure 6C, D: The relative changes after using an siRNA pool are rather mild. Further, the information might be better presented as heatmaps for clearer visualization of the results.

Discussion(⭐⭐⭐⭐☆): The discussion is concise and directly related to the results. But I have the following points that I think are worth addressing: - Further exploration of how XDNAX could enhance ChIP-seq or Cut’n Run approaches to improve precision, replicability, and informativeness would be valuable. Readers might also be interested in the implications for the reliability and utility of the ENCODE database, given the superior performance of XDNAX compared to formaldehyde crosslinking. Elaborating on the differences between XDNAX and formaldehyde crosslinking would provide a clearer understanding of the advantages of the former. - Additionally, discussing the potential for XDNAX to improve the analysis of 3D chromatin architecture, especially regarding how this architecture might respond to certain therapeutics, would be insightful. Exploring how the approach enhances deep-learning models for predicting DNA-binding proteins, such as transcription factors, could further demonstrate its utility. - The enrichment of splicing factors in the data, despite their likely non-zero distance from DNA, is an intriguing observation. Connecting this with the theory of phase-separated compartments could provide a better context and challenge the traditional notion of 'zero-distance' interactions.

In summary, expanding on these points would enrich the discussion and provide a more comprehensive understanding of the implications and potential applications of XDNAX in various biological contexts.

Reviewer Information Dr. Jacob Haase is a cancer scientist with 9+ years of experience in academic wet and dry lab work. His fields of expertise include CIRSPR/Cas9, but also molecular (cancer) biology in pan-cancer context and other disease. He is very familiar with many off the presented techniques and am able to interpret the shown data. His experiences include ribosomal profiling and sucrose gradients, protein purification, CRISPR/Cas9, RNA-sequencing plus its computational analysis, as well as quantitative proteomics. He has used XRNAX, a methodology similar to XDNAX, published by Jakob Trendel et al. in 2018 in Cell. Additionally, he has expertise in working on chromatin modifying enzymes and transcription factors. However, his limitations lie in his understanding of the physics of the cross-linking process and shallow expertise in proteomics and LS-MS.

Dr. Jacob Haase on ResearchHub: https://www.researchhub.com/user/991840/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆): The authors investigate the critical role of the PBAF chromatin remodeling complex in maintaining centromere integrity, essential for proper chromosome segregation during cell division. They identify PBRM1, a key subunit of PBAF, as crucial for protecting centromeres and pericentromeres from structural damage. Their research demonstrates that the loss of PBRM1 disrupts PBAF binding, leading to compromised centromere stability and increased reliance on the spindle assembly checkpoint, suggesting potential therapeutic targets in cancer treatment.The authors skillfully combine fundamental functional research with in vivo validation, illustrating their comprehensive understanding of the subject matter. Throughout the introduction and manuscript, they display a strong grasp of existing knowledge and contribute valuable insights that could significantly impact the field. However, their study is somewhat limited by the absence of a crucial recovery control, which affects the robustness of their conclusions. Despite this limitation, the authors' work represents a significant step forward in understanding the role of PBRM1 and the PBAF complex in safeguarding centromere structure and preventing chromosomal instability.

Impact (⭐⭐⭐⭐☆): The paper is poised to make a significant impact, introducing novel insights for the basic research community and offering promising ideas for treating PBRM1 mutant cancers. The work is undoubtedly significant. The Introduction is well-crafted, with strong language and a clear storyline. However, the manuscript has certain drawbacks, particularly in terms of providing a recovery control, which does not fully meet state-of-the-art standards. Reviewers for a journal are likely to raise concerns about this aspect, as detailed below.

Methods (⭐⭐⭐⭐☆): As outlined above, the paper is well-presented, and the methods are generally sound. However, I have several major and minor concerns and suggestions: A) Isogenic Models and Single-Cell Cloning: - The use of isogenic models of clones generated via CRISPR/Cas9, while commendable for the effort in generating numerous knock-out clones, may have limitations. The comparison of growth rates between these clones and the parental line is not very informative due to the long generation time of the clones. It is possible that the clones are those that have overcome the lethal effects of PBRM1 loss through compensatory mechanisms, which is common for knockouts generated this way. - To accurately interpret the results, particularly the proteome analysis, it is essential to perform a recovery experiment with exogenous overexpression of PBRM1. I understand the challenges associated with overexpressing a large 180 kDa protein, but this step is crucial for validating the findings. - The correlation of proteomic data for PBRM1 expression with centrosome/centromere proteins is logical and convincing, but would be strengthened by these additional controls. B) Additional Controls: - Including a second negative control clone in the analysis would bolster the robustness of the findings. - An alternative approach could involve demonstrating that knockouts with transfected sgRNAs or inducible systems yield similar effects. This would provide additional validation for the observed phenomena. C) Incorporating Publicly Available Data: - Integrating publicly available CRISPR screen information on PBRM1 would enhance the manuscript by providing context and supporting evidence. - It would be beneficial to discuss the findings in relation to published data, such as CRISPR screen data from platforms like DepMap. This comparison could help in contextualizing the results and reinforcing their significance.

Results (⭐⭐⭐⭐☆): I have the following major and minor concerns and suggestions: - Comparing growth rates from clones is not very informative due to the long generation time of these clones versus the parental line. Clones might have compensated for the lethal effects of PBRM1 loss, which is typical for BAF-component knockouts. - Explanation of CDK1i and siCCNB1 Use: The rationale behind using CDK1 inhibitors (CDK1i) and siRNA against Cyclin B1 (siCCNB1) should be clarified for readers who may not be familiar with mitosis. - The lack of CENPA (or other peptides of other proteins) in the proteomic data is a common obstacle. Double-checking CENPA expression via Western blotting would be better – immunofluorescence (IF) may not be sufficient. - Figure 2g: Can the authors present an intensity profile across nuclei for the H3K9me3 signal, even if the effects are not very strong? This would provide more quantitative data to support the observations. - The statement “(…) the changes in structure at centromeres and pericentromeric regions where PBRM1 is bound lead to sensitivity to mitotic perturbation when PBRM1 is absent” is misleading. The authors investigate the localization of certain proteins based on antibodies and ChIP/CUT&RUN, not the actual structural changes. This needs to be accurately reflected in the text. - Including DepMap data more frequently could enhance the manuscript by providing additional context and supporting evidence. - How does PBRM1 deletion affect the expression of other SWI/SNF proteins? Loss of function in SWI/SNF proteins typically affects the expression of other BAF components through targeted proteasomal degradation. - Figures 1 and S1: For clones, is the remaining signal in the Western blots non-specific? - Some parts of the text, such as the explanation of the k-mer analysis, could be simplified for better readability. For example: “Because of the repetitive nature of these regions, we also analyzed centromere and pericentromere-associated reads that mapped to multiple locations using a k-mer analysis1, 22 to identify 51-mer sequences that are significantly enriched in the datasets (see Supplementary Fig. 5 for workflow) relative to the IgG control. - Please explain the term “transition arms” in the text for clarity. - It would be helpful if the authors could describe what makes PBAF different from canonical BAF and non-canonical BAF.

Discussion(⭐⭐⭐☆☆): The discussion lacks sufficient interpretation of the data and how it fits the current literature. While it presents significant findings, several areas could be enhanced to provide a more comprehensive analysis and context - The authors should point towards clinical trials and available inhibitors, or in silico predictions, to connect their findings with potential therapeutic applications. This would help bridge the gap between basic research and clinical relevance. - The discussion would benefit from an expansion on how the PBRM1 knockout findings align with current literature, such as the DCAF5 paper from the Charles Roberts lab (at St. Judes Hospital, Memphis). - The authors should elaborate more on the impact observed in ARID1A knockouts. It would be beneficial to discuss what happens when other PBAF components, aside from PBRM1, are knocked out. This could provide insights into the broader implications of PBAF dysfunction.

Reviewer Information Dr. Jacob Haase is a cancer scientist with 9+ years of experience in academic wet and dry lab work. His fields of expertise include CIRSPR/Cas9, but also molecular (cancer) biology in pan-cancer context and other disease. He is very familiar with many off the presented techniques and am able to interpret the shown data. His experiences include ribosomal profiling and sucrose gradients, protein purification, CRISPR/Cas9, RNA-sequencing plus its computational analysis, as well as quantitative proteomics.

Dr. Jacob Haase on ResearchHub: https://www.researchhub.com/user/991840/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐☆☆☆): The manuscript is presented with clear figures, and the text is overall well-written with few mistakes, with only minor concerns. However, the study's novelty is limited, as similar data has been published before, as outlined below. Additionally, the limited number of models used makes the findings less convincing.

Impact (⭐⭐☆☆☆):<br /> - Since the efficacy of CPI-613 has been evaluated in several clinical studies, CPI-613 shows promise based on existing data (see CPI-613 + FOLFIRINOX clinical study in pancreatic cancer). - The combination of CPI-613 with chemotherapy has already been published (https://www.mdpi.com/2072-6694/11/11/1678). The authors need to discuss and interpret these results in conjunction with their own findings. Although the authors cite these studies, they should highlight the novelty of their particular study. - A weak point of the study is the low number of models used to test the hypothesis. The authors should consider incorporating additional lines to strengthen their findings. Consequently, the current story is not particularly compelling.

Methods (⭐⭐⭐☆☆): Overall, the methods are solid, following state-of-the-art practices, and are well-described with sufficient details. However, there are certain downsides to the quality of the methods section: - The lack of models is problematic for drawing definitive conclusions. Suggested solution: generate chemoresistant lines (and potentially newly patient-derived lines) by treating those lines with increasing concentrations over a longer period. This approach is commonly used in other studies. - Clarify the term ‘induction of XYZ’ (Xenografts). The authors should use ‘transplantation’ or ‘injection’ instead. - Specify the control condition for animal treatment. Was it corn oil injection? This needs to be stated clearly. - The authors need to specify the exact ‘RNA assay kit’ used for RNA extraction. - There does not appear to be a list of antibodies with catalog numbers, species, etc. - Similarly, for IHC, the antibody information is missing. - For the statistics, it is suggested that the authors show every single datapoint for each bar graph, not just in individual figures.

Results (⭐⭐⭐☆☆): The results are solidly presented with no redundant or unnecessary information, making it easy to follow the narrative. Nonetheless, there are several major and minor points the authors need to address: - Add PRISM data from DepMap or other platforms for CPI-613 in ovarian cancer cell lines. Given the low number of tested cell lines, this addition would strengthen the hypothesis. - Figure 2J: Specify how many images were evaluated per animal and the total number of animals used. - Figure 2C: CPI-613 treated animals seem to number only n=6, not 8 as stated. Although not a major issue, this discrepancy requires a different statistical test (Mann-Whitney U or log-rank test), which is not indicated in the manuscript. - Figure 2G-I: Include scale bars in the images. - The authors should better refrain from using the term "chemotherapy" throughout the manuscript when talking about the mouse treatments. Instead, specify the actual drugs used (carboplatin + paclitaxel). - Figure 4D & H: Clarify what is meant by 'Total Radiation Efficiency/Efficacy' as indicated on the y-axis. - Figure 6S: The Western blot detection of PARP1 is questionable. The ratio of cleaved PARP1 between the control and CPI-613 does not change, only the overall expression in CAOV3. Typically, one would expect not an increase in expression, but an increase in the lower band versus a decrease in the full-length band during apoptosis.

Discussion(⭐⭐⭐⭐☆): The authors provide an in-depth discussion of their results and interpret them well. - However, how do the authors envision translating these findings into clinical practice for ovarian carcinoma? What would be the recruitment requirements for a potential study in regard of the toxicity profile, since most of these chemoresistant tumors from patients are high-grade ones? - How do other OXPHOS-targeting agents perform in ovarian cancers? What does the literature say about these other agents? - Lastly, the authors should highlight the main selling point of this study, given that much of the information has been published before (as noted in the example above).

Summary Increased mitochondrial activity and upregulated OXPHOS are often observed in certain tumors, contrasting with the Warburg effect. In this study, the authors examine the mitochondrial inhibitor CPI-613 for treating chemoresistant ovarian cancer cell lines (OVCAR3) in vitro and in vivo, comparing them to chemosensitive ones (CAOV3, F2). The authors demonstrate increased survival and reduced tumor burden. CPI-613 inhibited key enzymes in the TCA cycle, decreasing OXPHOS and enhancing chemotherapy efficacy in resistant tumors. It induced mitochondrial collapse, increased superoxide production, reduced ATP, and triggered apoptosis, showing promise for treating chemoresistant ovarian cancer.

Reviewer Information Dr. Jacob Haase is a cancer scientist with 9+ years of experience in academic wet and dry lab work. His fields of expertise include CIRSPR/Cas9, but also molecular (cancer) biology in pan-cancer context, including ovarian carcinoma, and other disease. He is very familiar with many off the presented techniques and am able to interpret the shown data. His experiences include ribosomal profiling and sucrose gradients, protein purification, CRISPR/Cas9, RNA-sequencing plus its computational analysis, as well as quantitative proteomics.

Dr. Jacob Haase on ResearchHub: https://www.researchhub.com/user/991840/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆) The study is innovative and addresses a critical area in basic and cancer research. The study is of high quality, with methodologies executed to the highest standards and presented clearly without redundancy. The language is of high quality, and the data interpretation is robust. However, extended data figures mentioned in the manuscript were not available. The authors propose that MORC2 functions as a dimer and is extensively phosphorylated at specific hotspot sites.

Impact (⭐⭐⭐⭐☆): The authors provide intriguing new insights into the CTD-mediated, DNA-binding-independent autoregulation of MORC2's activity. Notably, ChIP-seq and ATAC-seq analyses reveal that MORC2 preferentially binds open chromatin. The key question is how wild-type or mutant MORC2 regulates chromatin in cancer-derived cell lines, similar to the Charcot-Marie-Tooth disease model tested with HeLa cells. Although the study is of exceptional quality, certain things are missing, including data generated with cancer-derived models. The data from Tan et al. has been exclusively generated with Hek293T cells, which do not represent any cancer.

Methods (⭐⭐⭐⭐⭐): The methods used are of the highest standard and are described in great detail. However, there are a few concerns: - For generating MORC2 KOs, what sgRNAs were used for wild-type cells? Were these cells subjected to mock transfections or left completely untransfected? This raises concerns about the validity of the RNA-seq data, which is limited by the detection of only a few differentially expressed genes post-KO. - It would be valuable to include experiments involving KO generation followed by re-expression of MORC2 in cancer-derived cell lines. - Additionally, the study appears to include videos of single-molecule fluorescence imaging and atomic force microscopy.

Results (⭐⭐⭐⭐⭐): The results section, while brief, is rich in novel findings. To further enhance the manuscript, the authors could consider the following suggestions: - the authors should include cancer-specific knockout or mutation data from DepMap or other public databases. Exploring the use of inhibitors, such as those targeting HSP90, to disrupt MORC2 dimerization and assess their therapeutic potential. - Incorporating cancer-relevant experiments, such as comparing MORC2 knockout with wild-type and mutant protein re-expression or siRNA-mediated depletion. - Additionally, considering including a xenograft model, if feasible and if time allows. - Presenting data on MORC2 mutation sites in cancer and other diseases could provide valuable insights.

Discussion(⭐⭐⭐⭐☆): The Discussion offers great insights and interpretations of the data but could benefit from being more concise. Consider including the following points: - Exploring how MORC2 interacts with or interferes with SWI/SNF chromatin remodelling complexes. - Discussing the impact of alternative splicing on MORC2 activity, functionality, and localization, including whether phosphosites might be spliced out. - The authors could note that the MORC2 gene locus is frequently gained in skin cancer-derived cell lines.Investigate whether there is a druggable structure associated with cancers that depend on the mutant form of MORC2 (data from DepMap).

Reviewer Information Dr. Jacob Haase is a cancer scientist with 9+ years of experience in academic wet and dry lab work. His fields of expertise include CIRSPR/Cas9, but also molecular (cancer) biology in pan-cancer context and other disease. He is very familiar with many off the presented techniques and am able to interpret the shown data. His experiences include ribosomal profiling and sucrose gradients, protein purification, CRISPR/Cas9, RNA-sequencing plus its computational analysis, as well as quantitative proteomics.

Dr. Jacob Haase on ResearchHub: https://www.researchhub.com/user/991840/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆) In this manuscript, Paudel and Lee identify a mechanism by which Epstein-Barr virus (EBV)-encoded RNA 1 (EBER1) sequesters ribosomal protein L22, preventing it from suppressing its paralog L22-like 1 (L22L1). This leads to the expression of L22L1, which is incorporated into ribosomes that preferentially translate mRNAs involved in oxidative phosphorylation, a process crucial for the growth transformation and immortalization of resting B cells upon EBV infection.The manuscript is compelling, of good quality, and well written. Although it is quite short, I enjoyed the quick read and found the efficient use of the CRISPR-KRAB system impressive. The story is concise, and the figures are of decent quality. However, there are concerns that reduce the overall quality, such as the lack of certain controls.

Impact (⭐⭐⭐☆☆): The study is pure basic research that builds on previous findings from the fields of immunology and protein translation. While it introduces novel insights, it does not explore or discuss the clinical applicability of these findings or their potential impact on advancing our understanding of EBV biology or treatment.

Methods (⭐⭐⭐☆☆): The methods section, though well written with sufficient details for individual methods, revealed some concerns: - The section lacks descriptions of certain methodologies, including RNA extraction, RNA sequencing, and western blotting. - Additional information about the BJAB-B1 cell line is needed. There are conflicting reports regarding the EBV status of the BJAB cell line. - Detailed protocols are provided for ribosome profiling and polysome fractionation, which enhances reproducibility. However, the description of the CRISPRi approach lacks information on the design and validation of sgRNAs. - The methods for measuring ATP levels are clear, but additional controls, such as measuring ATP levels in unrelated knockdowns, would strengthen the conclusions. - The authors assume that CRISPRi specifically and efficiently knocks down EBER1 without off-target effects, but this requires thorough validation. A recovery experiment with exogenous overexpression would be ideal. - The EBV growth transformation assay lacks precise details. The statement “Flask was swirled gently and placed in a CO2 incubator at 37°C for several weeks and examined as indicated” is not sufficiently specific about the duration.

Results (⭐⭐⭐⭐☆): The overall approach makes sense, and the results are generally of good quality. It is impressive that the authors found the Cas9-KRAB-knockdown system to be so effective, and the work involved in generating a paralog-specific antibody is particularly notable. However, there are certain concerns and suggestions: - It would be beneficial to include a recovery experiment with the exogenous overexpression of EBER1. - For Figures 2B and 2C, clarification is needed on what constitutes the WT control. Is it a control sgRNA? - How was the antibody generated? - Additional information on the purpose of the growth-transformation assays would be valuable. - Inclusion of in vivo data would enhance the study. - The mechanism behind the reduction of RPL22L1 requires further investigation. Is it truly a translational effect, or could it be secondary transcriptional or post-transcriptional? The post-transcriptional effect, as discussed in the preprint’s discussion section, might not be direct through L22. RNA stability can be tested in the knockdowns and control cells by running an RNA stability experiment using Actinomycin D over several time points up to 6 hours, with qPCR as the readout. - Changes in translational activity could be tested using a proteasome inhibitor at different time points, with Western blotting as the readout.

Discussion(⭐⭐⭐⭐☆): The discussion is well written and effectively interprets the key findings of the study. However, it would be valuable to explore the potential clinical applications of these findings. Is it feasible to develop inhibitors or target specific B cells with an antibody?

Reviewer Information Dr. Jacob Haase is a cancer scientist with 9+ years of experience in academic wet and dry lab work. His fields of expertise include CIRSPR/Cas9, but also molecular (cancer) biology in pan-cancer context and other disease. He is very familiar with many off the presented techniques and am able to interpret the shown data. His experiences include ribosomal profiling and sucrose gradients, protein purification, CRISPR/Cas9, RNA-sequencing plus its computational analysis, as well as quantitative proteomics.

Dr. Jacob Haase on ResearchHub: https://www.researchhub.com/user/991840/overview

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (5/5)

Impact (5/5) This paper describes studies aimed at solving the mystery of the role of EBER1 in Epstein-Barr virus (EBV) infections. As noted by the authors, EBV has been studied extensively and the importance of EBER1 has been known for over 40 years but how it aids in EBV infections has remained elusive due to the fact that it has been impervious to attempts at knockdown using conventional methods to date. Now, using CRISPR, the authors have been able to knock down EBER1 by over 90% and see the effects. In their interesting findings they see that unlike most RNA modulators, EBER1 does not work directly on the genome but instead, acts as a translation modifier by inhibiting the ribosomal protein L22 which then allows for the upregulation of its paralog, L22L1. The effect of this on cellular function is to increase oxidative phosphorylation, an event which supports cellular growth and transformation. This finding has high impact and with further work can lead to finding targets to limit the spread of cancers that are EBV based. One suggestion is to change the title to “Epstein-Barr virus non-coding RNA EBER1 promotes the expression of the ribosomal protein paralog L22L1 to boost oxidative phosphorylation” to increase search engine hits.

Methods (4/5) The authors used standard cell culture methods with the use of CRISPR to knock down EBER1 in EBV infected BJAB-B1 cells. BJAB cells are an EBV negative tumor cell line often used in oncology studies. For these studies they infected these cells with EBV so as to have controls and steady state EBV levels. Immunoblotting was used to confirm increases in L22L1.The methods were all cell based and appropriate. Next steps, although not for this particular study, would be to produce a mouse model of EBER1 conditional knockdown and see if introduction of EBV led to EBV based cancers or other diseases.

Results (5/5) The results clearly show that loss of EBER1 causes an increase in L22L1 within ribosomes. Overexpression of L22L1 in ribosomes led to the expression of mRNAs associated with oxidative phosphorylation. Examination of ribosomal subunits in the EBER1 knockdown cells confirmed that loss of EBER1 led to a similar pattern of mRNAs expression associated with oxidative phosphorylation. Interestingly, if L22L1 was knocked down in these cells, colony formation was inhibited suggesting that a role for oxidative phosphorylation in the formation of growth and potentially transformation.

Discussion (5/5) This paper gives an intriguing look into the pathway by which EBV can lead to cancer formation, something which has eluded researchers for decades. Thus, this study has the potential to be very high impact. The study identifies a key step by which EBER1, a known protein involved in EBV function, leads to cellular growth by activating L22L1 which is a paralog to the ribosomal protein L22. Activation of L22L1 stimulated oxidative phosphorylation pathways that are normally quiescent which in turn allows for cellular growth. There are still many holes in the story, but this paper plugs a big one. It would be nice to see the next steps taken in determining how these particular oxidative phosphorylation pathways stimulate cancer growth. Also, as noted above, moving this into a mouse model would be a great step, although not needed for the publication of this particular article.

Reviewer Information The reviewer (Dr. Heather Duffy) is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/overview

ResearchHub Peer Review Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆)

Impact: Perez et al have done an in depth examination of a series of CAR T moieties involved in tumor suppression for soft tumors, with an eye on determining if slight changes in the binding site could increase persistence and perhaps even allow for use of this technology in solid tumors, an ongoing problem in the field of CAR-T use in cancer treatment. The impact of this work has the potential to be high because it identifies moieties that increase the persistence of function of CAR-T function past what is presently used in the clinic today.

Methods: Overall, the study is well thought out with the main stem of the molecules left intact so as not to add in too much diversity at once, while a number of individual new compounds wee tested both in vitro in and in their function over time. The authors used tumor relevant NALM6 or CD19+ A375 cells for the in vitro studies and NSG mice that were tail injected with either NALM6 (soft tumor) or CD19+ A375 (melanoma for solid tumor) cells to elicit tumor growth.

Results: The main findings were that there were a number of changes that increased persistence, with a k7 moiety being a primary driver of persistence in soft tumors, but that the micro-environment of solid tumors presented different transcriptional responses as compared to soft tumors following CAR-T treatments indicating a need for more work to understand the different signal transduction pathways between these two tumor types in order to treat solid tumors in this fashion. Some anomalies to note: 1. Interferon gamma and TNF are known to activate the JAK-STAT pathway. In your assays there is change (increase) in INFgamma and TNF but the JAK-STAT activation does not correlate with these. It is worth noting that there may be differences in the intermediary pathways that are activated by different moieties, giving different outcomes. 2. In the solid tumor model, did you have an opportunity to exam any of the inflammatory cytokine levels, and if so, were they similar to changes in in soft tumors or were they also not the same as what was seen in soft tumors treated with CAR T? This could be a key to why there was not as robust a response as one would hope for in the solid tumors. 3. Mechanistic information as to how the k7 moiety functioned to increase persistence could be quite interesting and may lead to information that could help in determining how to approach the solid tumor microenvironment. 4. Minor point, the writing is very technical and could use more descriptive language for people that may not be directly in the field.

Opportunities for increasing value: This paper is informative and interesting. It could be helpful if there was more discussion of the potential reasons that the different moieties caused the different molecular outcomes as this might shed light on the molecular basis of persistence. A follow up on why solid tumors behave so differently could be a true clinical breakthrough.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆)

Impact (⭐⭐⭐⭐⭐): This paper compares the ability of three different species, two primates and one non-primate, to persist in behaviors and works to explain why there are such similarities in some actions but differences in others. It makes some interesting findings that may be relevant to brain cognition in humans and therefore has the potential to have high impact in the behavioral neuroscience field.In this study the authors utilized a well known decision making paradigm to study how decision making compares between primates and mice. This is important because rodent models are increasingly being used as replacements for primates in cognitive studies, particularly developmental studies, drug development, and injury models. This use of rodents can only be of value if their decision making behaviors properly model those of the primates they are replacing. Neural network studies in primate studies would suggest that rodents would not be a total replacement for cognitive studies and this paper seems to corroborate that, at least when it comes to task persistence, with rodents switching tasks at a more rapid pace than the primates. It is unclear yet how to incorporate this information into cognitive studies using rodents but having this information is an important step in being able to

Methods (⭐⭐⭐⭐☆): The authors use three different species, mice (Mus musculus (males and females). They were presented with a species appropriate k-armed bandit task where targets were placed for them to choose from to get a reward. Individuals had to choose from a known reward or to explore for a new reward. Switching between choices was analyzed and compared using standard ANOVA.

Note: Please add IACUC and IRB protocol numbers to the methods sections.

Results (⭐⭐⭐⭐⭐): The authors examined switching behavior and exploratory behaviors in each species and found that while all three species engaged in switching and exploring, the mice switched targets most often indicating a lack of task persistence. In other words, they seemed to explore their options more than the primates did. This remained even after controlling for trial times and task design. Overall the results were compelling and well documented. The statistical analysis was thorough. The figures were clear but, if space were not an object, I would recommend that the 4 across panels be reworked to be a 4 square with 2 top panels and 2 lower panels, all of which could be a bit larger for better viewing.

Discussion(⭐⭐⭐⭐☆): The discussion is fairly thorough although I think the addition of a discussion of the neural network models of task switching could add value. The neural networks are vastly different between rodents and primates and may also be a reason for the difference seen in the task persistence seen in this study. A discussion of next steps on how to potentially encorporate this information into the analysis of rodent studies on cognitive abilities would be so helprul seeing as we will only continue to increase the use of rodents in these types of studies, although that may take further experiementation.

Overall, the study is excellent and should be published.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆)

Impact (⭐⭐⭐⭐☆): This paper is a follow-up on a previous paper from the Hauryliuk laboratory where they had reported that New1 played a role in translation termination but had not identified the mechanism. First off, it is greatly appreciated by this reviewer that they continue to work on the problem to try to identify the mechanism, rather than just leave it at “we found a connection but don’t know what it is”. So many researchers don’t take this next step. I commend the authors for this work on that front. The work itself looks at the mechanism by which New1 facilitates the termination of protein translation at the ribosome and identifies its binding site and ability to stabilize the non-rotated ribosomes allowing for binding of eRF1 to facilitate translation termination. This has interest beyond basic interest in the understanding of cellular function as proper protein translation has important implications in human health and disease. This paper has medium high impact and would have higher impact if it would take the next step and discuss the implications of New 1 binding and function in cellular health and disease. No new experiments needed, just a tie into organismic health.

Methods (⭐⭐⭐⭐⭐): These studies were done in a variety of yeast strains expressing variants of interest relevant to the study. The authors used cryo EM to map the structure and binding of New1. Next gen sequencing was performed on multiplex 5Pseq libraries using standard methodologies. The methods used were all adequate and high quality.

Appropriate statistical analyses were performed.

Results (⭐⭐⭐⭐☆): The cryo EM images of the elongated and termination state ribosomes clearly show the New1 binding to the non-rotated ribosomes but not as visible to rotated ribosomes indicating its functional binding and potential stabilization of the non-rotated form. These interactions are stabilized in the experiment by glutaraldehyde, one thing of interest would be to calculate the dwell time and determine if there are difference in dwell time with each state. Not needed for publication of this work, but of interest.Using yeast strains lacking New1 the authors confirmed that loss of New1 led to a decrease in translation termination leading to a “pile-up” as it was referred to that were stop codon and context-specific determinants of translational termination. This indicates that New1 binding is important for blocking these pile-ups in order to facilitate normal translational termination. The finding that overexpression of eRF1 does not rescue the loss of New1 is very mportant. This indicates that New1 and eRF1 are not working in the same capacity but are part of a complex but have different roles. It would be of interest to do a similar study on the binding of eRF1.

Discussion(⭐⭐⭐☆☆): The key take-away from this paper is that the interaction between New1 and the ribosome is important for normal translation termination to occur. The data are solid, but the discussion is somewhat lacking in its relationship to cellular health and disease. While basis science is always of great importance, it would add greatly to the value of this paper to point out what the effect of a genetic loss of New1 could lead to, or what might happen if a drug for a disease is developed that has the side effect of targeting this interaction. No other experiments are suggested for this paper but a broadening of the viewpoint would greatly expand the interested audience for the paper. Well done.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆)

Impact (⭐⭐⭐⭐⭐): This study looks at the similarities between cancer and wound healing, focusing on how biopsies may stimulate basil cell carcinomas (BCCs) to transition from a non-invasive to an invasive phenotype. This has obvious impact on human health as biopsies are routinely done on people with suspected BCC which, as the data here suggest, may have a negative impact on the spread of the cancer.The over RNA data are strong but limited in their scope in that there is little data on whether the RNA data are indicative of actual changes at the protein level. While some changes in H&E staining indicate cellular shape changes consistent with a more invasive phenotype, this paper could be easily strengthened with a couple of simple protein assays.

Methods (⭐⭐⭐☆☆): The RNA methods are well thought out and well done. Additional recommendations would be to do a simple stain for activated myofibroblasts such as smooth muscle actin which stain myofibroblasts and a few assay for some of the proteins associated with some of the upregulated RNAs identified in the RNAseq experiments to show that translational efficiency is maintained and that the effects assumed to be occurring based on RNA production are happening at the protein level.

Results (⭐⭐⭐⭐⭐): There are a number of interesting findings in the paper including that there was some consistency across the BCC samples. The identification of TIMP1’s association with MP7 actually make’s some sense as TIMP1 has been shown to be associated with poor prognosis in other cancers. What makes less sense is the presence of CLDN4, a tight junction protein, in an invasive cell type. Generally these junctions form stable cell-cell junctions which inhibit cell movement and limit invasive behavior. They are lost when cells undergo cell division and during cell migration. An explanation or hypothesis on this, more than a single citation, would be a good addition to the discussion.A great experiment, but not needed for this paper, would be to do cryo-EM on these sample and see if the nodular form has tight junctions while the invasive form does not, particularly if you could identify the MP3 cells near the MP7 cells. The finding that wounding causes fibroblast activation and an inflammatory response is not novel, although in the context of BCC transition to an invasive phenotype it has become important. I would encourage the authors to look for markers of activated fibroblasts such as smooth muscle actin to further support their findings.

Discussion(⭐⭐⭐☆☆): This paper shows that the simple act of performing a biopsy on a basil cell carcinoma can have unintended consequences. Wounding sets off a cellular response which includes activation of resident fibroblasts, inflammatory pathways including cytokine production and changes in gene activity. In the context of a cellular phenotype that is already poised for aggressive growth, these factors can tip the balance from indolent to invasive, setting the cancer into a growth phase. These data suggest that biopsy protocols be reviewed for whether they should be done, or whether areas of suspected BCCs should be surgically removed altogether on first contact.

The paper could be improved with a few protein assays to back up the RNA assays but the RNA assays are solid and the paper is well written.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐☆☆)

Impact (⭐⭐⭐☆☆): This paper looks at the activation or inhibition of STING at the structural level and finds that positional shifts in and around residue M271 were, at least in part, the reason for shifts from activation to inhibition. This is of interest due to the fact that of patients with STING-associated vasculopathy at infancy (SAVI) 62% of them harbor a mutation V155M which causes a similar shift at M271 suggesting that the SAVI causing mutation is leading to activation of STING through this molecular mechanism. If so, it would suggest a makes this a high impact finding although more studies in in vitro would have added to the value of this paper. The determination that orthostatic inhibition of STING is not appropriate for resolution of SAVI show the difficulty in targeting diseases with a multifactorial basis.

Methods (⭐⭐⭐⭐☆): The authors used X-ray crystallography and NMR spectroscopy for structural analysis. To assess INF signaling and other cytokine signaling the authors used PBMCs either frozen or from healthy volunteers. No IRB protocol was listed and should be added if human volunteers were used. The in vitro studies were cursory and should be expanded upon. For example, just noting if cytokines were up or down at a single time point is not terribly informative. INF and at least the most common of the interleukin’s found in SAVI should be followed over a 24-48 hour period to determine the life span of the effect. This would give more information as to the targetability of this site.

Results (⭐⭐⭐⭐☆): The major result here is the finding that the M271 residue and potentially the region surrounding it undergoes molecular shifts thatdefine whether STING is activated or inhibited. The activation of STING leads to a strong pro-inflammatory which, when out of context, leads to disease. The increase in INF and other cytokines seen in this study indicates that when M271 shifts, STING is activated. This would lead to the idea that inhibition of STING may be a way to limit inappropriate inflammatory responses in disease conditions. The authors found that the V155M mutation seen in a majority of SAVI patients cause a similar molecular shift leading to constitutive activation of the STING protein and production of INF and other pro-inflammatory cytokines. This explains the phenotype in SAVI. They show that inhibition of STING drops production of some cytokines but, interestingly, show that due to the complexity of the signaling pathways, orthosteric inhibition of STING can lead to paradoxical overactivation of STING.

Discussion(⭐⭐☆☆☆):This paper is written as one long results section with no introduction, no discussion. I am not sure where the authors had planned to submit this but it needs to be separated out in standard journal fashion with an introduction, results, and discussion section. The findings are interesting, but more work needs to be done on identifying the time course of the effects. The importance of finding a druggable target for SAVI is high as presently there is no cure for this autoinflammatory disease that can have devastating effects on infants and can lead to infant mortality. Unfortunately the fact that this study also showed that pure inhibition of STING can lead to worsening of constitutive signaling in SAVI shows that the molecular mechanisms are more complex and further studies are needed.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐⭐)

Impact (⭐⭐⭐⭐☆): Using a hepatic specific Mettl14 knockout mouse the authors examined the role of Mettl14, an important RNA regulator, in hepatic function. Mettl14 is a M6A writer enzyme that has been assumed to play a role in the function of M6A but to date there has been no mechanistic explanation of how. The data provided by these studies show that Mettl14 plays a key role in normal hepatic growth indicating that it is mechanistically vital and dysregulation may be a key part of hepatic growth disorders. The authors also looked at M6A reader enzymes Ythdf1/Ythdf2 knockouts both alone and in combination with the Mettl14 knockout and found similar hepatic disfunction indicating that any disruption in M6A leads to abnormal hepatic growth and fibrotic infiltration. Therefore, the title should be changed to reflect that it is both the M6A writers AND readers that impact M6A hepatic growth.This paper has the potential to be high impact in the field of RNA regulation but more work need to be done in the future to untangle the difference in what Mettl14 does vs. Ythdf1/2.

Methods (⭐⭐⭐☆☆): This is a standard knockout mouse study where genes were knocked out then studies were done to see the end result of the loss. All studies were done well.Added studies of interest that are easy and quick would be a dye spread assay to determine if functional cell connectivity via hepatic gap junctions were lost in the knockout animals. For this all you need is luciferase and an injection needle. Excise a liver upon sacrifice, inject luciferase into a small section, wait 5 minute, freeze in liquid nitrogen then section and view for dye spread distance. If the dye spreads less in the knockdown, you likely have less functional gap junctions and less cell-cell communication. You can find methods for this at Babica et al 2016 in Method Mol Bio. A second easy and inexpensive study to look at an important change would be to stain for or do protein assays for the tight junction protein Claudin1. Preferably the authors would do both. The disruption seen following the loss of either the reader or writer enzyme suggest loss of cellular integrity that would likely cause a disruption of these vital hepatic cell junctions. Loss of these junctions are associated with aberrant cell growth.

Results (⭐⭐⭐⭐⭐): The authors show that loss of either the reader or writer enzymes for M6A in the liver leads to aberrant cellular growth patterns. Interestingly, in the normal development, the loss of Mettl14 showed a gender bias with male mice showing a worse phenotype earlier in age than female mice do. Signs of inflammation, hepatic fibrosis, and regions of necrosis were seen. In models of liver injury. Genetic studies indicate changes in pathways leading to fatty liver disease were activated in the Mettl14 ko animals.Surgical resection, injury, and infection models all show increased fibrosis in the both knock out models showing that both reader and writer loss limits the liver’s ability for normal self repair. To identify mechanisms for this the authors looked for oxidative phosphorylation markers in the ko animals and found increased ox-phos in both reader and writer ko animals, indicating that the mechanisms by which liver damage is induced when M6A is dysregulated is through these pathways. Of particular interest is the finding of the association with TREX shuttle protein Aly/REF where knockout of Mettl14 caused an accumulation of Aly/REF in the nucleus suggesting that the mechanism by which loss of Mettl14 leads to cellular damage is a loss of RNA transport out of the nucleus.

Discussion(⭐⭐⭐⭐☆): This paper takes a deep dive into understanding the molecular mechanisms by which both reader and writer enzymes of M6A alter hepatic function. The authors do a great job of looking at a number of markers of cellular function and dysfunction. The figures are clear and the findings are novel. Their model of RNA sequestration due to Mettl14 loss is elegant and could explain a number of situations where RNA shuttling is compromised. This paper should be published.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆)

Impact (⭐⭐⭐⭐☆): This study looked at the events occurring in aging ovaries which has important implications for understanding infertility in women and early menopause. The findings point to macrophage infiltration as well as ANNEXIN and TGFb signaling as culprits in the development of the ovarian tissue environment that is plays a role in loss of fertility. The study identifies a subset of macrophages found in aging ovaries, but not in young ovaries, that may be appropriate to target to understand infertility. These macrophages, CXCR1lowCD81hi, are a subset of the macrophages that are present but they are involved in pro-inflammatory signaling which leads to the development of age related ovarian fibrosis and subsequent infertility.The ability to target these cells in individuals that suffer from infertility or early menopause may give hope to thousands of women of traditional child bearing years that hope to have families of their own. This makes this paper potentially high impact

Methods (⭐⭐⭐⭐⭐): The methods of this paper are very straight forward. Using virgin C57B6/6J mice they harvested the ovaries from young (2-3 month) or old (14-17 month) mice and separated the cell types using flow cytometry. Then, using RNAseq they examined the RNA profiles of the cells. The authors should also do a third group and this would be non-virgin old mice (14-17 months) to determine if having gone through pregnancy altered the outcome of ovarian aging.There needs to be validation of some of the RNAseq information by either doing protein assays on some of the hits or immunohistochemistry study to localize cell types.

Results (⭐⭐⭐☆☆): The main findings of this paper are that as ovaries age, the macrophage population of ovaries shifts from neutral to a pro-inflammatory phenotype. This has important implications for human health in that targeting inflammation may be one way to limit infertility. The identification of ANNEXIN pathways is novel and interesting. More work should be done in future studies on this aspect of the role of macrophages in the aging ovary.The results of the studies described here are interesting but, as with all RNAseq data, they do not go far enough. It would be good if the authors had sought to verify any of the RNA data with a follow-up study of protein levels or localization. Typo “Figuire 3B” should read “Figure 3BTypo Line 319 “Upon Examination” should read "Upon examination”

Discussion(⭐⭐⭐⭐⭐): As the authors noted, the ovary is subject to repeated, monthly wounding as each time an ovum leaves the surface of the ovary is damaged and the entire wound recovery process is started including the attraction of neutrophils and other inflammatory cells. For individuals with polycystic ovary disease, this process can be quite damaging. These studies may also shed light on this process. It will be interesting to see how this subset of macrophages is implicated in disease states. Overall this paper is quite interesting but needs data on either proteins that are produced or on localization of cell types.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐⭐)

Impact (⭐⭐⭐⭐⭐): Emerging viruses have plagued mankind for centuries with a concern of viruses in animals being able to be transmitted to humans, as occurred with Covid-19 causing a world-wide pandemic. Determining the mechanism by which viruses mutate to allow for species-to-species transmission is extremely important. This study looks at the mutations in the avian flu, H1N1 which has mutated and jumped to dairy cows and in a small number of cases to humans. The goal of the study was to identify what residues allowed for novel receptor binding to new species which, once identified, could potentially be used to limit virus spread.The ability to limit viral “jumping” from species to species is extremely important therefore these data have to potential to be of high impact. The paper would be improved if mutational studies were done to show that if the identified sites were blocked, transmission of the virus was limited.

Methods (⭐⭐⭐⭐☆): The authors examined sequences from different H1N1 viruses and using microarrays looked at receptor binding. Structure prediction tools were used to examine binding. These are all high quality standard methods. Adding actual work with the virus, mutated to lose some of the identified binding site, to show that they were no longer infective would add value to these studies. Perhaps this would be a good next paper.

Results (⭐⭐⭐⭐⭐): The main results from this study were that the H1N1 virus has been able to jump species by expanding the area on the receptor to which it binds. It has a binding pocket for preferential binding in birds, but that site is not available in mammals but sites outside the binding pocket have glycan binding sites that the virus has taken advantage of to allow for binding of these new hosts. This is a key virus behavior that allows for spread to new hosts as previous hosts die out or become immune.The structural data are elegant and give a clear picture of how the binding of H1N1 is altered in new hosts. Particularly the identification of the I199T residue stabilization of N248 and their role in H1N1 binding in the A/Texas/37/2024 variant that was identified in a farmworker in early 2024. These are the types of shifts that need to be identified and tracked in order to limit the spread of this virus in humans.

Discussion(⭐⭐⭐⭐☆): As we have discovered with Covid-19, worldwide pandemics are not something we want to live through ever again. Getting ahead of virus mutations that could jump from an animal species to humans is of vital importance to avoid this occurrence. One way to do that is to find out how the virus is mutating to avoid immune surveillance while the other way to do that is to find out how the virus is finding its way into the cell. Both are important. This study looks at the latter, how H1N1 finds a way into a new host cell when it previously had no way to bind. The data here show that H1N1 expands its binding out of the normal binding pocket by recognizing novel glycans. This information can allow for the development of therapies to limit this access and thus limit human infection by H1N1.

The authors should discuss the implications of virus jumping and their data in more detail.

This paper should be published but it will be great to see more studies on the effect of blocking the glycan interactions of these mutated H1N1 viruses.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years. She used to do structure work for protein protein interactions. Please see Sorgen et al 2004, J. Biol Chem. Structural changes in the carboxyl terminus of gap junction protein Cx43 etc etc etc (long title).

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐⭐)

Impact (⭐⭐⭐⭐⭐): Age related vision loss is one of the most profound and distressing occurrences in human aging. It leads to social isolation as people are no longer able to drive, increasing loneliness and isolation related signs of dementia. Previously, while it has been known that the retina was subject to aging, the mechanisms of retinal aging were poorly understood meaning that Here, the authors describe molecular pathways involved in retinal aging and identify a potential therapeutic target which, if future studies confirm, could lead to the development of a first in its kind therapy for millions of people. This paper has the potential to be very high impact as aging happens to all of us.

Methods (⭐⭐⭐⭐☆): The authors have done a series of experiments on mouse retinas that are well thought out and well described except, unless I somehow missed it, they never tell us what type of mice they used. This needs to be added in the methods section along with their IACUS protocol information. The age difference between the two groups was good but not extreme and yet they still see the reported changes suggesting a robust change in fatty acid metabolism starting somewhat early. Addition of an even later age group to see if they can still rescue the aging phenotype would be of interest, but not needed for this study. Limiting retinal aging was not possible.

Results (⭐⭐⭐⭐☆): The main result of the study was that 24:5n-3, a product of ELOVL2 (elongation of a very long-chain fatty acid 2) limited age related retinal decline. They get here through a series of steps showing that over time vision declines in mice and that this is associated with changes in fatty acids within the retinal itself rather than brain related degeneration. Using an ELOVL2 knockout mouse and replacement therapy for 24:5n-3 they convincingly show that 1) loss of LEOV2 leads to augmented retinal aging and 2) using 2:5n-3 therapeutically can reverse this loss.This study is only missing a later time point to see if 24:5n-3 rescue has to occur early or if there is a time point past which too much damage has been done and aging related degeneration is not reversable.

Discussion(⭐⭐⭐⭐⭐): This is a well thought out, well written paper with the potential for very high impact. Those of us that are so lucky will all age and our retinas will all undergo degenerative processes. The ability to forestall this degenerative process could add decades to our healthy vision. In a time when people are living longer and longer, the ability to see properly long past when our retinas normally would have begun to degrade would be life changing.

I would like to thank the authors for noting the shortcomings of their studies. More authors should be willing to do this.

I would be interested in seeing if the gap junctions in the retina are altered by 24:5n-3. They are key in retinal function and may play a role in retinal aging. This is just my personal interest and not needed for publication.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.

Overall Rating (⭐⭐⭐⭐☆)

Impact (⭐⭐⭐⭐☆): This paper reports on studies on the role of neurofibromin in the genesis of melanoma, particularly uveal melanoma. They also found that loss of neurofibromin leads to the formation of neurofibromatosis, tumors of the Schwann cells indicating a role for NF1 in cancers of the nervous system. The authors identified a specific driver of this, GNAQ, suggesting a mechanism for melanoma development and thus identifying a potential therapeutic target. This improved throughout the document.

The introduction needs more of a generalized background into melanoma and the genes need to be spelled out before using all of the three letter acronyms for them. NF1, for example, is never explained so unless you know the field you have a hard time figuring out where the authors are going. There are a number of run on sentences throughout the paper.

One note from the abstract and the introduction, the authors state that “In this paper we investigated….”, what I believe they mean is that “In these studies we investigated….” Papers do not investigate anything, papers report things. The abstract and introduction should be reworded.

Methods (⭐⭐⭐⭐⭐): Studies were done in a variety of mouse models to assess the loss of proteins of interest. Standard biochemical and protein assays were performed. The methods are all very standard. The methods were done well, and the staining results are clear. Some figures need better labels (see review "Results" section for specifics)

Results (⭐⭐⭐☆☆): The literature review and Cancer data base review should be moved to the Introduction. While interesting, they are not experimental results.

The description of the mice experiments should be in the methods, leaving just the results of the experiments in the results section.

The authors describe a number of interesting types of tumors in the mice indicating that loss of NF1 or gain of GNAQ leads to the development of a variety of tumor types, most notably dermal tumors, uveal tumors and tumors of the white matter around peripheral nerves (Schwann cells). RNAseq identified a number of interesting changes in the transcriptome of these tumors that may be of interest as therapeutic targets. The problem arises when you do not have 100% translational read-through though. To make this study more comprehensive, at least a few of those findings should have been checked at the protein level.

The figures need better and larger labels. For example, Figure 4 C left Y axis and Figure 5 D and E axes are tiny and there is plenty of room to make those bigger and easier to read..

Discussion(⭐⭐⭐⭐⭐): Overall, this paper is interesting and has merit. It gives information on how NF1 may be impacting melanoma formation. It is one more step in understanding cancer and cancer development which is important for developing therapies. Identifying GNAQ as having a key role in development of these cancers is novel, therefore the paper had the potential to be moderately high impact. The authors point out in their discussion the novel connection between the NF1 loss and muscle related genes and discuss the higher than normal rate of cancers in patients with muscular dystrophies. This is an interesting and potentially important connection that should be further investigated. Additional mechanistic information would be a great next step in these studies.

Knowing exactly what GNAQ is doing will allow for therapeutic development although that will take a lot of work and is not necessary

The writing ineeds to be cleaned up, the run on sentences need to be cut, and every time an acronym for something is first used, the whole name needs to be spelled out.

Reviewer Information The reviewer is the Chair of Biotechnology at the Franklin Cummings Technical Institute. Her PhD is in neuroscience, but her work is as a protein biochemist working on inflammation, signal transduction, and cell-cell communication. She has worked in both industry and academia for over 20 years.

Dr. Heather Duffy on ResearchHub: https://www.researchhub.com/user/1790894/

ResearchHub Peer Reviewer Statement: This peer review has been uploaded from ResearchHub as part of a paid peer review initiative. ResearchHub aims to accelerate the pace of scientific research using novel incentive structures.