eLife Assessment

This important study uses Mendelian Randomisation to show that early life phenotypes (i.e. onset of age at menarche and age at first birth) have an influence on a multitude of health outcomes later in life. The provided empirical evidence supporting the antagonistic pleiotropy theory is solid. However, some results seem improbable and need to be checked to make sure they are correct.

Reviewer #1 (Public review):

Summary:

The present study aims to associate reproduction with age-related disease as support of the antagonistic pleiotropy hypothesis of ageing predominantly using Mendelian Randomization. The authors found evidence that early-life reproductive succes is associated with advanced ageing.

Strengths:

Large sample size. Many analyses

Weaknesses:

Still a number of doubts with regard to some of the results and their interpretation.

Reviewer #2 (Public review):

Summary:

The authors present an interesting paper where they test the antagonistic pleiotropy theory. Based on this theory they hypothesize that genetic variants associated with later onset of age at menarche and age at first birth may have a positive effect on a multitude of health outcomes later in life, such as epigenetic aging and prevalence of chronic diseases. Using a mendelian randomization and colocalization approach, the authors show that SNPs associated with later age at menarche are associated with delayed aging measurements, such as slower epigenetic aging and reduced facial aging and a lower risk of chronic diseases, such as type 2 diabetes and hypertension. Moreover, they identify 128 fertility-related SNPs that associate with age-related outcomes and they identified BMI as a mediating factor for disease risk, discussing this finding in the context of evolutionary theory.

Strengths:

The major strength of this manuscript is that it addresses the antagonistic pleiotropy theory in aging. Aging theories are not frequently empirically tested although this is highly necessary. The work is therefore relevant for the aging field as well as beyond this field, as the antagonistic pleiotropy theory addresses the link between fitness (early life health and reproduction) and aging.

The authors addressed the remarks on the previous version very well. Addressing the two points below would further increase the quality of the manuscript.

(1) In the previous version the authors mentioned that their results are also consistent with the disposable soma theory: "These results are also consistent with the disposable soma theory that suggests aging as an outcome tradeoff between an organism's investment in reproduction and somatic maintenance and repair."

Although the antagonistic pleiotropy and disposable soma theories describe different mechanisms, both provide frameworks for understanding how genes linked to fertility influence health. The antagonistic pleiotropy theory posits that genes enhancing fertility early in life may have detrimental effects later. In contrast, the disposable soma theory suggests that energy allocation involves a trade-off, where investment in fertility comes at the expense of somatic maintenance, potentially leading to poorer health in later life.

To strengthen the manuscript, a discussion section should be added to clarify the overlap and distinctions between these two evolutionary theories and suggest directions for future research in disentangling their specific mechanisms.

(2) In response to the question why the authors did not include age at menopause in addition to the already included age at first child and age at menarche the following explanation was provided: "Our manuscript focuses on the antagonistic pleiotropy theory, which posits that inherent trade-off in natural selection, where genes beneficial for early survival and reproduction (like menarche and childbirth) may have costly consequences later. So, we only included age at menarche and age at first childbirth as exposures in our research."

It remains, however, unclear why genes beneficial for early survival and reproduction would be reflected only in age at menarche and age at first childbirth, but not in age at menopause. While age at menarche marks the onset of fertility, age at menopause signifies its end. Since evolutionary selection acts directly until reproduction is no longer possible (though indirect evolutionary pressures persist beyond this point), the inclusion of additional fertility-related measures could have strengthened the analysis. A more detailed justification for focusing exclusively on age at menarche and first childbirth would enhance the clarity and rigor of the manuscript.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

The present study aims to associate reproduction with age-related disease as support of the antagonistic pleiotropy hypothesis of ageing, predominantly using Mendelian Randomization. The authors found evidence that early-life reproductive success is associated with advanced ageing.

Strengths:

Large sample size. Many analyses.

Weaknesses:

There are some errors in the methodology, that require revisions.

In particular, the main conclusions drawn by the authors refer to the Mendelian Randomization analyses. However, the authors made a few errors here that need to be reconsidered:

(1) Many of the outcomes investigated by the authors are continuous outcomes, while the authors report odds ratios. This is not correct and should be revised.

Thank you for your observation. We have revised the manuscript to ensure that the results for continuous outcomes are appropriately reported using beta coefficients, which indicate the change in the outcome per unit increase in exposure. This will accurately reflect the nature of the analysis and provide a clearer interpretation of continuous outcomes (lines 56-109).

(2) Some of the odds ratios (for example the one for osteoporosis) are really small, while still reaching the level of statistical significance. After some checking, I found the GWAS data used to generate these MR estimates were processed by the program BOLT-LLM. This program is a linear mixed model program, which requires the transformation of the beta estimates to be useful for dichotomous outcomes. The authors should check the manual of BOLT-LLM and recalculate the beta estimates of the SNP-outcome associations prior to the Mendelian Randomization analyses. This should be checked for all outcomes as it doesn't apply to all.

Thank you for your detailed feedback. We have reviewed all the GWAS data used in our MR analyses and confirmed that all GWAS of continuous traits have already been processed using the BOLT-LMM, including age at menarche, age at first birth, BMI, frailty index, father's age at death, mother's age at death, DNA methylation GrimAge acceleration, age at menopause, eye age, and facial aging. Most of the dichotomous outcomes have not been processed by BOLT-LMM, including late-onset Alzheimer's disease, type 2 diabetes, chronic heart failure, essential hypertension, cirrhosis, chronic kidney disease, early onset chronic obstructive pulmonary disease, breast cancer, ovarian cancer, endometrial cancer, and cervical cancer, except osteoporosis. We have reprocessed the GWAS beta values of osteoporosis and re-conducted the MR analysis (lines 74-75; lines 366-373).

(3) The authors should follow the MR-Strobe guidelines for presentation.

Thank you for your suggestion to follow the MR-STROBE guidelines for the presentation of our study. We appreciate the importance of adhering to these standardized guidelines to ensure clarity and transparency in reporting Mendelian Randomization (MR) analyses. We confirm that the MR components of our research are structured and presented following the MR-STROBE checklist. In addition to the MR analyses, our study also integrates Colocalization analysis, Genetic correlation analysis, Ingenuity Pathway Analysis (IPA), and population validation to provide a more comprehensive understanding of the genetic and biological context. While these analyses are not strictly covered by MR-STROBE guidelines, they complement the MR results by offering additional validation and mechanistic insights.

We have structured our manuscript to separate these complementary analyses from the core MR results, maintaining alignment with MR-STROBE for the MR-specific components. The additional analyses are discussed in dedicated sections to highlight their unique contributions and avoid conflating them with the MR findings.

(4) The authors should report data in the text with a 95% confidence interval.

Thank you for your feedback. We have added the 95% confidence intervals for the reported data within the main text to enhance clarity and provide comprehensive context (lines 56-109). Additionally, the complete analysis data, including all detailed results, can be found in Table S3.

(5) The authors should consider correction for multiple testing

Thank you for your comment regarding the need to consider correction for multiple testing. We agree that correcting for multiple comparisons is an important step to control for the possibility of false-positive findings, particularly in studies involving large numbers of statistical tests. In our study, we carefully considered the issue of multiple testing and adopted the following approach:

Context of Multiple Testing: The tests we conducted were hypothesis-driven, focusing on specific relationships (e.g., genetic correlation, colocalization, and Mendelian Randomization). These analyses are based on priori hypotheses supported by existing literature or biological relevance.

Statistical Methods: Where applicable, we applied appropriate measures to account for multiple tests. For instance, in Mendelian Randomization, sensitivity analyses serve to validate the robustness of the results.

We believe that the methodology and corrections applied in our study appropriately address concerns about multiple testing, given the hypothesis-driven nature of our analyses and the rigorous steps taken to validate our findings. If you feel that additional corrections are required for specific parts of the analysis, we would be happy to further clarify or revise as needed.

Reviewer #2 (Public review):

Summary:

The authors present an interesting paper where they test the antagonistic pleiotropy theory. Based on this theory they hypothesize that genetic variants associated with later onset of age at menarche and age at first birth have a positive causal effect on a multitude of health outcomes later in life, such as epigenetic aging and prevalence of chronic diseases. Using a mendelian randomization and colocalization approach, the authors show that SNPs associated with later age at menarche are associated with delayed aging measurements, such as slower epigenetic aging and reduced facial aging, and a lower risk of chronic diseases, such as type 2 diabetes and hypertension. Moreover, they identified 128 fertility-related SNPs that are associated with age-related outcomes and they identified BMI as a mediating factor for disease risk, discussing this finding in the context of evolutionary theory.

Strengths:

The major strength of this manuscript is that it addresses the antagonistic pleiotropy theory in aging. Aging theories are not frequently empirically tested although this is highly necessary. The work is therefore relevant for the aging field as well as beyond this field, as the antagonistic pleiotropy theory addresses the link between fitness (early life health and reproduction) and aging.

Points that have to be clarified/addressed:

(1) The antagonistic pleiotropy is an evolutionary theory pointing to the possibility that mutations that are beneficial for fitness (early life health and reproduction) may be detrimental later in life. As it concerns an evolutionary process and the authors focus on contemporary data from a single generation, more context is necessary on how this theory is accurately testable. For example, why and how much natural variation is there for fitness outcomes in humans?

Thank you for these insightful questions. We appreciate the opportunity to clarify how we approach the testing of AP theory within a contemporary human cohort and address the evolutionary context and comparative considerations with the disposable soma theory.

We recognize that modern human populations experience selection pressures that differ from those in the past, which may affect how well certain genetic variants reflect historical fitness benefits. Nonetheless, the genetic variation present today still offers valuable insights into potential AP mechanisms through statistical associations in contemporary cohorts. We believe that AP can indeed be explored in current populations by examining genetic links between reproductive traits and age-related health outcomes. In our study, we investigate whether certain genetic variants linked to reproductive timing—such as age at menarche and age at first birth—also correlate with late-life health risks. By identifying SNPs associated with both early-life reproductive success and adverse aging outcomes, we aim to capture the evolutionary trade-offs that AP theory suggests.

Despite contemporary selection pressures that differ from historical conditions, there remains natural genetic variation in traits like reproductive timing and longevity in humans today. This diversity allows us to apply MR to test causal relationships between reproductive traits and aging outcomes, providing insights into potential AP mechanisms. Prior studies have demonstrated that reproductive behaviors exhibit significant heritability and have identified genetic loci associated with reproductive timing (1,2). This genetic variation facilitates causal inference in modern cohorts, despite environmental and healthcare advances that might modulate these associations (3). By leveraging genetic risk scores for reproductive timing, our study captures the necessary variability to assess potential AP effects, thus providing valuable insights into how evolutionary trade-offs may continue to influence human health outcomes.

How do genetic risk score distributions of the exposure data look like?

Thank you for your question. Our study is focused on Mendelian Randomization (MR) analysis, which aims to infer causal relationships between exposures and outcomes. While genetic risk scores (GRS) provide valuable insights at an individual level, they do not directly align with our study's objective, which is centered on population-level causal inference rather than individual-level genetic risk assessment. In MR, we use genetic variants as instrumental variables to determine the causal effect of an exposure on an outcome. GRS analysis typically focuses on summarizing an individual's risk based on multiple genetic variants, which is outside the scope of our current research. Therefore, we did not perform or analyze the distribution of genetic risk scores, as our primary goal was to understand broader causal relationships using established genetic instruments.

Also, how can the authors distinguish in their data between the antagonistic pleiotropy theory and the disposable soma theory, which considers a trade-off between investment in reproduction and somatic maintenance and can be used to derive similar hypotheses? There is just a very brief mention of the disposable soma theory in lines 196-198.

In our manuscript, we test AP theory specifically by examining genetic variants associated with reproductive timing and their association with age-related health risks in later life. MR and genetic risk scores allow us to assess these associations, directly testing the hypothesis that certain alleles enhancing reproductive success might have adverse effects on aging outcomes. This gene-centered approach aligns with AP’s premise of genetic trade-offs, enabling us to observe whether alleles associated with early-life reproductive traits correlate with increased risks of age-related diseases. Distinguishing from disposable soma theory, which would predict a general trade-off in energy allocation affecting somatic maintenance and not specific genetic effects, our data focuses on how certain alleles have differential impacts across life stages. Our findings thus support AP theory over disposable soma by highlighting the effects of specific genetic loci on both reproductive and aging phenotypes. However, future research could indeed explore the intersection of these theories, for example, by examining how resource allocation and genetic predispositions interact to influence longevity in various environmental contexts.

(2) The antagonistic pleiotropy theory, used to derive the hypothesis, does not necessarily distinguish between male and female fitness. Would the authors expect that their results extrapolate to males as well? And can they test that?

Emerging evidence suggests that early puberty in males is linked to adverse health outcomes, such as an increased risk of cardiovascular disease, type 2 diabetes, and hypertension in later life (4). A Mendelian randomization study also reported a genetic association between the timing of male puberty and reduced lifespan (5). These findings support the hypothesis that genetic variants associated with delayed reproductive timing in males might similarly confer health benefits or improved longevity, akin to the patterns observed in females. This would suggest that similar mechanisms of antagonistic pleiotropy could operate in males as well.

In our study, BMI was identified as a mediator between reproductive timing and disease risk. Given that BMI is a common risk factor for age-related diseases in both males and females (6-9), it is plausible that similar mechanisms involving BMI, reproductive timing, and disease risk could exist in males. This shared mediator points to the possibility that, while reproductive timelines may differ, the pathways through which these traits influence aging outcomes may be consistent across genders.

AP theory could potentially be tested in males, as the principles of the theory may extend to analogous reproductive traits in males, such as age at puberty and testosterone levels, which could similarly influence health outcomes later in life. However, as our current study focuses specifically on female reproductive traits, testing the AP theory in males is outside the scope of this work. We acknowledge the importance of exploring these mechanisms in males, and we hope that future research will address this by investigating male-specific reproductive traits and their relationship to aging and health outcomes.

(3) There is no statistical analyses section providing the exact equations that are tested. Hence it's not clear how many tests were performed and if correction for multiple testing is necessary. It is also not clear what type of analyses have been done and why they have been done. For example in the section starting at line 47, Odds Ratios are presented, indicating that logistic regression analyses have been performed. As it's not clear how the outcomes are defined (genotype or phenotype, cross-sectional or longitudinal, etc.) it's also not clear why logistic regression analysis was used for the analyses.

Thank you for your thoughtful comments regarding the statistical analyses and the clarification of methods and variables used in the study.

Statistical Analyses Section: We have included a detailed explanation of all statistical analyses in the Methods section (lines 291–408), specifying the rationale for the choice of methods, the variables analyzed, and their relationships. Additionally, we have provided the relevant equations or statistical models used where appropriate to ensure transparency.

Beta Values and Odds Ratios: In the Results section (starting at line 56), both Beta values and Odds Ratios are presented: Beta values were used for analyses of continuous outcomes to quantify the linear relationship between predictors and outcomes. Odds Ratios (ORs) were calculated for binary or categorical disease outcomes to describe the relative odds of an outcome given specific exposures or independent variables.

Validation and Regression Analyses: For further validation of the MR results, we conducted analyses using the UK Biobank dataset (starting at line 162). Logistic regression analysis was then employed for disease risk assessments involving categorical outcomes (e.g., diseased or not).

We hope that this clarifies the methods and their applicability to our study, as well as the rationale for the presentation of Beta values and Odds Ratios. If further details or refinements are required, we are happy to incorporate them.

(4) Mendelian Randomization is an important part of the analyses done in the manuscript. It is not clear to what extent the MR assumptions are met, how the assumptions were tested, and if/what sensitivity analyses are performed; e.g. reverse MR, biological knowledge of the studied traits, etc. Can the authors explain to what extent the genetic instruments represent their targets (applicable expression/protein levels) well?

Thank you for your insightful comments regarding the Mendelian Randomization (MR) analysis and the evaluation of its assumptions. Below, we provide additional clarification on how the MR assumptions were addressed, sensitivity analyses performed, and the representativeness of the genetic instruments (starting at line 314):

Relevance Assumption (Genetic instruments are associated with the exposure): “We identified single nucleotide polymorphisms (SNPs) associated with exposure datasets with p < 5 × 10^-8 (10,11). In this case, 249 SNPs and 67 SNPs were selected as eligible instrumental variables (IVs) for exposures of age at menarche and age at first birth, respectively. All selected SNPs for every exposure would be clumped to avoid the linkage disequilibrium (r² = 0.001 and kb = 10,000).” “During the harmonization process, we aligned the alleles to the human genome reference sequence and removed incompatible SNPs. Subsequent analyses were based on the merged exposure-outcome dataset. We calculated the F statistics to quantify the strength of IVs for each exposure with a threshold of F>10 (12).”

Independence Assumption (Genetic instruments are not associated with confounders, Genetic instruments affect the outcome only through the exposure): Then we identified whether there were potential confounders of IVs associated with the outcomes based on a database of human genotype-phenotype associations, PhenoScanner V2 (13,14) (http://www.phenoscanner.medschl.cam.ac.uk/), with a threshold of p < 1 × 10^-5. IVs associated with education, smoking, alcohol, activity, and other confounders related to outcomes would be excluded.

Sensitivity Analyses Performed: A pleiotropy test was used to check if the IVs influence the outcome through pathways other than the exposure of interest. A heterogeneity test was applied to ensure whether there is a variation in the causal effect estimates across different IVs. Significant heterogeneity test results indicate that some instruments are invalid or that the causal effect varies depending on the IVs used. MRPRESSO was applied to detect and correct potential outliers of IVs with NbDistribution = 10,000 and threshold p = 0.05. Outliers would be excluded for repeated analysis. The causal estimates were given as odds ratios (ORs) and 95% confidence intervals (CI). A leave-one-out analysis was conducted to ensure the robustness of the results by sequentially excluding each IV and confirming the direction and statistical significance of the remained remaining SNPs.

Supplemental post-GWAS analysis: Colocalization analysis (starting at line 356), Genetic correlation analysis (starting at line 366).

Our MR analysis adheres to the guidelines for causal inference in MR studies. By combining multiple sensitivity analyses and ensuring the quality of genetic instruments, we demonstrate that the results are robust and unlikely to be driven by confounding or pleiotropy.

(5) It is not clear what reference genome is used and if or what imputation panel is used. It is also not clear what QC steps are applied to the genotype data in order to construct the genetic instruments of MR.

Starting in line 314, the steps of SNPs selection were included in the Methods part. “We identified single nucleotide polymorphisms (SNPs) associated with exposure datasets with p < 5 × 10^-8 (10,11). In this case, 249 SNPs and 67 SNPs were selected as eligible instrumental variables (IVs) for exposures of age at menarche and age at first birth, respectively. All selected SNPs for every exposure would be clumped to avoid the linkage disequilibrium (r² = 0.001 and kb = 10,000). Then we identified whether there were potential confounders of IVs associated with the outcomes based on a database of human genotype-phenotype associations, PhenoScanner V2 (13,14) (http://www.phenoscanner.medschl.cam.ac.uk/), with a threshold of p < 1 × 10^-5. IVs associated with education, smoking, alcohol, activity, and other confounders related to outcomes would be excluded. During the harmonization process, we aligned the alleles to the human genome reference sequence and removed incompatible SNPs. Subsequent analyses were based on the merged exposure-outcome dataset. We calculated the F statistics to quantify the strength of IVs for each exposure with a threshold of F>10 (12). If the effect allele frequency (EAF) was missing in the primary dataset, EAF would be collected from dsSNP (https://www.ncbi.nlm.nih.gov/snp/) based on the population to calculate the F value.” The SNP numbers of exposures for each outcome and F statistics results were listed in supplemental table S2.

(6) A code availability statement is missing. It is understandable that data cannot always be shared, but code should be openly accessible.

We have added it to the manuscript (starting at line 410).

Reviewer #2 (Recommendations for the authors):

(1) The outcomes seem to be genotypes (lines 274-288). In MR, genotypes are used as an instrument, representing an exposure, which is then associated with an outcome that is typically observed and measured at a later moment in time than the predictors. If both exposure and outcome are genotypes it is not clear how this works in terms of causality; it would rather reflect a genetic correlation. One would expect the genotypes that function as instruments for the exposure to have a functional cascade of (age-related) effects, leading to an (age-related) outcome. From line 149 the outcomes seem to be phenotypes. Can the authors please clearly explain in each section what is analyzed, how the analyses were done, and why the analyses were done that way?

Thank you for your insightful comment. We understand the concern regarding the use of genotypes as both exposures and outcomes and the implications this has for interpreting causality versus genetic correlation. To clarify, in our study, the outcomes analyzed in the MR framework are indeed genotypes, starting from line 47. We use genotypes as instrumental variables for exposures, which are then linked to phenotypic outcomes observed at a later stage, in line with standard MR principles.

To improve the robustness of the MR results, we validated the genetic associations in the population with phenotype data from UK Biobank (lines 162-203), and the detailed methods were listed in lines 385-408.

(2) Overall, the English writing is good. However, some small errors slipped in. Please check the manuscript for small grammar mistakes like in sentences 10 (punctuation) and 33 (grammar).

Thank you for your feedback. We appreciate your careful review and attention to detail. We thoroughly rechecked the manuscript for any grammatical errors, including punctuation and sentence structure, especially in sentences 11 and 35 in revised manuscript, as suggested.

(3) There is currently no results and discussion section.

The manuscript was submitted as Short Reports article type with a combined Results and Discussion section. We have added the section title of Discussion.

(4) Why did the authors not include SNPs associated with age at menopausal onset? See for example: https://www.nature.com/articles/s41586-021-03779-7https://urldefense.com/v3/__https://www.nature.com/articles/s41586-021-03779-7__;!!HYjtAOY1tjP_!Kl_ZKCmWOQEnvEbl46TG0TuhlsxapwvFdAFfZJkMvz8z7XhX5VEA1cT8CVvNu8xrv9k679Kl0XTrxwSajUeiXWm04XP4$.

Thank you for your information. Our manuscript focuses on the antagonistic pleiotropy theory, which posits that inherent trade-off in natural selection, where genes beneficial for early survival and reproduction (like menarche and childbirth) may have costly consequences later. So, we only included age at menarche and age at first childbirth as exposures in our research.

(5) Can the authors include genetic correlations between menarche, age at first child, BMI, and preferably menopause?

Thank you for your suggestion. We acknowledge that including genetic correlations between age at menarche, age at first childbirth, BMI, and menopause can provide valuable context to our analysis. While our current MR study sets age at menarche and age at first childbirth as exposures and menopause as the outcome, and we have already included results that account for BMI-related SNPs before and after correction, we recognize the importance of assessing genetic correlations.

To address this, we calculated the genetic correlations between these traits to provide insight into their shared genetic architecture. This analysis helps clarify whether there is a significant genetic overlap between the two exposures and between exposure and outcome, which can inform and support the interpretation of our MR results. We appreciate your suggestion and include these calculations to enhance the robustness and comprehensiveness of our study. In the genetic correlations analysis, LDSC software was applied and the genetic correlation values for all pairwise comparisons among age at menarche, age at first birth, BMI, and age at menopause onset were calculated(15,16). The results are listed in Table S6.

(6) Line 39-40: that is not entirely true. There is also amounting evidence that socioeconomic factors cause earlier onset of menarche through stress-related mechanisms: https://doi.org/10.1016/j.annepidem.2010.08.006https://urldefense.com/v3/__https://doi.org/10.1016/j.annepidem.2010.08.006__;!!HYjtAOY1tjP_!Kl_ZKCmWOQEnvEbl46TG0TuhlsxapwvFdAFfZJkMvz8z7XhX5VEA1cT8CVvNu8xrv9k679Kl0XTrxwSajUeiXZ4vbX0y$

Thank you so much for your information. We changed it to “Considering reproductive events are partly regulated by genetic factors that can manifest the physiological outcome later in life”.

(7) Why did the authors choose to work with studies derived from IEU Open GWAS? as it is often does not contain the most recent and relevant GWAS for a specific trait.

We chose to work with studies derived from the IEU Open GWAS database after careful consideration of several sources, including the GWAS Catalog database and recently published GWAS papers. Our selection criteria focused on publicly available GWAS with large sample sizes and a higher number of SNPs to ensure robust analysis. For specific traits such as late-onset Alzheimer's disease and eye aging, we used GWAS data published in scientific articles to ensure that our research reflects the latest findings in the field.

(1) Barban, N. et al. Genome-wide analysis identifies 12 loci influencing human reproductive behavior. Nat Genet 48, 1462-1472 (2016). https://doi.org/10.1038/ng.3698

(2) Tropf, F. C. et al. Hidden heritability due to heterogeneity across seven populations. Nat Hum Behav 1, 757-765 (2017). https://doi.org/10.1038/s41562-017-0195-1

(3) Stearns, S. C., Byars, S. G., Govindaraju, D. R. & Ewbank, D. Measuring selection in contemporary human populations. Nat Rev Genet 11, 611-622 (2010). https://doi.org/10.1038/nrg2831

(4) Day, F. R., Elks, C. E., Murray, A., Ong, K. K. & Perry, J. R. Puberty timing associated with diabetes, cardiovascular disease and also diverse health outcomes in men and women: the UK Biobank study. Sci Rep 5, 11208 (2015). https://doi.org/10.1038/srep11208

(5) Hollis, B. et al. Genomic analysis of male puberty timing highlights shared genetic basis with hair colour and lifespan. Nat Commun 11, 1536 (2020). https://doi.org/10.1038/s41467-020-14451-5

(6) Field, A. E. et al. Impact of overweight on the risk of developing common chronic diseases during a 10-year period. Arch Intern Med 161, 1581-1586 (2001). https://doi.org/10.1001/archinte.161.13.1581

(7) Singh, G. M. et al. The age-specific quantitative effects of metabolic risk factors on cardiovascular diseases and diabetes: a pooled analysis. PLoS One 8, e65174 (2013). https://doi.org/10.1371/journal.pone.0065174

(8) Kivimaki, M. et al. Obesity and risk of diseases associated with hallmarks of cellular ageing: a multicohort study. Lancet Healthy Longev 5, e454-e463 (2024). https://doi.org/10.1016/S2666-7568(24)00087-4

(9) Kivimaki, M. et al. Body-mass index and risk of obesity-related complex multimorbidity: an observational multicohort study. Lancet Diabetes Endocrinol 10, 253-263 (2022). https://doi.org/10.1016/S2213-8587(22)00033-X

(10) Savage, J. E. et al. Genome-wide association meta-analysis in 269,867 individuals identifies new genetic and functional links to intelligence. Nat Genet 50, 912-919 (2018). https://doi.org/10.1038/s41588-018-0152-6

(11) Gao, X. et al. The bidirectional causal relationships of insomnia with five major psychiatric disorders: A Mendelian randomization study. Eur Psychiatry 60, 79-85 (2019). https://doi.org/10.1016/j.eurpsy.2019.05.004

(12) Burgess, S., Small, D. S. & Thompson, S. G. A review of instrumental variable estimators for Mendelian randomization. Stat Methods Med Res 26, 2333-2355 (2017). https://doi.org/10.1177/0962280215597579

(13) Staley, J. R. et al. PhenoScanner: a database of human genotype-phenotype associations. Bioinformatics 32, 3207-3209 (2016). https://doi.org/10.1093/bioinformatics/btw373

(14) Kamat, M. A. et al. PhenoScanner V2: an expanded tool for searching human genotype-phenotype associations. Bioinformatics 35, 4851-4853 (2019). https://doi.org/10.1093/bioinformatics/btz469

(15) Bulik-Sullivan, B. et al. An atlas of genetic correlations across human diseases and traits. Nat Genet 47, 1236-1241 (2015). https://doi.org/10.1038/ng.3406

(16) Bulik-Sullivan, B. K. et al. LD Score regression distinguishes confounding from polygenicity in genome-wide association studies. Nat Genet 47, 291-295 (2015). https://doi.org/10.1038/ng.3211

eLife Assessment

This important study provides a nuanced analysis of the impact of cues on cost/benefit decision-making deficits in male rats that could have translational relevance to many addictive disorders. The main findings are that cues paired with rewarded outcomes increase the proportion of risky outcomes, whereas risky choice is reduced when cues are paired with reward loss. The experimental data is convincing, but the computational analysis based on the optimisation of different Q-learning models is incomplete. The findings will be of interest to behavioural neuroscientists and clinicians with an interest in risk, decision making, and gambling disorders.

Reviewer #1 (Public review):

Summary:

Maladaptive decision-making is a trait commonly seen in gambling disorders. Salient cues can impact decision-making and drive gambling, though how cues affect decision-making isn't well understood. This manuscript describes the impact of cueing distinct outcomes of a validated rodent cost/benefit-making task based on the human Iowa Gambling Task. Comparing six task variants, the authors describe the effect of adding salient cues to wins (that scale with the size of win or the inverse), to every outcome regardless of loss or win, randomly to losses or wins, or to losses. Behavioral results reveal that cueing wins increased risky choices. By contrast, presenting the cues randomly or cueing the losses reduced risky choices. Risk-preferring animals of the uncued, randomly cued, and loss-cued tasks showed sensitivity to devaluation, whereas win-paired cued rats did not, suggesting cues blunt behavioral updating. Behavioral analyses were paired with computational modeling of initial acquisition which revealed that risky decision-making was related to reduced punishment learning. These data provide unique insight into how cues may bias behavior and drive gambling-related phenotypes.

Strengths:

The detailed analyses provide interesting insight into how cues impact complex decision-making. While there has been a great deal of work into the impact of cues on choice, few studies integrate multiple probabilistic outcomes. Complementing these data with computational parameters helps the reader to understand what may be driving these differences in behavior. The manuscript is well-written, clearly explaining the relevance of the results and potential future directions.

Weaknesses:

Two main questions arise from these results. The first - when do behavioral differences emerge between the task variants? Based on the results and discussion, the cues increase the salience of either the wins or the losses, biasing behavior in favor of either risky or optimal choice. If this is the case, one might expect the cues to expedite learning, particularly in the standard and loss condition. Providing an analysis of the acquisition of the tasks may provide insight into how the cues are "teaching" decision-making and might explain how biases are formed and cemented.

The second question is - does the learning period used for the modeling impact the interpretation of the behavioral results? The authors indicate that computational modeling was done on the first five sessions and used these data to predict preferences at baseline. Based on these results, punishment learning predicts choice preference. However, these animals are not naïve to the contingencies because of the forced choice training prior to the task, which may impact behavior in these early sessions. Though punishment learning may initially predict risk preference, other parameters later in training may also predict behavior at baseline. The authors also present simulated data from the models for sessions 18-20, but according to the statistical analysis section, sessions 35-40 were used for analysis (and presumably presented in Figure 1). If the simulation is carried out in sessions 35-40, do the models fit the data? Finally, though the n's are small, it would be interesting to see how the devaluation impacts computational metrics. These additional analyses may help to explain the nuanced effects of the cues in the task variants.

Reviewer #2 (Public review):

Summary:

The manuscript by Hathaway et al. describes a set of elegant behavioral experiments designed to understand which aspects of cue-reward contingencies drive risky choice behavior. The authors developed several clever variants of the well-established rodent gambling task (also developed by this group) to understand how audiovisual cues alter learning, choice behavior, and risk. Computational and sophisticated statistical approaches were used to provide evidence that: (1) audiovisual cues drive risky choice if they are paired with rewards and decrease risk if only paired with loss, (2) pairing cues with rewards reduces learning from punishment, and (3) differences in risk-taking seem to be present early on in training.

Strengths:

The paper is well-written, the experiments are well-designed, and the results are highly interesting, particularly for understanding how cues can motivate and invigorate normal and abnormal behavior.

Weaknesses:

Additional support and evidence are needed for the claims made by the authors. Some of the statements are inconsistent with the data and/or analyses or are only weakly supportive of the claims.

Reviewer #3 (Public review):

Summary:

In this work, Hathaway and colleagues aim to understand how audiovisual cues at the time of outcome promote the selection of risky choices. A real-life illustration of this effect is used in electronic gambling machines which signal a win with flashing lights and jingles, encouraging the player to keep betting. More specifically, the authors ask whether the cue has to be paired exclusively to wins, or whether it can be paired to both outcomes, or exclusively loss outcomes, or occur randomly. To tackle this question, they employ a version of the Iowa Gambling Task adapted to rats, and test the effect of different rules of cue-outcome associations on the probability of selecting the riskier options; they then test the effect of prior reward devaluation on the task; finally, the optimised computational models on the early phases of the experiment to investigate potential mechanisms underlying the behavioural differences.

Strengths:

The experimental approach is very well thought-out, in particular, the choice of the different task variants covers a wide range of different potential hypotheses. Using this approach, they find that, although rats prefer the optimal choices, there is a shift towards selecting riskier options in the variants of the task where the cue is paired to win outcomes. They analyse this population average shift by showing that there is a concurrent increase in the number of risk-taking individuals in these tasks. They also make the novel discovery that pairing cues with loss outcomes only reduces the tendency for risky decisions.

The computational strategy is appropriate and in keeping with the accepted state of the art: defining a set of candidate models, optimising them, comparing them, simulating the best ones to ensure they replicate the main experimental results, then analysing parameter estimates in the different tasks to speculate about potential mechanisms.

Weaknesses:

There is a very problematic statistical stratagem that involves categorising individuals as either risky or optimal based on their choice probabilities. As a measurement or outcome, this is fine, as previously highlighted in the results, but this label is then used as a factor in different ANOVAs to analyse the very same choice probabilities, which then constitutes a circular argument (individuals categorised as risky because they make more risky choices, make more risky choices...).

A second experiment was done to study the effect of devaluation on risky choices in the different tasks. The results, which are not very clear to understand from Figure 3, would suggest that reward devaluation affects choices in tasks where the win-cue pairing is not present. The authors interpret this result by saying that pairing wins with cues makes the individuals insensitive to reward devaluation. Counter this, if an individual is prone to making risky choices in a given task, this points to an already distorted sense of value as the most rewarding strategy is to make optimal non-risky choices.

While the overall computational approach is excellent, I believe that the choice of computational models is poor. Loss trials come at a double cost, something the authors might want to elaborate more upon, firstly the lost opportunity of not having selected a winning option which is reflected in Q-learning by the fact that r=0, and secondly a waiting period which will affect the overall reward rate. The authors choose to combine these costs by attempting to convert the time penalty into "reward currency" using three different functions that make up the three different tested models. This is a bit of a wasted opportunity as the question when comparing models is not something like "are individuals in the paired win-cue tasks more sensitive to risk? or less sensitive to time? etc" but "what is the best way of converting time into Q-value currency to fit the data?" Instead, the authors could have contrasted other models that explicitly track time as a separate variable (see for example "Impulsivity and risk-seeking as Bayesian inference under dopaminergic control" (Mikhael & Gershman 2021)) or give actions an extra risk bonus (as in "Nicotinic receptors in the VTA promote uncertainty seeking" (Naude et al 2016)). Another weakness of the computational section is the fact, that despite simulations having been made, figure 5 only shows the simulated risk scores and not the different choice probabilities which would be a much more interesting metric by which to judge model validity. In the last section, the authors ask whether the parameter estimates (obtained from optimisation on the early sessions) could be used to predict risk preference. While this is an interesting question to address, the authors give very little explanation as to how they establish any predictive relationship. A figure and more detailed explanation would have been warranted to support their claims.

Author response:

We thank the reviewers for their thoughtful comments and suggestions. We plan to make a number of revisions to the manuscript to address their feedback.

Firstly, we plan to incorporate feedback related to our modeling approach. We will provide justification for the chosen models and why this dataset is not appropriate for an in-depth exploration of other models. In particular, we will highlight that the models included in this manuscript were taken from Langdon et al. (2019) with a minor extension. Model development and validation in the Langdon et al. (2019) paper required a dataset with >100 rats per task. As the current n per variant is 28-32, and behavioral performance on this task is highly variable, it would be difficult to sufficiently test the validity of models that majorly depart from the previously tested RL models. Nevertheless, we will acknowledge this as a limitation in the discussion section. Additionally, we will test some alternatives suggested by reviewers that fall within the scope of the current RL modeling framework (e.g., comparison to a standard delta-rule update for unrewarded choices). We will address other concerns brought up by reviewers by a.) providing a rationale for why we constrained our analyses to the first five sessions, b.) simulating data for sessions that match those that were analyzed in the real data (i.e., sessions 35-40 instead of 18-20), and c.) including a figure of the simulated choice probabilities rather than just risk score.

Secondly, we will include additional analyses and clarify the current statistical approach to address comments on how the data were analyzed. We will include an analysis of task acquisition to investigate when choice preferences emerge across the different variants. We will justify the statistical approach used for detecting behavioral differences between task variants, including a better explanation of the inclusion of the risky/optimal label as a between-subjects factor in the ANOVAs. We will also expand the section on parameters predicting risk preference on the rGT to fully explain the statistical method used and provide a figure of the results.

Lastly, we will provide a more detailed rationale for the reinforcer devaluation test, and describe the hypothesis it tests. We will also expand on how the results from the devaluation test support our conclusions, and address alternative explanations suggested by the reviewers.

eLife Assessment

This work presents an atlas of vasopressin (AVP) and its receptor AVPR1a in mouse brains using RNAscope to map single transcript expressions of Avp and Avpr1a across various brain regions in males and females. The findings are valuable in that they identify brain regions expressing Avpr1a mRNA transcript. The impact of findings is decreased by incomplete analysis of the data due to limited description of Avpr1a mRNA distribution within brain regions and limited statistical inference.

Reviewer #1 (Public review):

Summary:

Despite accumulating prior studies on the expressions of AVP and AVPR1a in the brain, a detailed, gender-specific mapping of AVP/AVPR1a neuronal nodes has been lacking. Using RNAscope, a cutting-edge technology that detects single RNA transcripts, the authors created a comprehensive neuroanatomical atlas of Avp and Avpr1a in male and female brains. The findings are important, given that: (1) a detailed, gender-specific mapping of AVP/AVPR1a neuronal nodes has been lacking, and (2) the study offers valuable new insights into Avpr1a expression across the mouse brain. The findings are solid, and with improved data presentation and analysis, this work could serve as an important resource for the neuroscience community.

Strengths:

This well-executed study provides valuable new insights into gender differences in the distribution of Avp and Avpr1a. The atlas is an important resource for the neuroscience community.

Weaknesses:

A few concerns remain to be addressed. The primary weakness of this manuscript lies in the robustness of its data presentation and analysis.

Reviewer #2 (Public review):

Summary:

The authors conducted a brain-wide survey of vasopressin and vasopressin receptor 1A gene expression in the mouse brain using a high-resolution in situ hybridization method called RNAscope. Overall, the findings are useful in identifying brain regions expressing Avpr1a transcript. The impact of findings is decreased by incomplete or inadequate data analysis due to limited description of Avpr1a mRNA distribution within brain regions and limited statistical inference. A comprehensive overview of Avpr1a expression in the mouse brain has the potential to be highly informative and impactful. The current manuscript used RNAscope (a proprietary method of in situ hybridization) to assess the transcript abundance of Avp (arginine vasopressin, a neuropeptide) and its receptor (Avpr1a). The style of graphs, limited use of photomicrographs, and low number of subjects all combine to limit the impact of the dataset. The finding of Avp-expressing cells outside of the hypothalamus and extended amygdala is poorly documented but would be novel. The Avpr1a data suggest expression in numerous brain regions. However, the data presented are difficult to interpret, with every value being an extremely small density value for a large swath of the brain. How many cells are impacted? Are puncta spread across many cells or only present in a few cells? Is density evenly distributed through a brain region or compacted into a subfield? For a descriptive study, there is minimal statistical inference and relatively little description. The authors make a case for the novel nature of the work but do not seem, at times, to recognize a robust literature developed over the last 50 years. In conclusion, the experimental data are important and informative; however, the low number of subjects, lack of statistical power, limited description of individual brain regions, and poor quality and design of data figures reduce the overall impact.

Strengths:

A survey of Avpr1a expression in the mouse brain is an important tool for exploring the function of vasopressin in the mammalian brain and developing hypotheses about cell - and circuit-level function.

Weaknesses:

(1) The style and type of data presentation, focusing on the density of individual mRNA transcript across a whole brain region, seemed incomplete in so far as the data presentation did not provide a clear visualization of the distribution of Avpr1a-expressing cells or transcript itself. However, knowing which brain regions do express transcript is itself informative.

(2) The manuscript strongly emphases on the possibility of sex differences in Avp and Avpr1a expression. However, the low number of animals used does not provide adequate statistical power to make strong inferences regarding sex differences in the data.

(3) The manuscript's methods are minimal but adequate to understand data acquisition. The description of how quantitative analyses were conducted is inadequate and would be impossible to replicate beyond identifying the program used.

eLife Assessment

This valuable study investigates the computational role of top-down feedback -- a property that is found in biological circuits -- in Artificial Neural Network (ANN) models of the neocortex. Using hierarchical recurrent ANNs in an audiovisual integration task, the authors show a visual bias consistent with that observed in human perception, which mildly improves learning speed. While the study offers a tool that is of value for studying top-down feedback in cortical models, with the potential to inspire other fields (e.g. machine learning), the presented evidence for a general framework of deep learning architectures that predict behavior is incomplete, and the methods section lacks sufficient detail in terms of hyperparameter choice and network structures.

Reviewer #1 (Public review):

Summary:

Here, the authors aim to investigate the potential improvements of ANNs when used to explain brain data using top-down feedback connections found in the neocortex. To do so, they use a retinotopic and tonotopic organization to model each subregion of the ventral visual (V1, V2, V4, and IT) and ventral auditory (A1, Belt, A4) regions using Convolutional Gated Recurrent Units. The top-down feedback connections are inspired by the apical tree of pyramidal neurons, modeled either with a multiplicative effect (change of gain of the activation function) or a composite effect (change of gain and threshold of the activation function).

To assess the functional impact of the top-down connections, the authors compare three architectures: a brain-like architecture derived directly from brain data analysis, a reversed architecture where all feedforward connections become feedback connections and vice versa, and a random connectivity architecture. More specifically, in the brain-like model the visual regions provide feedforward input to all auditory areas, whereas auditory areas provide feedback to visual regions.

First, the authors found that top-down feedback influences audiovisual processing and that the brain-like model exhibits a visual bias in multimodal visual and auditory tasks. Second, they discovered that in the brain-like model, the composite integration of top-down feedback, similar to that found in the neocortex, leads to an inductive bias toward visual stimuli, which is not observed in the feedforward-only model. Furthermore, the authors found that the brain-like model learns to utilize relevant stimuli more quickly while ignoring distractors. Finally, by analyzing the activations of all hidden layers (brain regions), they found that the feedforward and feedback connectivity of a region could determine its functional specializations during the given tasks.

Strengths:

The study introduces a novel methodology for designing connectivity between regions in deep learning models. The authors also employ several tasks based on audiovisual stimuli to support their conclusions. Additionally, the model utilizes backpropagation of error as a learning algorithm, making it applicable across a range of tasks, from various supervised learning scenarios to reinforcement learning agents. Conversely, the presented framework offers a valuable tool for studying top-down feedback connections in cortical models. Thus, it is a very nice study that also can give inspiration to other fields (machine learning) to start exploring new architectures.

Weaknesses:

Although the study explores some novel ideas on how to study the feedback connections of the neocortex, the data presented here are not complete in order to propose a concrete theory of the role of top-down feedback inputs in such models of the brain.

(1) The gap in the literature that the paper tries to fill in the ability of DL algorithms to predict behavior: "However, there are still significant gaps in most deep neural networks' ability to predict behavior, particularly when presented with ambiguous, challenging stimuli." and "[...] to accurately model the brain."

It is unclear to me how the presented work addresses this gap, as the only facts provided are derived from a simple categorization task that could also be solved by the feedforward-only model (see Figures 4 and 5). In my opinion, this statement is somewhat far-fetched, and there is insufficient data throughout the manuscript to support this claim.

(2) It is not clear what the advantages are between the brain-like model and a feedforward-only model in terms of performance in solving the task. Given Figures 4 and 5, it is evident that the feedforward-only model reaches almost the same performance as the brain-like model (when the latter uses the modulatory feedback with the composite function) on almost all tasks tested. The speed of learning is nearly the same: for some tested tasks the brain-like model learns faster, while for others it learns slower. Thus, it is hard to attribute a functional implication to the feedback connections given the presented figures and therefore the strong claims in the Discussion should be rephrased or toned down.

(3) The Methods section lacks sufficient detail. There is no explanation provided for the choice of hyperparameters nor for the structure of the networks (number of trainable parameters, number of nodes per layer, etc). Clarifying the rationale behind these decisions would enhance understanding. Moreover, since the authors draw conclusions based on the performance of the networks on specific tasks, it is unclear whether the comparisons are fair, particularly concerning the number of trainable parameters. Furthermore, it is not clear if the visual bias observed in the brain-like model is an emerging property of the network or has been created because of the asymmetries in the visual vs. auditory pathway (size of the layer, number of layers, etc).

Reviewer #2 (Public review):

Summary:

This work addresses the question of whether artificial deep neural network models of the brain could be improved by incorporating top-down feedback, inspired by the architecture of the neocortex.

In line with known biological features of cortical top-down feedback, the authors model such feedback connections with both, a typical driving effect and a purely modulatory effect on the activation of units in the network.

To assess the functional impact of these top-down connections, they compare different architectures of feedforward and feedback connections in a model that mimics the ventral visual and auditory pathways in the cortex on an audiovisual integration task.

Notably, one architecture is inspired by human anatomical data, where higher visual and auditory layers possess modulatory top-down connections to all lower-level layers of the same modality, and visual areas provide feedforward input to auditory layers, whereas auditory areas provide modulatory feedback to visual areas.

First, the authors find that this brain-like architecture imparts the models with a light visual bias similar to what is seen in human data, which is the opposite in a reversed architecture, where auditory areas provide a feedforward drive to the visual areas.

Second, they find that, in their model, modulatory feedback should be complemented by a driving component to enable effective audiovisual integration, similar to what is observed in neural data.

Last, they find that the brain-like architecture with modulatory feedback learns a bit faster in some audiovisual switching tasks compared to a feedforward-only model.

Overall, the study shows some possible functional implications when adding feedback connections in a deep artificial neural network that mimics some functional aspects of visual perception in humans.

Strengths:

The study contains innovative ideas, such as incorporating an anatomically inspired architecture into a deep ANN, and comparing its impact on a relevant task to alternative architectures.

Moreover, the simplicity of the model allows it to draw conclusions on how features of the architecture and functional aspects of the top-down feedback affect the performance of the network.

This could be a helpful resource for future studies of the impact of top-down connections in deep artificial neural network models of the neocortex.

Weaknesses:

Overall, the study appears to be a bit premature, as several parts need to be worked out more to support the claims of the paper and to increase its impact.

First, the functional implication of modulatory feedback is not really clear. The "only feedforward" model (is a drive-only model meant?) attains the same performance as the composite model (with modulatory feedback) on virtually all tasks tested, it just takes a bit longer to learn for some tasks, but then is also faster at others. It even reproduces the visual bias on the audiovisual switching task. Therefore, the claims "Altogether, our results demonstrate that the distinction between feedforward and feedback inputs has clear computational implications, and that ANN models of the brain should therefore consider top-down feedback as an important biological feature." and "More broadly, our work supports the conclusion that both the cellular neurophysiology and structure of feed-back inputs have critical functional implications that need to be considered by computational models of brain function" are not sufficiently supported by the results of the study. Moreover, the latter points would require showing that this model describes neural data better, e.g., by comparing representations in the model with and without top-down feedback to recorded neural activity.

Second, the analyses are not supported by supplementary material, hence it is difficult to evaluate parts of the claims. For example, it would be helpful to investigate the impact of the process time after which the output is taken for evaluation of the model. This is especially important because in recurrent and feedback models the convergence should be checked, and if the network does not converge, then it should be discussed why at which point in time the network is evaluated.

Third, the descriptions of the models in the methods are hard to understand, i.e., parameters are not described and equations are explained by referring to multiple other studies. Since the implications of the results heavily rely on the model, a more detailed description of the model seems necessary.

Lastly, the discussion and testable predictions are not very well worked out and need more details. For example, the point "This represents another testable prediction flowing from our study, which could be studied in humans by examining the optical flow (Pines et al., 2023) between auditory and visual regions during an audiovisual task" needs to be made more precise to be useful as a prediction. What did the model predict in terms of "optic flow", how can modulatory from simple driving effect be distinguished, etc.

Reviewer #3 (Public review):

Summary:

This study investigates the computational role of top-down feedback in artificial neural networks (ANNs), a feature that is prevalent in the brain but largely absent in standard ANN architectures. The authors construct hierarchical recurrent ANN models that incorporate key properties of top-down feedback in the neocortex. Using these models in an audiovisual integration task, they find that hierarchical structures introduce a mild visual bias, akin to that observed in human perception, not always compromising task performance.

Strengths:

The study investigates a relevant and current topic of considering top-down feedback in deep neural networks. In designing their brain-like model, they use neurophysiological data, such as externopyramidisation and hierarchical connectivity. Their brain-like model exhibits a visual bias that qualitatively matches human perception.

Weaknesses:

While the model is brain-inspired, it has limited bioplausibility. The model assumes a simplified and fixed hierarchy. In the brain with additional neuromodulation, the hierarchy could be more flexible and more task-dependent.

While the brain-like model showed an advantage in ignoring distracting auditory inputs, it struggled when visual information had to be ignored. This suggests that its rigid bias toward visual processing could make it less adaptive in tasks requiring flexible multimodal integration. It hence does not necessarily constitute an improvement over existing ANNs. It is unclear, whether this aspect of the model also matches human data. In general, there is no direct comparison to human data. The study does not evaluate whether the top-down feedback architecture scales well to more complex problems or larger datasets. The model is not well enough specified in the methods and some definitions are missing.

eLife Assessment

This valuable study builds on previous work by the authors by presenting a potentially key method for correcting optical aberrations in GRIN lens-based microendoscopes used for imaging deep brain regions. By combining simulations and experiments, the authors provide convincing evidence showing that the obtained field of view is significantly increased with corrected, versus uncorrected microendoscopes. Because the approach described in this paper does not require any microscope or software modifications, it can be readily adopted by neuroscientists who wish to image neuronal activity deep in the brain.

Reviewer #1 (Public review):

Summary:

Sattin, Nardin, and colleagues designed and evaluated corrective microlenses that increase the useable field of view of two long (>6mm) thin (500 um diameter) GRIN lenses used in deep-tissue two-photon imaging. This paper closely follows the thread of earlier work from the same group (esp. Antonini et al, 2020; eLife), filling out the quiver of available extended-field-of-view 2P endoscopes with these longer lenses. The lenses are made by a molding process that appears practical and easy to adopt with conventional two-photon microscopes.

Simulations are used to motivate the benefits of extended field of view, demonstrating that more cells can be recorded, with less mixing of signals in extracted traces, when recorded with higher optical resolution. In vivo tests were performed in piriform cortex, which is difficult to access, especially in chronic preparations.

The design, characterization, and simulations are clear and thorough, but they do not break new ground in optical design or biological application. However, the approach shows much promise, including for applications such as miniaturized GRIN-based microscopes. Readers will largely be interested in this work for practical reasons: to apply the authors' corrected endoscopes to their own research.

Strengths:

The text is clearly written, the ex vivo analysis is thorough and well supported, and the figures are clear. The authors achieved their aims, as evidenced by the images presented, and were able to make measurements from large numbers of cells simultaneously in vivo in a difficult preparation.

The authors did a good job of addressing issues I raised in initial review, including analyses of chromaticity and the axial field of view, descriptions of manufacturing and assembly yield, explanations in the text of differences between ex vivo and in vivo imaging conditions, and basic analysis of the in vivo recordings relative to odor presentations. They have also shortened the text, reduced repetition, and better motivated their approach in the introduction.

Reviewer #2 (Public review):

In this manuscript, the authors present an approach to correct GRIN lens aberrations, which primarily cause a decrease in signal-to-noise ratio (SNR), particularly in the lateral regions of the field-of-view (FOV), thereby limiting the usable FOV. The authors propose to mitigate these aberrations by designing and fabricating aspherical corrective lenses using ray trace simulations and two-photon lithography, respectively; the corrective lenses are then mounted on the back aperture of the GRIN lens.

This approach was previously demonstrated by the same lab for GRIN lenses shorter than 4.1 mm (Antonini et al., eLife, 2020). In the current work, the authors extend their method to a new class of GRIN lenses with lengths exceeding 6 mm, enabling access to deeper brain regions as most ventral region of the mouse brain. Specifically, they designed and characterized corrective lenses for GRIN lenses measuring 6.4 mm and 8.8 mm in length. Finally, they applied these corrected long micro-endoscopes to perform high-precision calcium signal recordings in the olfactory cortex.

Compared with alternative approaches using adaptive optics, the main strength of this method is that it does not require hardware or software modifications, nor does it limit the system's temporal resolution. The manuscript is well-written, the data are clearly presented, and the experiments convincingly demonstrate the advantages of the corrective lenses.

The implementation of these long corrected micro-endoscopes, demonstrated here for deep imaging in the mouse olfactory bulb, will also enable deep imaging in larger mammals such as rats or marmosets.

Comments on revisions:

The authors have clearly addressed all my comments.

Reviewer #3 (Public review):

Summary:

This work presents the development, characterization and use of new thin microendoscopes (500µm diameter) whose accessible field of view has been extended by the addition of a corrective optical element glued to the entrance face. Two microendoscopes of different lengths (6.4mm and 8.8mm) have been developed, allowing imaging of neuronal activity in brain regions >4mm deep. An alternative solution to increase the field of view could be to add an adaptive optics loop to the microscope to correct the aberrations of the GRIN lens. The solution presented in this paper does not require any modification of the optical microscope and can therefore be easily accessible to any neuroscience laboratory performing optical imaging of neuronal activity.

Strengths:

(1) The paper is generally clear and well written. The scientific approach is well structured, and numerous experiments and simulations are presented to evaluate the performance of corrected microendoscopes. In particular, we can highlight several consistent and convincing pieces of evidence for the improved performance of corrected microendoscopes:

- PSFs measured with corrected microendoscopes 75µm from the centre of the FOV show a significant reduction in optical aberrations compared to PSFs measured with uncorrected microendoscopes.

- Morphological imaging of fixed brain slices shows that optical resolution is maintained over a larger field of view with corrected microendoscopes compared to uncorrected ones, allowing neuronal processes to be revealed even close to the edge of the FOV.

- Using synthetic calcium data, the authors showed that the signals obtained with the corrected microendoscopes have a significantly stronger correlation with the ground truth signals than those obtained with uncorrected microendoscopes.

(2) There is a strong need for high quality microendoscopes to image deep brain regions in vivo. The solution proposed by the authors is simple, efficient and potentially easy to disseminate within the neuroscience community.

Weaknesses:

Weaknesses that were present in the first version of the paper were carefully addressed by the authors.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1: 

(1) As discussed in review and nicely simulated by the authors, the large figure error indicated by profilometry (~10 um in some cases on average) is inconsistent with the optical performance improvements observed, suggesting that those measurements are inaccurate.

I see no reason to include these inaccurate measurements.  

We agree with the Referee and removed the indicated figure (old Supplementary Fig. 4) and data.

Reviewer #3:

(1) It would be interesting to comment on how the addition of a coverslip changes the performance of the uncorrected microendoscope compared to the use of bare grin lenses. 

We modified the discussion section (page 18) and added a new reference (#36) to include the request of the Referee.

(2) In Figure 6C-H, the authors can indeed show data corresponding to all detected cells, but I still think that the statistics should be calculated using the same effective FOV. 

We modified Figure 6 legend to include the request of the Referee.

(3) Authors could present the images in Figures 4-6 as in the original version, with a scale bar in the centre of the FOV that is different for the two types of objectives (corrected vs uncorrected). They could add a short justification for this choice, and perhaps present the other version for Figure 4 in a supplementary information sheet (with similar scale bars at the centre of the FOV for both types of objectives). It would allow readers to appreciate that the FOV still appears significantly enlarged with this other presentation.

As requested by the Referee, we modified the text in the Result section (page 11) and added the additional version of Figure 4 as Figure 4-figure supplement 1.

eLife Assessment

This study presents potentially valuable insights into the role of climbing fibers in cerebellar learning. The main claim is that climbing fiber activity is necessary for optokinetic reflex adaptation, but is dispensable for its long-term consolidation. There is evidence to support the first part of this claim, though it requires a clearer demonstration of the penetrance and selectivity of the manipulation. However, support for the latter part of the claim is incomplete owing to methodological concerns, including the robustness of the CF marking and manipulation approach and the unclear efficacy of longer-duration climbing fiber activity suppression.

Reviewer #1 (Public Review):

Summary:

The study by Seo et al highlights knowledge gaps regarding the role of cerebellar complex spike (CS) activity during different phases of learning related to optokinetic reflex (OKR) in mice. The novelty of the approach is twofold: first, specifically perturbing the activity of climbing fibers (CFs) in the flocculus (as opposed to disrupting communication between the inferior olive (IO) and its cerebellar targets globally); and second, examining whether disruption of the CS activity during the putative "consolidation phase" following training affects OKR performance.

The first part of the results provides adequate evidence supporting the notion that optogenetic disruption of normal CF-Purkinje neuron (PN) signaling results in the degradation of OKR performance. As no effects are seen in OKR performance in animals subjected to optogenetic irradiation during the memory consolidation or retrieval phases, the authors conclude that CF function is not essential beyond memory acquisition. However, the manuscript does not provide a sufficiently solid demonstration that their long-term activity manipulation of CF activity is effective, thus undermining the confidence of the conclusions.

Strengths:

The main strength of the work is the aim to examine the specific involvement of the CF activity in the flocculus during distinct phases of learning. This is a challenging goal, due to the technical challenges related to the anatomical location of the flocculus as well as the IO. These obstacles are counterbalanced by the use of a well-established and easy-to-analyse behavioral model (OKR), that can lead to fundamental insights regarding the long-term cerebellar learning process.

Weaknesses:

The impact of the work is diminished by several methodological shortcomings.

Most importantly, the key finding that prolonged optogenetic inhibition of CFs (for 30 min to 6 hours after the training period) must be complemented by the demonstration that the manipulation maintains its efficacy. In its current form, the authors only show inhibition by short-term optogenetic irradiation in the context of electrical-stimulation-evoked CSs in an ex vivo preparation. As the inhibitory effect of even the eNpHR3.0 is greatly diminished during seconds-long stimulations (especially when using the yellow laser as is done in this work (see Zhang, Chuanqiang, et al. "Optimized photo-stimulation of halorhodopsin for long-term neuronal inhibition." BMC biology 17.1 (2019): 1-17. ), we remain skeptical of the extent of inhibition during the long manipulations. In short, without a demonstration of effective inhibition throughout the putative consolidation phase (for example by showing a significant decrease in CS frequency throughout the irradiation period), the main claim of the manuscript of phase-specific involvement of CF activity in OKR learning can not be considered to be based on evidence.

Second, the choice of viral targeting strategy leaves gaps in the argument for CF-specific mechanisms. CaMKII promoters are not selective for the IO neurons, and even the most precise viral injections always lead to the transfection of neurons in the surrounding brainstem, many of which project to the cerebellar cortex in the form of mossy fibers (MF). Figure 1Bii shows sparsely-labelled CFs in the flocculus, but possibly also MFs. While obtaining homogenous and strong labeling in all floccular CFs might be impossible, at the very least the authors should demonstrate that their optogenetic manipulation does not affect simple spiking in PNs.

Finally, while the paper explicitly focuses on the effects of CF-evoked complex spikes in the PNs and not, for example, on those mediated by molecular layer interneurons or via direct interaction of the CF with vestibular nuclear neurons, it would be best if these other dimensions of CF involvement in cerebellar learning were candidly discussed.

Reviewer #2 (Public Review):

Summary:

The authors aimed to explore the role of climbing fibers (CFs) in cerebellar learning, with a focus on optokinetic reflex (OKR) adaptation. Their goal was to understand how CF activity influences memory acquisition, memory consolidation, and memory retrieval by optogenetically suppressing CF inputs at various stages of the learning process.

Strengths:

The study addresses a significant question in the cerebellar field by focusing on the specific role of CFs in adaptive learning. The authors use optogenetic tools to manipulate CF activity. This provides a direct method to test the causal relationship between CF activity and learning outcomes.

Weaknesses:

Despite shedding light on the potential role of CFs in cerebellar learning, the study is hampered by significant methodological issues that question the validity of its conclusions. The absence of detailed evidence on the effectiveness of CF suppression and concerns over tissue damage from optogenetic stimulation weakens the argument that CFs are not essential for memory consolidation. These challenges make it difficult to confirm whether the study's objectives were fully met or if the findings conclusively support the authors' claims. The research commendably attempts to unravel the temporal involvement of CFs in learning but also underscores the difficulties in pinpointing specific neural mechanisms that underlie the phases of learning. Addressing these methodological issues, investigating other signals that might instruct consolidation, and understanding CFs' broader impact on various learning behaviors are crucial steps for future studies.

[Editors' note: we have included the original concerns, which the Reviewing Editor agrees with. Methodological concerns remain after revisions.]

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study presents potentially valuable insights into the role of climbing fibers in cerebellar learning. The main claim is that climbing fiber activity is necessary for optokinetic reflex adaptation, but is dispensable for its long-term consolidation. There is evidence to support the first part of this claim, though it requires a clearer demonstration of the penetrance and selectivity of the manipulation. However, support for the latter part of the claim is incomplete owing to methodological concerns, including unclear efficacy of longer-duration climbing fiber activity suppression.

We sincerely appreciate the thoughtful feedback provided by the reviewer regarding our study on the role of climbing fibers in cerebellar learning. Each point raised has been carefully considered, and we are committed to addressing them comprehensively. We acknowledge the importance of addressing methodological concerns, particularly regarding the efficacy of long-term suppression of CF activity, as well as ensuring clarity regarding the penetrance and selectivity of our manipulation. To this end, we have outlined plans for substantial revisions to the manuscript to adequately address these issues.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by Seo et al highlights knowledge gaps regarding the role of cerebellar complex spike (CS) activity during different phases of learning related to optokinetic reflex (OKR) in mice. The novelty of the approach is twofold: first, specifically perturbing the activity of climbing fibers (CFs) in the flocculus (as opposed to disrupting communication between the inferior olive (IO) and its cerebellar targets globally); and second, examining whether disruption of the CS activity during the putative "consolidation phase" following training affects OKR performance.

The first part of the results provides adequate evidence supporting the notion that optogenetic disruption of normal CF-Purkinje neuron (PN) signaling results in the degradation of OKR performance. As no effects are seen in OKR performance in animals subjected to optogenetic irradiation during the memory consolidation or retrieval phases, the authors conclude that CF function is not essential beyond memory acquisition. However, the manuscript does not provide a sufficiently solid demonstration that their longterm activity manipulation of CF activity is effective, thus undermining the confidence of the conclusions.

Strengths:

The main strength of the work is the aim to examine the specific involvement of the CF activity in the flocculus during distinct phases of learning. This is a challenging goal, due to the technical challenges related to the anatomical location of the flocculus as well as the IO. These obstacles are counterbalanced by the use of a well-established and easy-to-analyse behavioral model (OKR), that can lead to fundamental insights regarding the long-term cerebellar learning process.

Weaknesses:

The impact of the work is diminshed by several methodological shortcomings.

Most importantly, the key finding that prolonged optogenetic inhibition of CFs (for 30 min to 6 hours after the training period) must be complemented by the demonstration that the manipulation maintains its efficacy. In its current form, the authors only show inhibition by short-term optogenetic irradiation in the context of electrical-stimulation-evoked CSs in an ex vivo preparation. As the inhibitory effect of even the eNpHR3.0 is greatly diminished during seconds-long stimulations (especially when using the yellow laser as is done in this work (see Zhang, Chuanqiang, et al. "Optimized photo-stimulation of halorhodopsin for long-term neuronal inhibition." BMC biology 17.1 (2019): 1-17. ), we remain skeptical of the extent of inhibition during the long manipulations. In short, without a demonstration of effective inhibition throughout the putative consolidation phase (for example by showing a significant decrease in CS frequency throughout the irradiation period), the main claim of the manuscript of phase-specific involvement of CF activity in OKR learning cannot be considered to be based on evidence.

Second, the choice of viral targeting strategy leaves gaps in the argument for CF-specific mechanisms. CaMKII promoters are not selective for the IO neurons, and even the most precise viral injections always lead to the transfection of neurons in the surrounding brainstem, many of which project to the cerebellar cortex in the form of mossy fibers (MF). Figure 1Bii shows sparsely-labelled CFs in the flocculus, but possibly also MFs. While obtaining homogenous and strong labeling in all floccular CFs might be impossible, at the very least the authors should demonstrate that their optogenetic manipulation does not affect simple spiking in PNs.

Finally, while the paper explicitly focuses on the effects of CF-evoked complex spikes in the PNs and not, for example, on those mediated by molecular layer interneurons or via direct interaction of the CF with vestibular nuclear neurons, it would be best if these other dimensions of CF involvement in cerebellar learning were candidly discussed.

We appreciate the reviewer’s thorough evaluation, which thoughtfully highlights the strengths and areas for improvement in our study.

We agree with the reviewer’s recognition of the novelty of our approach, particularly in specifically perturbing climbing fiber (CF) activity in the flocculus and examining its effects across distinct phases of learning. Additionally, our use of the well-established OKR behavior paradigm provides a robust framework for investigating cerebellar learning processes, further strengthening our study.

To address concerns regarding the efficacy of long-term optogenetic inhibition and the specificity of viral targeting, we conducted additional experiments. These include in vivo monitoring of CF activity during the irradiation period, confirming sustained inhibition of complex spikes throughout the consolidation phase. To ensure precise targeting and mitigate potential side effects, such as unintended modification of Purkinje cell (PC) simple spike activity, we demonstrated that optogenetic suppression of CF transmission did not affect simple spike firing. Furthermore, we made additional characterizations to confirm the specificity of viral targeting.

Lastly, we recognize the importance of exploring alternative mechanisms underlying CF involvement in cerebellar learning. Accordingly, we expanded the manuscript to provide a more comprehensive discussion of these mechanisms, offering a clearer perspective on the broader implications of our findings.

Reviewer #2 (Public Review):

Summary:

The authors aimed to explore the role of climbing fibers (CFs) in cerebellar learning, with a focus on optokinetic reflex (OKR) adaptation. Their goal was to understand how CF activity influences memory acquisition, memory consolidation, and memory retrieval by optogenetically suppressing CF inputs at various stages of the learning process.

Strengths:

The study addresses a significant question in the cerebellar field by focusing on the specific role of CFs in adaptive learning. The authors use optogenetic tools to manipulate CF activity. This provides a direct method to test the causal relationship between CF activity and learning outcomes.

Weaknesses:

Despite shedding light on the potential role of CFs in cerebellar learning, the study is hampered by significant methodological issues that question the validity of its conclusions. The absence of detailed evidence on the effectiveness of CF suppression and concerns over tissue damage from optogenetic stimulation weakens the argument that CFs are not essential for memory consolidation. These challenges make it difficult to confirm whether the study's objectives were fully met or if the findings conclusively support the authors' claims. The research commendably attempts to unravel the temporal involvement of CFs in learning but also underscores the difficulties in pinpointing specific neural mechanisms that underlie the phases of learning. Addressing these methodological issues, investigating other signals that might instruct consolidation, and understanding CFs' broader impact on various learning behaviors are crucial steps for future studies.

We appreciate the reviewer’s recognition of the significance of our study in addressing the fundamental question of the role of CF in adaptive learning within the cerebellar field. The use of optogenetic tools indeed provides a direct means to investigate the causal relationship between CF activity and learning outcomes.

To address concerns regarding the effectiveness of CF suppression during consolidation, we plan to conduct further in-vivo recordings. These will demonstrate how reliably CF transmission can be suppressed through optogenetic manipulation over an extended period.

In response to the concern about potential tissue damage from laser stimulation, we believe that our optogenetic manipulation was not strong enough to induce significant heat-induced tissue damage in the flocculus. According to Cardin et al. (2010), light applied through an optic fiber may cause critical damage if the intensity exceeds 100 mW, which is eight times stronger than the intensity we used in our OKR experiment. Furthermore, if there had been tissue damage from chronic laser stimulation, we would expect to see impaired long-term memory reflected in abnormal gain retrieval results tested the following day. However, as shown in Figures 2 and 3, there were no significant abnormalities in consolidation percentages even after the optogenetic manipulation.

Finally, we appreciate the reviewer’s recognition of the challenges involved in pinpointing specific neural mechanisms. We plan to expand the discussion to address these complexities and outline future research directions.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Inhibitory optogenetic actuators are generally problematic, especially in time frames longer than seconds. If the authors wish to be able to inhibit activity in the flocculus-targeting CFs for a long time, maybe it would make sense to try to retrogradely transfect the IO neurons from the flocculus (using a cre-lox approach) with inhibitory DREADDs. This approach is also full of problems, so the absence or significant decrease in CS activity throughout the period of manipulation must be demonstrated.

In addition to re-examining the strength of the evidence regarding the role of CFs in the consolidation and retrival phases, the manuscript would benefit from significant reworking of the details in the manuscript and figures. Below is a possibly incomplete list of things we would want to highlight:

(1) While the text states the authors "... verified the potential reduction of Cs firing rate in PCs of awake mice in vivo by inhibiting CF signals", the data nor a figure are shown. This is of critical importance when judging the reliability of the following results. The data presented in panels Figure 1D-E should also be improved to be more informative, specifically, the waveforms of EPSCs should be shown in higher resolution. We are not informed about how many cells/slices/animals the results are obtained from, nor how many trials were done per condition. Finally, the in vitro data is from vermal Purkinje neurons, while the focus of the work is in the flocculus. Please provide these verifications for the flocculus.

To verify the suppression of complex spike (Cs) activity, we conducted additional in-vivo experiments and added Figure 2, which presents recordings of Cs firing rates from Purkinje cells (PCs) during optogenetic suppression of climbing fiber (CF) activity. These data demonstrate that the suppression specifically and robustly targets Cs activity without affecting simple spike firing, as shown in Figure 2C. The results presented in Figure 2 were acquired at 40 minutes of optostimulation, consistently showing effective suppression of Cs activity throughout this period. While continuous recordings over several hours were not performed, the stability and sustained suppression observed at the 40-minute mark strongly suggest that the manipulation remains effective during the extended durations required for the behavioral tests.

Additionally, we have improved Figure 1D by enhancing the resolution of EPSC waveforms and including more detailed information in the figure legend regarding the number of cells and animals analyzed. For the current-clamp mode data (Figures 1E and F), we clarified the experimental conditions to provide additional context. While the in vitro data were collected from vermal PCs, these experiments were intended to illustrate the fundamental properties of CF-PC transmission.

(2) It is challenging to get a homogenous transfection of all CFs in a given region. To be able to judge the significance of the results, the readers should be provided with material allowing assessing the transfection quality. The images shown in panels Bi-ii are spatially restricted and of too low quality to make judgements. Also, it is not stated whether the images shown are from GFP or NpHR-transfected animals. These different payloads are delivered using different viral capsids (AAV1 vs. AAV9) that have significantly different transfection capacities and results from AAV9-CamKIIGFP cannot be generalized to AAV1-CamKII-NpHR. Please show the expression for the capsid used with NpHR.

To clarify, the images in Figure Bi-ii are representative of GFP expression in animals transfected using AAV1-CamKII-EGFP. The purpose of these panels is to confirm the successful targeting of the region of interest rather than to evaluate viral tropism or capsid-specific transfection efficiency. Moreover, while the transfection characteristics of AAV1 and AAV9 may differ, the key experimental parameter of effective CF suppression was validated through in-vivo electrophysiological recordings, which robustly confirm the efficacy of NpHR expression.

(3) Finally, please show the location of the optic fiber implant in the flocculus from post-mortem images.

In Figure 3a of our revised manuscript, we added post-mortem histological images showing the exact location of the optic fiber implants in the flocculus. These images provided clear confirmation that the optogenetic stimulation was targeted to the correct anatomical region, ensuring that the observed effects are attributable to CF manipulation in the flocculus.

Reviewer #2 (Recommendations For The Authors):

(1) The efficacy of CF suppression is questionable. The histology in Figure 1 shows that only a handful of CFs are transduced in their approach. This observation casts doubt on the claimed complete suppression of CF-evoked EPSCs in every recorded PC in the same figure. This necessitates a more detailed explanation for this apparent discrepancy. Also, the absence of current-clamp recordings to measure the effect on CF-evoked complex spiking in PCs and the lack of detail regarding the timing of optogenetic actuation (continuous or pulsed) during these slice experiments are also significant omissions.

We are providing additional in vivo electrophysiological recordings showing sustained CF suppression in awake animals (Figure 2). These recordings will directly demonstrate the extent of CFevoked complex spike (Cs) suppression.

Moreover, we have included additional data of current-clamp recordings to measure the impact of CF suppression on Cs activity (Figures 1E and 1F). Regarding the timing of the optogenetic actuation, the stimulation was applied continuously in the slice experiments.

(2) The authors claim that their method effectively suppresses CF activity in vivo, yet they do not present any supporting data. Given the histological evidence provided, it's questionable whether their approach truly impacts the CF population broadly, casting doubts on the efficacy of their suppression approach to identify the role of CFs during behavior. To address these concerns, further experiments and detailed quantification are essential to validate the extent and uniformity of CF suppression achieved.

As we responded earlier, we conducted additional in-vivo experiments with continuous recordings of CF-evoked complex spike (Cs) activity during optogenetic suppression (Figure 2). These data directly demonstrate effective and sustained inhibition of CF transmission throughout the behavioral experiments. Quantification of CF suppression revealed consistent inhibition across the manipulation period, with no observable alterations in Purkinje cell simple spike firing rates, confirming that our intervention specifically targeted CF activity without off-target effects. In addition to the in-vivo data, the in-vitro data presented in Figure 1 (lines 107~116) further validate the efficacy of our optogenetic manipulation, showing consistent suppression of CF transmission without any failures. These findings collectively confirm the reliability and specificity of our suppression approach for studying CF contributions to behavior.

(3) To optogenetically test the role of CFs in memory consolidation, the authors deliver continuous, high-power light to the flocculus (13 mW for 6 hrs). This extends well beyond typical experimental conditions. The sustained nature of the light exposure thus brings into question the consistency and reliability of CF suppression over time. Firstly, it is imperative to determine whether CF activity is suppressed throughout this extended period. Secondly, the intensity and duration of light exposure carry a significant risk of causing extensive damage to the surrounding tissue. Given these concerns, a thorough histological examination is warranted to assess the potential adverse effects on tissue integrity. Such an analysis is crucial not only for validating the experimental outcomes but also for ensuring that the observed effects are not confounded by light-induced tissue damage.

To address whether CF activity is suppressed throughout the extended period, we included new in-vivo recordings demonstrating robust suppression of CF transmission, as evidenced by inhibited complex spikes sustained at 40 minutes of optostimulation. Regarding potential tissue damage, our optogenetic protocol used a light intensity (13 mW), which is much lower than the 75 mW threshold reported by Cardin et al. (2010) as sufficient to maintain normal neuronal activity. Moreover, critical damage typically requires intensities exceeding 100 mW for several hours (Cardin, Jessica A., et al. "Targeted optogenetic stimulation and recording of neurons in vivo using cell-type-specific expression of Channelrhodopsin-2." Nature protocols 5.2 (2010): 247-254.). Finally, we observed no abnormalities in long-term memory consolidation or gain retrieval (Figures 3C, 4C, 4F), further supporting that our light stimulation did not induce tissue damage.

(4) The generalizability of their findings to various learning behaviors remains uncertain. Given that the flocculus plays a role in vestibulo-ocular reflex (VOR) adaptation, which encompasses both CFdependent and CF-independent learning types (gain increase and gain decrease, respectively), this system could offer a more feasible approach for investigating hypotheses about the role of CFs in guiding distinct learning processes.

In response to the reviewer’s comment on the generalizability of our findings to learning behaviors involving both CF-dependent and CF-independent mechanisms, we acknowledge the importance of examining these dynamics in cerebellar motor adaptation systems, such as the OKR. Although our study used an OKR task, findings from VOR studies apply here. Ke et al. (2009) demonstrated that VOR gain increases (CF-dependent) and gain decreases (CF-independent) involve distinct plasticity processes (Ke, Michael C., Cong C. Guo, and Jennifer L. Raymond. "Elimination of climbing fiber instructive signals during motor learning." Nature neuroscience 12.9 (2009): 1171-1179), suggesting that CF engagement is task-dependent, particularly for larger error signals that require CF-guided adaptation.

Similarly, our OKR findings suggest that CF-dependent pathways are likely used for large, persistent errors, whereas CF-independent mechanisms may drive more gradual adjustments. This alignment between OKR and VOR systems supports the generalizability of CF-selective adaptation across cerebellar learning tasks. We have elaborated on this point in our revised manuscript (lines 219~237), clarifying how CF-dependent and CF-independent mechanisms can generalize across motor learning contexts in the cerebellum.

(5) The acute effect of CF suppression on OKR eye movements warrants investigation. If OKR eye movements are altered by their method, this could complicate the interpretation of their results.

During our experiments, we monitored ocular movements during CF optogenetic manipulation and found no aberrant effects, such as nystagmus. As shown in Figures 4G and 4H, disrupting CF signaling during gain retrieval did not alter the gain, confirming that our manipulation neither acutely affects ocular reflexes nor induces abnormal eye movement. Therefore, it leads to the conclusion that the observed effects are specific to learning and memory processes.

(6) The authors raise the potential issue of inducing presynaptic LTD in CFs. Can they be sure that their manipulation doesn't generate a similar effect? Additional controls or techniques to accurately interpret the results are needed considering this concern.

However, our discussion does not claim that optogenetic suppression directly induces CF-LTD. Instead, we posit that CF suppression may have mimicked the functional consequences of CFLTD, such as reduced complex spike (Cs) activity and associated calcium signaling. This, in turn, may have indirectly interfered with the induction of parallel fiber-Purkinje cell (PF-PC) LTD, thereby preventing gain enhancement during learning.

This hypothesis is consistent with previous studies highlighting the interplay between CF and PF synaptic plasticity in cerebellar motor learning. For example, Hansel and Linden (2000) and Weber et al. (2003) discuss how changes at CF synapses can modulate Cs waveforms and calcium dynamics, which are critical for PF-PC LTD. Coesmans et al. (2004) and Han et al. (2007) further elaborate on the necessity of CF input for effective PF-PC LTD induction during learning tasks such as retinal slip correction.

While our experiments were not designed to directly measure CF-LTD, the observed prevention of gain enhancement aligns with the hypothesis that CF suppression functionally disrupted downstream PF-PC LTD. We have clarified these points in our revised manuscript (lines 250~258) to avoid misunderstanding.

(7) The specific timeframe for OKR consolidation remains uncertain, with evidence from numerous studies indicating that cerebellar memory consolidation unfolds over several days. Therefore, a more thorough investigation into these extended durations, supported by control experiments to validate the outcomes, would significantly strengthen the study's conclusions, and provide clearer insights into the consolidation process of OKR learning.

Our current study specifically focused on the early phase of the post-learning period, as supported by findings from several studies: Cooke et al., (2004); Titley et al., (2007); Steinmetz et al., (2016); Seo et al., (2024)

These studies collectively indicate that cerebellar-dependent memory consolidation—including OKR—can occur rapidly during the early consolidation phase. While the specific mechanisms examined in these studies vary (e.g., synaptic plasticity, intrinsic plasticity, or circuit-level changes), they consistently demonstrate that modifications in the cerebellum after the early consolidation period no longer influence memory storage or performance. This evidence strongly supports the relevance of our experimental focus and the timing of our interventions.

We acknowledge the importance of investigating extended consolidation periods, which could indeed provide additional insights. However, given our current aims, the rapid consolidation dynamics observed in the early phase are most relevant to the questions addressed in this study. We have elaborated on these matter in our revised manuscript (lines 273~283).

(8) Issues around whether the authors have control over CF activity with their optogenetic intervention raise questions of whether learning can be recovered during the training procedure if the optogenetic stimuli are halted. Specifically, if suppression is applied for three blocks (what the authors refer to as "sessions") during the training procedure and then ceases, does learning rapidly recover in the immediately following blocks?

While we did not directly examine the restoration of learning capability within the same training session following the cessation of optogenetic inhibition, we believe several aspects of our experimental design and insights from prior studies support our interpretation.

Our optogenetic intervention specifically targeted Purkinje cells (PCs) in the flocculus and was applied continuously during designated training sessions to modulate cerebellar activity. Notably, Medina et al. (2001) demonstrated that transient inactivation of the cerebellar cortex impairs the expression of learned responses but does not disrupt the underlying plasticity mechanisms (Medina, Javier F., Keith S. Garcia, and Michael D. Mauk. "A mechanism for savings in the cerebellum." Journal of Neuroscience 21.11 (2001): 4081-4089.). This finding suggests that cerebellar plasticity remains intact and functional even after transient perturbations.

Therefore, it is plausible that once optogenetic inhibition is lifted, the cerebellar network regains its capacity for learning and adaptation, as the intrinsic plasticity and memory encoding processes remain preserved. While we acknowledge that direct experimental confirmation of rapid recovery in our setup was not performed, this interpretation is consistent with our experimental framework and the broader literature.

(9) The study does not fully explore the instructive signals/mechanisms underlying the memory consolidation process. A detailed investigation into potential instructive signals for consolidation beyond CF-induced signaling, like the simple spiking of PCs, could significantly enhance the study's conclusions. Indeed, there is currently no evidence to suggest that CFs play a role in the consolidation phase anyway so testing their role seems a bit of a strawman argument.

While our study primarily focused on characterizing CF-dependent pathways, we acknowledge that memory consolidation is likely driven by a multifaceted interplay of instructive signals beyond CF-induced mechanisms. In particular, Purkinje cell (PC) simple spiking may act as a critical signal during the consolidation phase, either complementing or functioning independently of CF input. Emerging evidence suggests that simple spiking can modulate downstream circuitry in ways that stabilize and strengthen memory traces.

To address this, we have expanded the discussion in the revised manuscript to explore potential instructive signals for consolidation, including PC simple spiking, local circuit plasticity within the cerebellar cortex, and its interaction with the cerebellar nuclei. We propose that these mechanisms collectively contribute to the transfer and stabilization of motor memory, offering a more comprehensive framework for understanding consolidation. We have elaborated on these matter in our revised manuscript (lines 238~250).

(10) Previous reports have highlighted the necessity of CF activity for extinction/memory maintenance (Medina et al. 2002; Kim et al. 2020). That is, the absence of CF activity is consequential for cerebellar function. These results present a potential contrast to the findings reported in this current study. This discrepancy raises important questions about the experimental conditions, methodologies, and interpretations of CF function across different studies. A thorough discussion comparing these divergent outcomes is essential, as it could elucidate the specific contexts or conditions under which CF activity influences memory processes.

We acknowledge that previous studies (Medina et al., 2002; Kim et al., 2020) have suggested a role for climbing fiber (CF) activity in extinction. However, our study specifically focuses on the acquisition phase of motor learning and does not extend to extinction or maintenance. As such, we have revised our discussion to limit interpretations strictly to the scope of our findings and removed references to extinction.

The discrepancies between our results and prior work may arise from differences in methodologies and behavioral paradigms. For instance, we utilized optogenetic inhibition to achieve precise temporal and spatial control of CF activity, whereas previous studies employed pharmacological or lesion methods that may have broader effects on the cerebellar circuitry. Additionally, differences in behavioral paradigms, such as the optokinetic reflex (OKR) task used in our study compared to the eye-blink conditioning tasks in prior studies, may demand distinct roles for CF signaling depending on the specific requirements for error correction and adaptation.

This clarification is now incorporated into our revised manuscript, and the discussion has been streamlined to focus on the phase-specific role of CF activity during acquisition without extending to extinction or maintenance (lines 259~270).

eLife Assessment

This important study investigates the influence of the cingulate cortex on the development of the social vocalizations of marmoset monkeys by making bilateral lesions of this brain area in neonatal animals. The evidence supporting the authors' claims is convincing. The work will be of broad interest to cognitive neuroscientists, speech and language researchers, and primate neuroscientists.

Reviewer #1 (Public review):

Summary:

This study seeks to quantify changes in vocal behavior during development in marmosets with bilateral anterior cingulate cortex (ACC) lesions. The ACC and its role in social vocal behaviors is of great interest given previous literature on its involvement in initiation of vocalizations, processing emotional content, and its connectivity to two other critical nodes in the vocal network, the amygdala and the PAG. The authors seek to test the hypothesis that the ACC contributes to the development of mature vocal behaviors during the first few weeks of life by disrupting this process with neonatal ACC lesions. Imaging and histological analyses confirm the extent of the lesion and suggest downstream effects in connected regions. Analysis of call rates and call type proportions show no or slight differences between lesioned and controlled animals. Additional analyses on the proportion of grouped 'social' calls and certain acoustic features of a particular call, the phee, reveal more distinct differences between the groups.

Strengths:

The authors have identified that ACC lesions in early life have no or little influence on certain aspects of vocal behavior (e.g. call rate, call intervals) but larger impacts on other aspects (e.g. acoustic features of phee calls). This is difficult data to collect, especially in the difficulties of that particular time period. This data is a valuable addition to the literature on the effects of the ACC on vocal production and sparks intriguing follow-up questions on the role of different acoustic features (as related to emotional content) on vocal interactions with conspecifics over the lifespan.

The histological methods and resulting quantification of neural changes in the lesioned area and in downstream areas of interest are intriguing given the large time gap between the lesion and these analyses.

The changes to the text, figures, and additional supplemental figures to my previous review requests have made it easier to determine if conclusions are supported by the data in the manuscript. Examples include the quantification of the loss of neurons and increase in glial cells, the inclusion of changes in body weight and grip strength that could also be a result from the lesions affecting vocal behavior, and additional details on analysis methods.

Weaknesses:

The article emphasizes vocal social behavior. However, marmoset infants are recorded in isolation which allows for examining the development of vocal behavior in that particular context - reaching out to conspecifics. The text now covers the relationship between 'social' information in calls and development in this particular context. However, early-life maturation of vocal behavior is strongly influenced by social interactions with conspecifics. For example, the transition of cries and subharmonic phees which are high-entropy calls to more low-entropy mature phees is affected by social reinforcement from the parents. And this effect extends cross-context, where differences in these interaction patterns extend to vocal behavior when the marmosets are alone. Together, the results are interesting and important but may not fully capture the changes resulting from direct social interactions.

Additionally, it is an intriguing finding that the infants' phee calls have acoustic differences being 'blunted of variation, less diverse and more regular'. Though the text about how the social message conveyed by these infants was 'deficient, limited, and/or indiscriminate' is now better explained with additional text from human studies, it is still an assumption that this would directly translate to marmoset communication. Thus, experiments directed at the responses of other marmosets to these calls would still be important.

Reviewer #2 (Public review):

Summary:

Nagarajan et al. investigate the role of the anterior cingulate cortex (ACC) in vocal development of infant marmoset monkeys using lesions in this brain area. Many previous studies show that ACC plays an important role in volitional and emotion-driven vocal behavior in mammals. The experiments Nagarajan et al. performed strengthen the long-standing hypothesis that ACC influences the development of social-vocal behavior in non-human primates. Furthermore, their anatomical studies support the idea of cortical structures exerting cognitive control over subcortical networks for innate vocalization, and thus, enabling mammals to perform flexible social-vocal communication.

Strengths:

Many invasive behavioral studies in monkeys often use 2-3 animals. The authors used a sufficiently high number of animals for their experiments. This increases the power of their conclusions.

The study also investigates the impact of ACC lesions on downstream areas important for innate vocal production. This adds further evidence to the role of ACC on influencing these subcortical regions during vocal development and vocal behavior in general.

Weaknesses:

The study only provides data up to the 6th week after birth. Given the plasticity of the cortex, it would be interesting to see if these impairments in vocal behavior persist throughout adulthood or if the lesioned marmosets will recover their social-vocal behavior compared to the control animals. The authors give a reasonable explanation for why they did not provide this data.

Even though this study focuses entirely on the development of social vocalizations, providing data about altered social non-vocal behaviors that accompany ACC lesions is missing. This data can provide further insights and generate new hypothesis about the exact role of ACC in social-vocal development. For example, do these marmosets behave differently towards their conspecifics or family members and vice versa, and is this an alternate cause for the observed changes in social-vocal development? Unfortunately, the authors are unable to provide that data. Hopefully, this will be the goal of future studies.

Reviewer #3 (Public review):

Summary:

In this manuscript, Nagarajan et al. study the impact of early damage to the anterior cingulate cortex (ACC) on the vocal development of marmoset monkeys. AAC lesions were performed on neonatal marmosets and their vocal patterns and the spectrotemporal features of their calls were analyzed compared to control groups during the first six weeks of life. While the vocal repertoire was not significantly affected by ACC lesions, the authors described notable differences in the social contact call, the phee call. Marmosets with ACC damage made fewer social contact calls, and when they did, these calls were shorter, louder, and monotonic. Additionally, the study revealed that ACC damage in infancy led to permanent alterations in downstream brain areas involved in social vocalizations, such as the amygdala and periaqueductal gray.

Strengths:

This study suggests that the ACC plays a crucial role in the normal development of social vocal behavior in infant marmosets. Studying vocal behavior in marmosets can provide insights into the neural mechanisms underlying human speech and communication disorders due to their similarity in brain structure and social behavior.

The methods are robust and reliable with precise localization of the lesions with neuroimaging and histological examination.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

The article emphasizes vocal social behavior but none of the experiments involve a social element. Marmosets are recorded in isolation which could be sufficient for examining the development of vocal behavior in that particular context. However, the early-life maturation of vocal behavior is strongly influenced by social interactions with conspecifics. For example, the transition of cries and subharmonic phees which are high-entropy calls to more low-entropy mature phees is affected by social reinforcement from the parents. And this effect extends cross context where differences in these interaction patterns extend to vocal behavior when the marmosets are alone. From the chord diagrams, cries still consist of a significant proportion of call types in lesioned animals. Additionally, though it is an intriguing finding that the infants' phee calls have acoustic differences being 'blunted of variation, less diverse and more regular,' the suggestion that the social message conveyed by these infants was 'deficient, limited, and/or indiscriminate' is not but can be tested with, for example, playback experiments.

We recognize that our definition of vocal social behavior is not within the normal realm of direct social interactions. We were particularly interested in marmoset vocalizations as a social signal, such as phees, cries and twitter, even when their family members or conspecifics are not visibly present. Generally speaking, in the laboratory, infant marmosets make few calls when in the presence of another conspecific, but when isolated they naturally make phee calls to reach out to their distantly located relatives. In this context, while we did not assess the animals interacting directly, we assessed what are normally referred to as ‘social contact calls,’ hence the term ‘social vocalizations.’ Playback recordings might provide potential evidence of antiphonal calling as a means of social interaction and might reveal the poor quality of the social message conveyed by the infant, but even here, the vocalizing marmoset would be calling to a non-visible conspecific. Thus, although our experiment lacked a direct social element, our data suggest that in the absence of a functioning ACC in early life, infant calls that convey social information, and which would elicit feedback from parents and other family members, may be compromised, and this could potentially influence how that infant develops its social interactive skills. We have now commented on the significance of social vocalizations in the introductory text (page 3) and discussion (page 15).

The manuscript would benefit from the addition of more details to be able to better determine if the conclusions are well supported by the data. Understanding that this is very difficult data to get, the number of marmosets and some variability in the collection of the data would allow for the plotting of each individual across figures. For example, in the behavioral figures, which is the marmoset that is in the behavioral data that has a sparing of the ACC lesion in one hemisphere? Certain figures, described below in the recommendations for the authors, could also do with additional description.

Thanks for these suggestions. We have plotted the individual animals in the relevant figures and addressed the comments and recommendations listed below.

Reviewer #1 (Recommendations For The Authors):

Given the number of marmosets, variability in the collected data, lesion extent, and different controls, I would like to see more plots with individuals indicated (perhaps with different symbols). More details could also be added for several plots.

Figure 2D (new) and 2E now have plots that represent the individual animals, each represented by a different symbol.

Figure 2A) Since lesions are bilateral, could you also show the extent of the lesions on the other side for completeness?

Our intention was to process one hemisphere of each brain for Golgi staining to examine changes in cell morphology in the ACC and associated brain regions following the lesion. Unfortunately, the Golgi stain was unsuccessful. Consequently, we were unable to use the tissue to reconstruct the bilateral extent of the lesion. We did, however, first establish the bilateral nature of the lesion through coronal slices of the animals MRI scan before processing the intact hemisphere to confirm the bilateral extent of the lesion. The MRI scans (every 5th section) for each control and lesioned animal is compiled in a figure in the supplementary materials (Fig. S1). These scans show that the ACC-lesioned animals have bilateral lesions with one animal (ACC1) showing some sparing in one hemisphere, as we noted in the text. We have now made reference to this supplemental figure in the text (page 5).

Figure 2B/C) In Figure 2B, control and ACC lesions are in the columns while right next to it in 2C, ACC lesion and control are in the rows. Could these figures be adjusted so that they are consistent?

We have now adjusted these figures and updated the figure legends accordingly.

Figure 2C) Is there quantification of the 'loss of neurons and respective increase in glial cells at the lesioned site especially at the interface between gray and white matter'? There are multiple slices for each animal.

Thanks for suggesting this. We have now quantified these data which are presented as a new graph as Fig. 2D. These data revealed a significant loss of neurons (NeuN) in the ACC group as well as an increase in glial cells (GFAP and Iba1) relative to the controls. The figure legend and results have also been updated.

Figure 2C) It is difficult for me to distinguish between white and purple - could you show color channels independently since images were split into separate channels for each fluorophore?

Fig. 2C has been revised to better visualize the neurons and glia at the gray and white matter interface. We found that grayscale images for each channel offered a better contrast than separating the channels for each fluorophore.

Figure 2C/D) I like how there are individual dots here for the individual marmosets. Since there are four in each group, could they be represented throughout with symbols (with a key indicating the pair and also the control condition)? For example, were there changes in the histology for control animals that got saline injections as opposed to those that didn't get any surgery?

We have highlighted the individual animals with different symbols in the figures. Although some animals were twin pairs, it was not possible to have twins in all cases. Only two sets were twins. We have indicated the symbols that represent the twin pair in Fig. 2 as well as the MRI scans of the twin pairs in Fig. S1. There were no observed changes in histology for the sham animals relative to the other non-sham controls. The MRI scan for one sham CON2 shows herniated tissue in the right hemisphere which is a normal consequence of brain exposure caused by a craniotomy.

Figure 3D-E) Here, individual data points could be informative especially given that some animals are missing data past the third week.

To prevent cluttering the figure with too many data points, we have added the sample size for each group in the figure legend (pages 33).

Figure 3D/F) What exactly is the period that goes into this analysis? In the text, 'Further analysis showed that the ACC lesion had minimal effects on the rate of most call types during this period'. Is this period from weeks 3 to 6 relative to the proportions in week 2? I think I also don't quite understand the chord diagram. The legend says 'the numbers around each chord diagram represents relative probability value for each call type transition' so how does that relate to the proportion of these call types? It looks like there is a wider slice for cries for ACC-lesioned animals each week. I also don't see in the week 4 chord diagram, the text description of 'elevation in the rate of 'other' calls, which comprised tsik, egg, eck, chatter and seep calls. These calls were significantly elevated in animals after the ACC lesion."

We apologize for the confusion. Fig 3D and Fig 3F are not directly related. Fig. 3D shows the different types of emitted calls. The figure shows the averaged data per group pooled from post-surgery weeks (week 3 – week 6). It represents the proportion of individual call types relative to the total number of calls during each recording period. The only major finding here was the increased rate of ‘other’ calls comprising tsik, egg, ock, chatter and seep calls. These calls were significantly elevated in animals after the ACC lesion.

While Fig. 3D represents the differences in the proportion of calls, the chord diagrams in Fig. 3F represents the probability of call-to-call transition obtained from a probability matrix. At postnatal week 6, marmosets with ACC lesions showed a higher likelihood of transitions between all call types, but less frequent transitions between social contact calls relative to sham controls. The chord diagrams visualize the weighted probabilities and directionality of these transitions between the different call types. Weighted probabilities were used to account for variations in call counts. The thickness of the arrows or links indicates the probability of a call transition, while the numbers surrounding each chord diagram represent the relative probability value for each specific transition. We have now reworded the text and clarified these details in the figure legend (pages 32-33).

Figure 3E) How is the ratio on the y-axis calculated here?

The y-axis represents the averaged value of the ratios of the number of social contact calls relative to non-social contact calls in each recording per subject per group (i.e., (x̄ (# social calls / # non-social calls). This is now included in the figure legend and the axis is updated (page 32).

Also, cries could be considered a 'social contact call' since they are produced by infants to elicit responses from the parents. There is also the hypothesis in the literature that cries transition into phees.

The reviewer is correct. Cries are often considered a social contact call because they elicit parental feedback. We decided to separate cry-calls from other social contact calls for two reasons. First, in our sample, we found cry behavior to be highly variable across the animals. For example, one control infant cried incessantly whereas another control infant cried less than normal. This extreme variability in animals of the same group masked the features between animals that reliably differentiated between them. Second, cry-calls elicit feedback from parents who are normally within the vicinity of the infant whereas phee calls elicit antiphonal phee calls from any distantly located conspecific. In other words, the context in which these calls are often elicited are very different.

The use of 'syntactical' is a bit jarring to me because outside of linguistics, its use in animal communication generally refers to meaning-bearing units that can be combined into well-formed complexes such as pod-specific whale songs or predator alarm calls with concatenated syllable types in some species of monkeys. To my knowledge, individual phee syllables have not been currently shown to carry information on their own and may be better described as 'sequential' rather than 'syntactical'.

We agree. We have made this change accordingly.

Figure 4B) How many phee calls with differing numbers of syllables are present each week? How equal is the distribution given that later analyses go up to 5 syllables?

The total number of phee calls with differing number of syllables ranged between 20-40 phees. This number varied between subjects, per week. The most common were 3- and 4-syllable phee calls which ranged from 7-15. Due to this variability, Fig. 4B presents the average syllable count. The axis is now updated.

Figure 4C-E) How is the data combined here? Is there a 2nd syllable, the combined data from the 2nd syllable from phee calls of all lengths (1 - 5?). If so, are there differences based on how long the total sequence is?

The combined data represents the specific syllable (e.g., the 1st syllable in a 2-syllable phee, in a 3-syllable phee and in a 4-syllable phee) irrespective of the length of the sequence in a sequence. No differences were observed between 2nd syllable in a 2 syllable phee and 2nd syllable in a 3 or a 4 syllable phee. We have included this detail in the figure legend (page 33-34).

So duration is a vocal parameter that is highly dependent on physical factors such as body size and lung volume, where there differences in physical growth between the pairs of ACC-lesioned marmosets and their twins? Entropy is less closely tied to these physical factors but has previously been shown to decrease as phee calls mature, which we can also see in the negative relationship of the control animals. Do you know of experiments that show that lower entropy calls are more 'blunted'?

Thank you for raising the important issue of physical growth factors. For twin pairs, it is not uncommon for one infant to be slightly bigger, heavier or stronger than the other presumably because one gets more access to food. With increasing age, we did not observe significant changes in bodyweight between the groups. We examined grip strength in all infants as a means of assessing how well the infant was able to access food during nursing. Poor grip strength would indicate a lower propensity to ‘hang on’ to the mother for nursing which could lead to lower weight gain and reduced physical growth. We found that both grip strength and body weight increased as the infants got older and both parameters were equivalent. We have included an additional figure to show the normal increase in both weight and grip strength to the supplemental materials (Fig. S3) and have made reference to this in the text (page 8).

As for entropy, it’s impact on the emotional quality of vocalizations has not been systematically explored. Generally speaking, high entropy relates to high randomness and distortion in the signal. Accordingly, one view posits low-entropy phee calls represent mature sounding calls relative to noisy and immature high-entropy calls (e.g., Takahasi et al 2017). In the current study, the reduction in syllable entropy observed for both groups of animals with increasing age is consistent with this view. At the same time entropy can relate to vocal complexity; high entropy refers to complex and variable sound patterns whereas low entropy sounds are predictable, less diverse and simple vocal sequences (Kershenbaum, A. 2013. Entropy rate as a measure of animal vocal complexity. Bioacoustics, 23(3), 195–208). One possibility is that call maturity does not equate directly to emotional quality. In other words, a low-entropy mature call can also be lacking in emotion as observed in humans with ACC damage; these patients show mature speech, but they lack the variations in rhythms, patterns and intonation (i.e., prosody) that would normally convey emotional salience and meaning. Our observation of a reduction in phee syllable entropy in the ACC group in the context of being short and loud with reduced peak frequency is consistent with this view. Our use of the word ‘blunt’ was to convey how the calls exhibited by the ACC group were potentially lacking emotional meaning. Beyond this speculation, we are not aware of any papers that have examined the relationship between entropy and blunted calls directly. We have now included this speculation in the discussion (pages 12-13).

Reviewer #2 (Public Review):

The authors state that the integrity of white matter tracts at the injection site was impacted but do not show data.

We have added representative micrographs of a control and ACC-lesioned animal in a new supplementary figure which shows the neurotoxin impacted the integrity of white matter tracts local to the site of the lesion (Fig. S2).

The study only provides data up to the 6th week after birth. Given the plasticity of the cortex, it would be interesting to see if these impairments in vocal behavior persist throughout adulthood or if the lesioned marmosets will recover their social-vocal behavior compared to the control animals.

We agree. Our original intention was to examine behavior into adulthood. Unfortunately, the COVID-19 pandemic compromised the continuation of the study. We were limited by the data that we were allowed to acquire due to imposed restrictions. Some non-vocalization data collected when the animals were young adults is currently being prepared for another paper.

Even though this study focuses entirely on the development of social vocalizations, providing data about altered social non-vocal behaviors that accompany ACC lesions is missing. This data can provide further insights and generate new hypotheses about the exact role of ACC in social vocal development. For example, do these marmosets behave differently towards their conspecifics or family members and vice versa, and is this an alternate cause for the observed changes in social-vocal development?

We agree. At the time however, apparatus for assessing behavior between the infant’s family and non-family members was not available. Assessing such behaviors in the animals holding room posed some difficulty since marmosets are easily distracted by other animals as well as the presence of an experimenter, amongst other things. This is an area of investigation we are currently pursuing.

Reviewer #3 (Public Review):

It is striking to find that the vocal repertoire of infant marmosets was not significantly affected by ACC lesions. During development, the neural circuits are still maturing and the role of different brain regions may evolve over time. While the ACC likely contributes to vocalizations across the lifespan, its relative importance may vary depending on the developmental stage. In neonates, vocalizations may be more reflexive or driven by physiological needs. At this stage, the ACC may play a role in basic socioemotional regulation but may not be as critical for vocal production. Since the animals lived for two years, further analysis might be helpful to elucidate the precise role of ACC in the vocal behavior of marmosets.

Figure 3D. According to the Introduction "...infant ACC lesions abolish the characteristic cries that infants normally issue when separated from its mother". Are the present results in marmosets showing the opposite effect? Please discuss.

To date, the work of Maclean (1985) is the only publication that describes the effect of early cingulate ablation on the spontaneous production of ‘separation calls’ largely construed as cries, coos and whimpers in response to maternal separation. All of this work was largely performed in rhesus macaques or squirrel monkeys. In addition to ablating the cingulate cortex, Maclean found that it was necessary to ablate the subcallosal (areas 25) and preseptal cingulate cortex (presumably referring to prelimbic area 32) to permanently eliminate the spontaneous production of separation cry calls. Our ablation of the ACC was more circumscribed to area 24 and is therefore consistent with MacLean’s earlier work that removal of ACC alone does not eliminate cry behavior. In adults, ACC ablation is insufficient at eliminating vocalization as well. We make reference to this on pages 13-14 of the discussion.

Figure 3E and Discussion. Phees are mature contact calls and cries immature contact calls (Zhang et al, 2019, Nat Commun). Therefore, I would rather say that the proportion of immature (cries) contact calls increases vs the mature (phee, trill, twitters) contact calls in the ACC group. Cries are also "isolated-induced contact calls" to attract the attention of the caregivers.

The reviewer is correct in that cries are directed towards caregivers but in our sample, cry behavior was highly variable between the infants. Consequently, in Fig. 3E social contact calls include phee, twitter and trill calls but does not include cries which were separated (see also response to reviewer #1). Many of the calls made during babbling were immature in their spectral pattern (compare phee calls between Fig. 3A and 3B). Cries typically transitioned into phees, twitters or trills before they fully matured. Fig 3E shows that the controls made more isolation-induced social contact calls at postnatal week 6 which were presumably maturing at this time point. Thus, if anything, there was an increase in the proportion of mature contact calls vs immature contact calls with increasing age.

Figure 4D. Animal location and head direction within the recording incubator can have significant effects on the perceived amplitude of a call. Were these factors taken into account?

The reviewer makes an excellent observation. Unfortunately, we did not account for location and head direction because the infants were quite mobile in the incubator. The directional microphone was hidden from view because the infants were distracted by it, and positioned ~12 cm from the marmoset, and placed in the exact same location for every recording. In addition, calls with phantom frequencies were eliminated during visual inspection of spectrograms. Beyond these details, location and head direction were not taken into account.

Figure 4E. When a phee call has a higher amplitude, as is the case for the ACC group (Figure 4D), the energy of the signal will be concentrated more strongly at the phee call frequency ~8KHz. This concentration of the energy reduces the variability in the frequency distribution, leading to lower entropy. The interpretation of the results should be reconsidered. A faint call (control group) can exhibit more variability in the frequency content since the energy is distributed across a wider range of frequencies contributing to higher entropy. It can still be "fixed, regular, and stereotyped" if the behavior is consistent or predictable with little variation. Also, to define ACC calls as "monotonic" I would rather search for the lack of frequency modulation, amplitude variation, or narrower bandwidth.

We very much appreciate this explanation. We were able to identify the maximum frequency that closely matched pitch of a sound for each syllable in a multisyllabic phee. New Fig. 4E shows that the peak frequency for each phee syllable was lower in the ACC-lesioned monkeys which may directly translate to the low entropy observed in this group. The term “monotonic” was used to relate our data to the classical and long-standing evidence of human ACC lesions causing monotonous intonation of speech. When all factors are taken into account, it is evident that the vocal phee signature of the ACC-lesioned animal was structurally different to the controls implicating a less complex and stereotyped ACC signal. Further studies are needed to systematically explore the relationship between entropy and emotional quality of vocalizations

Apart from the changes in the vocal behavior, did the AAC lesions manifest in any other observable cognitive, emotional, or social behavior? ACC plays a role in processing pain and modulating pain perception. Could that be the reason for the observed increase in the proportion of cries in the ACC group and the increase in the phee call amplitude? Did the cries in the ACC group also display a higher amplitude than the cries in the control group?

It was our intention to acquire as much data as possible from these infants as they matured from a cognitive, social and emotional perspective. Unfortunately, our study was hampered by variety of reasons including the COVID-19 pandemic which imposed major restrictions on our ability to continue with the experiment in a time sensitive manner. In addition, the development and construction of the custom apparatus to measure these behaviors was stalled during this period further preventing us from collecting behavioral data at regular time intervals. As for the cry behavior, the number of cries, in the ACC group were very low especially at postnatal week 5 and 6. Consequently, there were very few data points to work with.

Discussion. Louder calls have the potential to travel longer distances compared to fainter calls, possess higher energy levels, and can propagate through the environment more effectively. If the ACC group produced louder phee syllables, how could be the message conveyed over long distances "deficient, limited, and/or indiscriminate"?

Thanks for raising this interesting concept. Not all calls emitted by the animals were loud. We specifically examined the long-distance phee call in this regard. The phee syllables emitted by the ACC group were high amplitude with low frequencies, short duration and low entropy. Taking these factors into account, it is conceivable that the phee calls produced by the ACC group could not effectively convey their message over long distances despite their propagation through the environment. We have made reference to this in the discussion where we focus is specifically on the phee calls only (pages 12).

Abstract: Do marmosets have syntax? Consider replacing "syntactical" with a more appropriate term (maybe "syntax-like").

Thanks for this suggestion. We have replaced the term syntactical with ‘sequential’ as per the recommendation of reviewer #1.

Introduction: "...cries that infants normally issue when separated from its mother". Please replace "its" with "their".

This has been corrected.

Results: Is the reference to Fig 1B related to the text?

We have included and referred to Fig. 1B in the text (results and methods) to show other researchers how they can use this technique as a reliable and safe means of monitoring tidal volume under anesthesia in small infant marmoset without intubation.

I understand that both "spectrograph" and "spectrogram" are used to analyze the frequency content of a signal. Nevertheless, "spectrogram" refers to the visual representation of the frequency content of a signal over time, and this term is commonly used in audio signal processing and specifically in the vocal communication field. I would recommend replacing "spectrograph" with "spectrogram".

Thanks for this suggestion. We have corrected this throughout the manuscript.

(Concerning the previous comment in the public review). Cries are uttered to attract the attention of the caregivers. The increase in the proportion of cries in the ACC group does not match the sentence: "...these infants appeared to make little effort in using vocalizations to solicit social contact when socially isolated".

We apologize for the confusion. It is not the case that the ACC animals make more cries. Cry calls were highly variable amongst the animals. Consequently, although Fig 3D gives the impression that the proportion of cries in higher in ACC animals they did not differ significantly from the controls. Due to their high variability, cries were removed in the measurement of social contact. Accordingly, Fig. 3E does not include cry behavior; it shows that the ACC animals engage less in social contact calls.

Related to Figure 3. What is the difference between "egg" and "eck" calls? Do you mean "ock"?

We apologize. This was a typo. It should be ock calls.

Figure 4B. Is the sample size five animals per group and per week? Overlapping data points seem to be placed next to each other. Why in some groups (e.g. ACC 6 weeks) less than five dots are visible?

The sample size differed per week because of the lack of recording during the COVID restrictions. In Fig 4b, we have now separated the overlapping dots. We have also added the sample size of the groups in the figure legends.

Would the authors expect to see stronger differences between the lesioned and the control groups when comparing a later developmental stage? The animals were euthanized at the age of

These speculation is certainly feasible and yes, we were hoping to establish this level of detail with testing at later developmental stages. This is an aspect of development we are currently pursuing.

Could these experiments be conducted?

I’m afraid these animals are longer available, but we are currently conducting experiments in other animals with early life neurochemical manipulations who show behavioral changes into early adulthood.

ACC lesion: It is reported that the lesions extended past 24b into motor area 6M. Did the animal display any motor control disability?

Surprisingly, despite the lesion encroaching into 6M, these animals showed no observable motor impairment. We assessed the animals grip strength and body weight and discovered normal strength and growth in weight in both controls and the lesioned group. We have added this data as supplemental information (Fig. S3).

eLife Assessment

This study investigates how the maintenance of a spatial location in working memory affects the representation of visual information in area V4 of monkeys. As such, it is important not only for understanding vision but also for determining how working memory impacts perceptual signals and their underlying circuits. The data provide convincing evidence of a direct communication between prefrontal circuits that store spatial information and V4, which, under the current experimental conditions, manifests mainly as changes in temporal activity patterns (oscillations).

Reviewer #1 (Public review):

Summary:

This study investigates what happens to the stimulus-driven responses of V4 neurons when an item is held in working memory. Monkeys are trained to perform memory guided saccades: they must remember the location of a visual cue and then, after a delay, make an eye movement to the remembered location. In addition, a background stimulus (a grating) is presented that varies in contrast and orientation across trials. This stimulus serves to probe the V4 responses, is present throughout the trial, and is task-irrelevant. Using this design, the authors report memory-driven changes in the LFP power spectrum, changes in synchronization between the V4 spikes and the ongoing LFP, and no significant changes in firing rate.

Strengths:

- The logic of the experiment is nicely laid out.

- The presentation is clear and concise.

- The analyses are thorough, careful, and yield unambiguous results.

- Together, the recording and inactivation data demonstrate quite convincingly that the signal stored in FEF is communicated to V4 and that, under the current experimental conditions, the impact from FEF manifests as variations in the timing of the stimulus-evoked V4 spikes and not in the intensity of the evoked activity (i.e., firing rate).

Weaknesses:

The weaknesses I noted in the first round of reviews were effectively addressed by the authors. In particular, the expanded discussion on the overlapping effects of attention, working memory, and motor planning does a great job putting the current findings against the wider context concerning the neural mechanisms of visuomotor guidance.

I think this is a well-designed and well-executed study that helps to better outline the relationship between perception and working memory given their respective neural substrates. A broad range of systems neuroscientists and experimental psychologists will find it illuminating.

Reviewer #2 (Public review):

Summary:

It is generally believed that higher-order areas in the prefrontal cortex guide selection during working memory and attention through signals that selectively recruiting neuronal populations in sensory areas that encode the relevant feature. In this work, Parto-Dezfouli and colleagues tested how these prefrontal signals influence activity in visual area V4 using a spatial working memory task. They recorded neuronal activity from visual area V4 and found that information about visual features at the behaviorally relevant part of space during the memory period is carried in a spatially selective manner in the timing of spikes relative to a beta oscillation (phase coding) rather than in the average firing rate (rate code). The authors further tested whether there is a causal link between prefrontal input and the phase encoding of visual information during the memory period. They found that indeed inactivation of the frontal eye fields, a prefrontal area known to send spatial signal to V4, decreased beta oscillatory activity in V4 and information about the visual features. The authors went one step further to develop a neural model that replicated the experimental findings and suggested that changes in the average firing rate of individual neurons might be a result of small changes in the exact beta oscillation frequency within V4. These data provide important new insights on the possible mechanisms through which top-down signals can influence activity in hierarchically lower sensory areas and can therefore have a significant impact on the Systems, Cognitive and Computational Neuroscience fields.

Strengths:

This is a well-written paper with a well-thought-out experimental design. The authors used a smart variation of the memory-guided saccade task to assess how information about the visual features of stimuli is encoded during the memory period. By using a grating of various contrasts and orientations as the background the authors ensured that bottom-up visual input would drive responses in visual area V4 in the delay period, something that is not commonly done in experimental settings in the same task. Moreover, one of the major strengths of the study is the use of different approaches including analysis of electrophysiological data using advanced computational methods of analysis, manipulation of activity through inactivation of prefrontal cortex to establish causality of top-down signals on local activity signatures (beta oscillations, spike locking and information carried) as well as computational neuronal modeling. This has helped extend an observation into a possible mechanism well supported by the results.

Weaknesses:

Although the authors provide support for their conclusions from different approaches, a few conceptual gaps make it harder for the reader to appreciate the mechanisms that lead to the observed results and evaluate whether and how these may apply to other cases of top-down control. The fact that the visual features under study were behaviorally irrelevant make it difficult to appreciate the relevance of the finding and its relation to top-down spatial attention mechanisms that involve similar/overlapping circuits. In the same vein, the use of the memory-guided saccade task has certain disadvantages in the context of this study. Although delay activity is interpreted as memory activity by the authors, it is in principle possible that it reflects preparation for the upcoming saccade, spatial attention (particularly since there is a stimulus in the RF) etc. This could potentially change the conclusion and perspective.

Moreover, encoding of the two visual features that are manipulated in the context of the study (contrast and orientation) seems to be affected differently in certain cases, which leaves a reader wondering about the source of this variability.

Finally, although the study provides evidence in favor of a role of FEF in influencing phase coding of visual features in V4 in beta frequencies, important analysis that could have revealed the long-range mechanisms of such an effect including the analysis of intra-FEF and interareal (FEF-V4) neuronal interactions is missing from this paper

Reviewer #3 (Public review):

Summary:

In this report, the authors test the necessity of prefrontal cortex (specifically, FEF) activity in driving changes in oscillatory power, spike rate, and spike timing of extrastriate visual cortex neurons during a visual spatial working memory (WM) task. The authors recorded LFP and spikes in V4 while macaques remembered a single spatial location over a delay period during which task-irrelevant background gratings were displayed on the screen with varying orientation and contrast. V4 oscillations (in the beta range) scaled with WM maintenance, and the information encoded by spike timing relative to beta band LFP about the task-irrelevant background orientation depended on remembered location. They also compared recorded signals in V4 with and without muscimol inactivation of FEF, demonstrating the importance of FEF input for WM-induced changes in oscillatory amplitude, phase coding, and information encoded about background orientations. Finally, they built a network model that can account for some of these results. Together, these results show that FEF provides meaningful input to visual cortex that is used to alter neural activity, and that these signals can impact information coding of task-irrelevant information during a WM delay.

Strengths:

- Elegant and robust experiment that allows for clear tests for the necessity of FEF activity in WM-induced changes in V4 activity<br /> - Comprehensive and broad analyses of interactions between LFP and spike timing provide compelling evidence for FEF-modulated phase coding of task-irrelevant stimuli at remembered location<br /> - Convincing modeling efforts

Comments on revisions:

I have no further comments for the authors. The revised manuscript appears to have adequately addressed the substantial comments raised in the previous round of review. I especially appreciate the addition of a new supplementary figure analyzing the data when no background stimulus was presented.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

This study investigates what happens to the stimulus-driven responses of V4 neurons when an item is held in working memory. Monkeys are trained to perform memory-guided saccades: they must remember the location of a visual cue and then, after a delay, make an eye movement to the remembered location. In addition, a background stimulus (a grating) is presented that varies in contrast and orientation across trials. This stimulus serves to probe the V4 responses, is present throughout the trial, and is task-irrelevant. Using this design, the authors report memory-driven changes in the LFP power spectrum, changes in synchronization between the V4 spikes and the ongoing LFP, and no significant changes in firing rate.

Strengths:

(1) The logic of the experiment is nicely laid out.

(2) The presentation is clear and concise.

(3) The analyses are thorough, careful, and yield unambiguous results.

(4) Together, the recording and inactivation data demonstrate quite convincingly that the signal stored in FEF is communicated to V4 and that, under the current experimental conditions, the impact from FEF manifests as variations in the timing of the stimulus-evoked V4 spikes and not in the intensity of the evoked activity (i.e., firing rate).

Weaknesses:

I think there are two limitations of the study that are important for evaluating the potential functional implications of the data. If these were acknowledged and discussed, it would be easier to situate these results in the broader context of the topic, and their importance would be conveyed more fairly and transparently.

(1) While it may be true that no firing rate modulations were observed in this case, this may have been because the probe stimuli in the task were behaviorally irrelevant; if anything, they might have served as distracters to the monkey's actual task (the MGS). From this perspective, the lack of rate modulation could simply mean that the monkeys were successful in attending the relevant cue and shielding their performance from the potentially distracting effect of the background gratings. Had the visual probes been in some way behaviorally relevant and/or spatially localized (instead of full field), the data might have looked very different.

Any task design involves tradeoffs; if the visual stimulus was behaviorally relevant, then any observed neurophysiological changes would be more confounded by possible attentional effects. We cannot exclude the possibility that a different task or different stimuli would produce different results; we ourselves have reported firing rate enhancements for other types of visual probes during an MGS task (Merrikhi et al. 2017). We have added an acknowledgement of these limitations in the discussion section (lines 323-330 in untracked version). At minimum, our results show a dissociation between the top-down modulation of phase coding, which is enhanced during WM even for these task-irrelevant stimuli, and rate coding. Establishing whether and how this phase coding is related to perception and behavior will be an important direction for future work.

With this in mind, it would be prudent to dial down the tone of the conclusions, which stretch well beyond the current experimental conditions (see recommendations).

We have edited the title (removing the word ‘primarily’) and key sentences throughout to tone down the conclusions, generally to state that the importance of a phase code in WM modulations is *possible* given the observed results, rather than certain (see abstract lines 26-27, introduction lines 59-62, conclusion lines 310-311).

(2) Another point worth discussing is that although the FEF delay-period activity corresponds to a remembered location, it can also be interpreted as an attended location, or as a motor plan for the upcoming eye movement. These are overlapping constructs that are difficult to disentangle, but it would be important to mention them given prior studies of attentional or saccade-related modulation in V4. The firing rate modulations reported in some of those cases provide a stark contrast with the findings here, and I again suspect that the differences may be due at least in part to the differing experimental conditions, rather than a drastically different encoding mode or functional linkage between FEF and V4.

We have added a paragraph to the discussion section addressing links to attention and motor planning (lines 315-333), and specifically acknowledging the inherent difficulties of fully dissociating these effects when interpreting our results (lines 323-330).

Reviewer #2 (Public review):

Summary:

It is generally believed that higher-order areas in the prefrontal cortex guide selection during working memory and attention through signals that selectively recruit neuronal populations in sensory areas that encode the relevant feature. In this work, Parto-Dezfouli and colleagues tested how these prefrontal signals influence activity in visual area V4 using a spatial working memory task. They recorded neuronal activity from visual area V4 and found that information about visual features at the behaviorally relevant part of space during the memory period is carried in a spatially selective manner in the timing of spikes relative to a beta oscillation (phase coding) rather than in the average firing rate (rate code). The authors further tested whether there is a causal link between prefrontal input and the phase encoding of visual information during the memory period. They found that indeed inactivation of the frontal eye fields, a prefrontal area known to send spatial signals to V4, decreased beta oscillatory activity in V4 and information about the visual features. The authors went one step further to develop a neural model that replicated the experimental findings and suggested that changes in the average firing rate of individual neurons might be a result of small changes in the exact beta oscillation frequency within V4. These data provide important new insights into the possible mechanisms through which top-down signals can influence activity in hierarchically lower sensory areas and can therefore have a significant impact on the Systems, Cognitive, and Computational Neuroscience fields.

Strengths:

This is a well-written paper with a well-thought-out experimental design. The authors used a smart variation of the memory-guided saccade task to assess how information about the visual features of stimuli is encoded during the memory period. By using a grating of various contrasts and orientations as the background the authors ensured that bottom-up visual input would drive responses in visual area V4 in the delay period, something that is not commonly done in experimental settings in the same task. Moreover, one of the major strengths of the study is the use of different approaches including analysis of electrophysiological data using advanced computational methods of analysis, manipulation of activity through inactivation of the prefrontal cortex to establish causality of top-down signals on local activity signatures (beta oscillations, spike locking and information carried) as well as computational neuronal modeling. This has helped extend an observation into a possible mechanism well supported by the results.

Weaknesses:

Although the authors provide support for their conclusions from different approaches, I found that the selection of some of the analyses and statistical assessments made it harder for the reader to follow the comparison between a rate code and a phase code. Specifically, the authors wish to assess whether stimulus information is carried selectively for the relevant position through a firing rate or a phase code. Results for the rate code are shown in Figures 1B-G and for the phase code are shown in Figure 2. Whereas an F-statistic is shown over time in Figure 1F (and Figure S1) no such analysis is shown for LFP power. Similarly, following FEF inactivation there is no data on how that influences V4 firing rates and information carried by firing rates in the two conditions (for positions inside and outside the V4 RF). In the same vein, no data are shown on how the inactivation affects beta phase coding in the OUT condition.

Per the reviewer’s suggestion, we have added several new supplementary figures. We now show the F-statistic for discriminability over time for the LFP timecourse (Fig. S2), and as a function of power in various frequencies (Fig. S4). We have added before/after inactivation comparisons of the LFP and spiking activity, and their respective F-statistics for discrimination between contrasts and orientations in Fig. S9. Lastly, we added a supplementary figure evaluating the impact of FEF inactivation on beta phase coding in the OUT condition, showing no significant change (Fig. S11).

Moreover, some of the statistical assessments could be carried out differently including all conditions to provide more insight into mechanisms. For example, a two-way ANOVA followed by post hoc tests could be employed to include comparisons across both spatial (IN, OUT) and visual feature conditions (see results in Figures 2D, S4, etc.). Figure 2D suggests that the absence of selectivity in the OUT condition (no significant difference between high and low contrast stimuli) is mainly due to an increase in slope in the OUT condition for the low contrast stimulus compared to that for the same stimulus in the IN condition. If this turns out to be true it would provide important information that the authors should address.

We have updated the STA slope measurement, excluding the low contrast condition which lacks a clear peak in the STA. Additionally, we equalized the bin widths and aligned the x-axes for better visual comparability. Then, we performed a two-way ANOVA, analyzing the effects of spatial features (IN vs. OUT) and visual conditions (contrast and orientation). The results showed a significant effect of the visual feature on both orientation (F = 3.96, p=0.046) and contrast (F = 14.26, p<10^-3). However, neither the spatial feature nor the spatial-visual interaction exhibited significant effects for orientation (F = 0.52, p=0.473, F=1.56, p=0.212) or contrast (F = 2.19, p=0.139, F=1.15, p=0.283).

There are also a few conceptual gaps that leave the reader wondering whether the results and conclusion are general enough. Specifically,

(1) The authors used microstimulation in the FEF to determine RFs. It is thus possible that the FEF sites that were inactivated were largely more motor-related. Given that beta oscillations and motor preparatory activity have been found to be correlated and motor sites show increased beta oscillatory activity in the delay period, it is possible that the effect of FEF inactivation on V4 beta oscillations is due to inactivation of the main source of beta activity. Had the authors inactivated sites with a preponderance of visual neurons in the FEF would the results be different?

We do not believe this to be likely based on what is known anatomically and functionally about this circuitry. Anatomically, the projections from FEF to V4 arise primarily from the supragranular layers, not layers which contain the highest proportion of motor activity (Barone et al. 2000, Pouget et al. 2009, Markov et al. 2013). Functionally, based on electrical identification of V4-projecting FEF neurons, we know that FEF to V4 projections are predominantly characterized by delay rather than motor activity (Merrikhi et al. 2017). We have now tried to emphasize these points when we introduce the inactivation experiments (lines 185-186).

Experimentally, the spread of the pharmacological effect with our infusion system is quite large relative to any clustering of visual vs. motor neurons within the FEF, with behavioral consequences of inactivation spreading to cover a substantial portion of the visual hemifield (e.g., Noudoost et al. 2014, Clark et al. 2014), and so our manipulation lacks the spatial resolution to selectively target motor vs. other FEF neurons.

(2) Somewhat related to this point and given the prominence of low-frequency activity in deeper layers of the visual cortex according to some previous studies, it is not clear where the authors' V4 recordings were located. The authors report that they do have data from linear arrays, so it should be possible to address this.

Unfortunately, our chamber placement for V4 has produced linear array penetration angles which do not reliably allow identification of cortical layers. We are aware of previous results showing layer-specific effects of attention in V4 (e.g., Pettine et al. 2019, Buffalo et al. 2011), and it would indeed be interesting to determine whether our observed WM-driven changes follow similar patterns. We may be able to analyze a subset of the data with current source density analysis to look for layer-specific effects in the future, but are not able to provide any information at this time.

(3) The authors suggest that a change in the exact frequency of oscillation underlies the increase in firing rate for different stimulus features. However, the shift in frequency is prominent for contrast but not for orientation, something that raises questions about the general applicability of this observation for different visual features.

While the shift in peak frequency across contrasts is more prominent than that across orientations (Fig. S3A-B), the relationship between orientation and peak frequency is also significant (one-way ANOVA for peak frequency across contrasts, F_Contrast=10.72, p<10^-4; or across orientations, F_Orientation=3, p=0.030; stats have been added to Fig. S3 caption). This finding also aligns with previous studies, which reported slight peak frequency shifts (~1–2 Hz) in the context of attention (Fries, 2015). To address the question of whether the frequency-firing rate correlation generalizes to orientation-driven changes, we now examine the relationship between peak frequency and firing rate separately for each contrast level (Fig. S14). The average normalized response as a function of peak frequency, pooled across subsamples of trials from each of 145 V4 neurons (100 subsamples/neuron), IN vs. OUT conditions, shows a significant correlation during the delay period for each contrast (contrast low (F_Condition=0.03, p=0.867; F_Frequency=141.86, p<10^-18; F_Interaction=10.70, p=0.002, ANCOVA), contrast middle (F_Condition=7.18, p=0.009; F_Frequency=96.76, p<10^-14; F_Interaction=0.13, p=0.716, ANCOVA), contrast high (F_Condition=12.51, p=0.001; F_Frequency=333.74, p<10^-29; F_Interaction=7.91, p=0.006, ANCOVA).

(4) One of the major points of the study is the primacy of the phase code over the rate code during the delay period. Specifically, here it is shown that information about the visual features of a stimulus carried by the rate code is similar for relevant and irrelevant locations during the delay period. This contrasts with what several studies have shown for attention in which case information carried in firing rates about stimuli in the attended location is enhanced relative to that for stimuli in the unattended location. If we are to understand how top-down signals work in cognitive functions it is inevitable to compare working memory with attention. The possible source of this difference is not clear and is not discussed. The reader is left wondering whether perhaps a different measure or analysis (e.g. a percent explained variance analysis) might reveal differences during the delay period for different visual features across the two spatial conditions.

We have added discussion regarding the relationship of these results to previous findings during attention in the discussion section (lines 315-333).

The use of the memory-guided saccade task has certain disadvantages in the context of this study. Although delay activity is interpreted as memory activity by the authors, it is in principle possible that it reflects preparation for the upcoming saccade, spatial attention (particularly since there is a stimulus in the RF), etc. This could potentially change the conclusion and perspective.

We have added a new discussion paragraph addressing the relationship to attention and motor planning (lines 315-333). We have also moderated the language used to describe our conclusions throughout the manuscript in light of this ambiguity.

For the position outside the V4 RF, there is a decrease in both beta oscillations and the clustering of spikes at a specific phase. It is therefore possible that the decrease in information about the stimuli features is a byproduct of the decrease in beta power and phase locking. Decreased oscillatory activity and phase locking can result in less reliable estimates of phase, which could decrease the mutual information estimates.

Looking at the SNR as a ratio of power in the beta band to all other bands, there is no significant drop in SNR between conditions (SNRIN = 4.074+-984, SNROUT = 4.333+-0.834 OUT, p=0.341, Wilcoxon signed-rank). Therefore, we do not think that the change in phase coding is merely a result of less reliable phase estimates.

The authors propose that coherent oscillations could be the mechanism through which the prefrontal cortex influences beta activity in V4. I assume they mean coherent oscillations between the prefrontal cortex and V4. Given that they do have simultaneous recordings from the two areas they could test this hypothesis on their own data, however, they do not provide any results on that.

This paper only includes inactivation data. We are working on analyzing the simultaneous recording data for a future publication.

The authors make a strong point about the relevance of changes in the oscillation frequency and how this may result in an increase in firing rate although it could also be the reverse - an increase in firing rate leading to an increase in the frequency peak. It is not clear at all how these changes in frequency could come about. A more nuanced discussion based on both experimental and modeling data is necessary to appreciate the source and role (if any) of this observation.

As the reviewer notes, it is difficult to determine whether the frequency changes drive the rate changes, vice versa, or whether both are generated in parallel by a common source. We have adjusted our language to reflect this (lines 291-293). Future modeling work may be able to shed more light on the causal relationships between various neural signatures.

Reviewer #3 (Public review):

Summary:

In this report, the authors test the necessity of prefrontal cortex (specifically, FEF) activity in driving changes in oscillatory power, spike rate, and spike timing of extrastriate visual cortex neurons during a visual-spatial working memory (WM) task. The authors recorded LFP and spikes in V4 while macaques remembered a single spatial location over a delay period during which task-irrelevant background gratings were displayed on the screen with varying orientation and contrast. V4 oscillations (in the beta range) scaled with WM maintenance, and the information encoded by spike timing relative to beta band LFP about the task-irrelevant background orientation depended on remembered location. They also compared recorded signals in V4 with and without muscimol inactivation of FEF, demonstrating the importance of FEF input for WM-induced changes in oscillatory amplitude, phase coding, and information encoded about background orientations. Finally, they built a network model that can account for some of these results. Together, these results show that FEF provides meaningful input to the visual cortex that is used to alter neural activity and that these signals can impact information coding of task-irrelevant information during a WM delay.

Strengths:

(1) Elegant and robust experiment that allows for clear tests for the necessity of FEF activity in WM-induced changes in V4 activity.

(2) Comprehensive and broad analyses of interactions between LFP and spike timing provide compelling evidence for FEF-modulated phase coding of task-irrelevant stimuli at remembered location.

(3) Convincing modeling efforts.

Weaknesses:

(1) 0% contrast background data (standard memory-guided saccade task) are not reported in the manuscript. While these data cannot be used to consider information content of spike rate/time about task-irrelevant background stimuli, this condition is still informative as a 'baseline' (and a more typical example of a WM task).

We have added a new supplementary figure to show the effect of WM on V4 LFP power and SPL in 0% contrast trials (Fig. S6). These results (increases in beta LFP power and SPL when remembering the V4 RF location) match our previous report for the effect of spatial WM on LFP power and SPL within extrastriate area MT (Bahmani et al. 2018).

(2) Throughout the manuscript, the primary measurements of neural coding pertain to task-irrelevant stimuli (the orientation/contrast of the background, which is unrelated to the animal's task to remember a spatial location). The remembered location impacts the coding of these stimulus variables, but it's unclear how this relates to WM representations themselves.

Indeed, here we have focused on how maintaining spatial WM impacts visual processing of incoming sensory information, rather than on how the spatial WM signal itself is represented and maintained. Behaviorally, this impact on visual signals could be related to the effects of the content of WM on perception and reaction times (e.g., Soto et al. 2008, Awh et al. 1998, Teng et al. 2019), but no such link to behavior is shown in our data.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

As mentioned above, the two points I raised in the public review merit a bit of development in the Discussion. In addition, the authors should revise some of their conclusions.

For instance (L217):

"The finding that WM mainly modulates phase coded information within extrastriate areas fundamentally shifts our understanding of how the top-down influence of prefrontal cortex shapes the neural representation, suggesting that inducing oscillations is the main way WM recruits sensory areas."

In my opinion, this one is over-the-top on various counts.

Here is another exaggerated instance (L298):

"...leading us to conclude that representations based on the average firing rate of neurons are not the primary way that top-down signals enhance sensory processing."

Again, as noted above, the problem is that one could make the case that the top-down signals are, in fact, highly effective, since they are completely quashing any distracter-related modulation in firing rate across RFs. There is only so much that one can conclude from responses to stimuli that are task-irrelevant, uniform across space, and constant over the course of a trial.

I think even the title goes too far. What the work shows, by all accounts, is that the sustained activity in FEF has a definitive impact on V4 *even* with respect to a sustained, irrelevant background stimulus. The result is very robust in this sense. However, this is quite different from saying that the *primary* means of functional control for FEF is via phase coding. Establishing that would require ruling out other forms of control (i.e., rate coding) in all or a wide range of experimental conditions. That is far from the restricted set of conditions tested here and is also at variance with many other experiments demonstrating effects of attention or even FEF microstimulation on V4 firing activity.

To reiterate, in my opinion, the work is carefully executed and the data are interesting and largely unambiguous. I simply take issue with what can be reliably concluded, and how the results fit with the rest of the literature. Revisions along these lines would improve the readability of the paper considerably.

We have edited the title (removing the word ‘primarily’) and key sentences throughout to tone down the conclusions, generally to state that the importance of a phase code in WM modulations is *possible* given the observed results, rather than certain (see abstract lines 26-27, introduction lines 59-62, conclusion lines 310-311).

Reviewer #3 (Recommendations for the authors):

(1) My primary comment that came up multiple times as I read the manuscript (and which is summarized above) is that I wasn't ever sure why the authors are focused on analyzing neural coding of task-irrelevant sensory information during a WM task as a function of WM contents (remembered location). Most studies of neural codes supporting WM often focus on coding the remembered information - not other information. Conceptually, it seems that the brain would want to suppress - or at least not enhance - representations of task-irrelevant information when performing a demanding task, especially when there is no search requirement, and when there is no feature correspondence between the remembered and viewed stimuli. (i.e., the interaction between WM and visual input is more obvious for visual search for a remembered target). Why, in theory, would a visual region need to improve its coding of non-remembered information as a function of WM? This isn't meant to detract from the results, which are indeed very interesting and I think quite informative. The authors are correct that this is certainly relevant for sensory recruitment models of WM - there's clear evidence for a role of feedback from PFC to extrastriate cortex - but what role, specifically, each region plays in this task is critical to describe clearly, especially given the task-irrelevance of the input. Put another way: what if the animal was remembering an oriented grating? In that case, MI between spike-based measures and orientation would be directly relevant to questions of neural WM representations, as the remembered feature is itself being modeled. But here, the focus seems to be on incidental coding.

Indeed, here we have focused on how maintaining spatial WM impacts visual processing of incoming sensory information, rather than on how the spatial WM signal itself is represented and maintained. Behaviorally, this impact on visual signals could be related to the effects of the content of WM on perception and reaction times (e.g., Soto et al. 2008, Awh et al. 1998, Teng et al. 2019), but no such link to behavior is shown in our data.

Whether similar phase coding is also used to represent the content of object WM (for example, if the animal was remembering an oriented grating), or whether phase coding is only observed for WM’s modulation of the representation of incoming sensory signals, is an important question to be addressed in future work.

(2) Related to the above, the phrasing of the second sentence of the Discussion (lines 291-292) is ambiguous - do the authors mean that the FEF sends signals that carry WM content to V4, or that FEF sends projections to V4, and V4 has the WM content? As presently phrased, either of these are reasonable interpretations, yet they're directly opposing one another (the next sentence clarifies, but I imagine the authors want to minimize any confusion).

We have edited this sentence to read, “Within prefrontal areas, FEF sends direct projections to extrastriate visual areas, and activity in these projections reflects the content of WM.”

(3) I'm curious about how the authors consider the spatial WM task here different from a cued spatial attention task. Indeed, both require sustained use of a location for further task performance. The section of the Discussion addressing similar results with attention (lines 307-311) presently just summarizes the similarities of results but doesn't offer a theoretical perspective for how/why these different types of tasks would be expected to show similar neural mechanisms.

We have added discussion regarding the relationship of these results to previous findings during attention in the discussion section (lines 315-333).

(4) As far as I can tell, there is no consideration of behavioral performance on the memory-guided saccade task (RT, precision) across the different stimulus background conditions. This should be reported for completeness, and to determine whether there is an impact of the (likely) task-irrelevant background on task performance. This analysis should also be reported for Figure 3's results characterizing how FEF inactivation disrupts behavior (if background conditions were varied, see point 7 below).

We have added the effect of inactivation on behavioral RT and % correct across the different stimulus background conditions (Fig. S8). Background contrast and orientation did not impact either RT or % correct.

(5) Results from Figure 2 (especially Figures 2A-B) concerning phase-locked spiking in V4 should be shown for 0%-contrast trials as well, as these trials better align with 'typical' WM tasks.

We have added a new supplementary figure to show the effect of WM on V4 LFP power and SPL in 0% contrast trials (Fig. S6). These results (increases in beta LFP power and SPL) match our previous report for the effect of spatial WM on LFP power and SPL within extrastriate area MT (Bahmani et al. 2018).

(6) The magnitude of SPL difference in aggregate (Figure 2B) is much, much smaller than that of the example site shown (Figure 2A), such that Figure 2A's neuron doesn't appear to be visible on Figure 2B's scatterplot. Perhaps a more representative sample could be shown? Or, the full range of x/y axes in Figure 2B could be plotted to illustrate the full distribution.

We have updated Fig. 2A with a more representative sample neuron.

(7) I'm a bit confused about the FEF inactivation experiments. In the Methods (lines 512-513), the authors mention there was no background stimulus presented during the inactivation experiment, and instead, a typical 8-location MGS task was employed. However, in the results on pg 8 (Lines 201-214), and Figure 3G, the authors quantify a phase code MI. The previous phase code MI analysis was looking at MI between each spike's phase and the background stimulus - but if there's no background, what's used to compute phase code MI? Perhaps what they meant to write was that, in addition to the primary task with a manipulation of background properties, an 8-location MGS task was additionally employed.

The reviewer is correct that both tasks were used after inactivation (the 8-location task to assess the spread of the behavioral effect of inactivation, and the MGS-background task for measuring MI). We have edited the methods text to clarify.

(8) How is % Correct defined for the MGS task? (what is the error threshold? Especially for the results described in lines 192-193).

The % correct is defined as correct completed trials divided by the total number of trials; the target window was a circle with radius of 2 or 4 dva (depending on cue eccentricity). These details have been added to the Methods.

(9) The paragraph from lines 183-200 describes a number of behavioral results concerning "scatter" and "RT" - the RT shown seems extremely high, and perhaps is normalized. Details of this normalization should be included in the Methods. The "scatter" is listed as dva, but it's not clear how scatter is quantified (std dev of endpoint distribution? Mean absolute error), nor how target eccentricity is incorporated (as scatter is likely higher for greater target eccentricity).

We have renamed ‘scatter’ to ‘saccade error’ in the text to match the figure, and now provide details in the Methods section. Both RT and saccade error are normalized for each session, details are now provided in the Methods. Since error was normalized for each session before performing population statistics, no other adjustment for eccentricity was made.

eLife Assessment

This important study investigates how AD(H)D affects attention using neural and physiological measures in a Virtual Reality (VR) environment. Solid evidence is provided that individuals diagnosed with AD(H)D differ from control participants in both the encoding of the target sound and the encoding of acoustic interference. The VR paradigm here can potentially bridge lab experiments and real-life experiments. The study is of potential interests to researchers who are interested in auditory cognition, education, and ADHD.

Reviewer #1 (Public review):

Summary:

This is an interesting study on AD(H)D. The authors combine a variety of neural and physiological metrics to study attention in a VR classroom setting. The manuscript is well written and the results are interesting, ranging from an effect of group (AD(H)D vs. control) on metrics such as envelope tracking, to multivariate regression analyses considering alpha-power, gaze, TRF, ERPs, and behaviour simultaneously. I find the first part of the results clear and strong. The multivariate analyses in Tables 1 and 2 are good ideas, but I think they would benefit from additional clarifications. Overall, I think that the methodological approach is useful in itself. The rest is interesting in that it informs us on which metrics are sensitive to group-effects and correlated with each other. I think this might be one interesting way forward. Indeed, much more work is needed to clarify how these results change with different stimuli and tasks. So, I see this as an interesting first step into more naturalistic measurement of speech attention.

Strengths:

I praise the authors for this interesting attempt to tackle a challenging topic with naturalistic experiment and metrics. I think the results broadly make sense and they contribute to a complex literature that is far from being linear and cohesive.

Weaknesses:

The authors have successfully addressed most of my concerns during the review process. Some weaknesses remain in this resubmission, but they do not make the results invalid. For example:<br /> - The EEG data was filtered twice, which is not recommended as that can introduce additional filtering artifacts. So, while I definitely do not recommend doing that, I do not expect that issue to have an impact on this specific result.<br /> - The authors did not check whether participants were somewhat familiar with the topics in the speech material. The authors agreed that this point might be beneficial for future research.<br /> - The hyperparameter tuning is consistent with previous work from the authors, and it involves selecting the optimal lambda value of the regularized regression based on the group average, thus choosing a single lambda value for all participants. In my opinion, that is not the optimal way to run those models, and I do not generally recommend using this approach. The reason is that the lambda can change depending on the magnitude of the signals and the SNR, leading to different optimal lambdas for distinct participants. On the other hand, finding those optimal lambda values for individual participants can be difficult depending on the amount of data and amount of noise, so it is sometimes necessary to apply strategies that ensure an appropriate choice of lambda. Using the group average as a metric for hyperparameter tuning produces a more stable metric and lambda value selection, which might be preferrable (even though this choice should not be taken lightly). In this specific case, I think the authors had a good reason to do so.

Comments on revisions:

The authors have done a great job at addressing my comments. I don't have any further concerns. Congratulations!

Reviewer #2 (Public review):

Summary:

While selective attention is a crucial ability of human beings, previous studies on selective attention are primarily conducted in a strictly controlled context, leaving a notable gap in underlying the complexity and dynamic nature of selective attention in a naturalistic context. This issue is particularly important for classroom learning in individuals with ADHD, as selecting the target and ignoring the distractions are pretty difficult for them but are the pre-requirement of effective learning. The authors of this study have addressed this challenge using a well-motivated study. I believe the findings of this study will be a nice addition to the fields both cognitive neuroscience and educational neuroscience.

Strengths:

To achieve the purpose of setting up a naturalistic context, the authors have based their study on a novel Virtual Reality platform. This is clever as it is usually difficult to perform such a study in the real classroom. Moreover, various techniques such as brain imaging, eye-tracking and physiological measurement are combined to collect multi-level data. They found that, different from the controls, individuals with ADHD had higher neural responses to the irrelevant rather than the target sounds, reduced speech tracking of the teacher. Additionally, the power of alpha-oscillations and frequency of gaze-shifts away from the teacher are found to be associated with the ADHD symptoms. These results provide new insights into the mechanism of selective attention among ADHD populations.

Weaknesses:

It is worth noting that nowadays there has been some studies trying to do so in the real classroom, and thus the authors should acknowledge the difference between the virtual and real classroom context and foresee the potential future changes.<br /> The approach of combining multi-level data owns advantage to obtain reliable results, but also raises significant difficult for the readers to understand the main results.

- An appraisal of whether the authors achieved their aims, and whether the results support their conclusions.

As expected, individuals with ADHD showed anomalous pattern of neural responses, and eye-tracking pattern, compared to the controls. But there are also some similarities between groups such as amount of time paying attention to teachers, etc. In general, their conclusions are supported.

- A discussion of the likely impact of the work on the field, and the utility of the methods and data to the community.

The findings are an extension of previous efforts in understanding selective attention in the naturalistic context. The findings of this study are particularly helpful in inspiring teacher's practice and advancing the research of educational neuroscience. This study demonstrates, again, that it is important to understand the complexity of cognitive process in the naturalistic context.

Comments on revisions:

The authors have appropriately responded to my concerns. I do not have other comments. I do hope to see more data and results from the authors in future.

Reviewer #3 (Public review):

Summary:

The authors conducted a well-designed experiment, incorporating VR classroom scenes and background sound events, with both control and ADHD participants. They employed multiple neurophysiological measures, such as EEG, eye movements, and skin conductance, to investigate the mechanistic underpinnings of paying attention in class and the disruptive effects of background noise.

The results revealed that individuals with ADHD exhibited heightened sensory responses to irrelevant sounds and reduced tracking of the teacher's speech. Overall, this manuscript presented an ecologically valid paradigm for assessing neurophysiological responses in both control and ADHD groups. The analyses were comprehensive and clear, making the study potentially valuable for the application of detecting attentional deficits.

Strengths:

• The VR learning paradigm is well-designed and ecologically valid.

• The neurophysiological metrics and analyses are comprehensive, and two physiological markers are identified capable of diagnosing ADHD.

• The data shared could serve as a benchmark for future studies on attention deficits in ecologically valid scenarios.

Weaknesses:

• Several results are null results, i.e., no significant differences were found between ADHD and control populations.

Comments on revisions:

The authors have addressed all of my concerns with the original manuscript.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

(1) Line numbers are missing.

Added

(2) VR classroom. Was this a completely custom design based on Unity, or was this developed on top of some pre-existing code? Many aspects of the VR classroom scenario are only introduced (e.g., how was the lip-speech synchronisation done exactly?). Additional detail is required. Also, is or will the experiment code be shared publicly with appropriate documentation? It would also be useful to share brief example video-clips.

We have added details about the VR classroom programming to the methods section (p. 6-7), and we have now included a video-example as supplementary material.

“Development and programming of the VR classroom were done primarily in-house, using assets (avatars and environment) were sourced from pre-existing databases. The classroom environment was adapted from assets provided by Tirgames on TurboSquid (https://www.turbosquid.com/Search/Artists/Tirgames) and modified to meet the experimental needs. The avatars and their basic animations were sourced from the Mixamo library, which at the time of development supported legacy avatars with facial blendshapes (this functionality is no longer available in current versions of Mixamo). A brief video example of the VR classroom is available at: https://osf.io/rf6t8.

“To achieve realistic lip-speech synchronization, the teacher’s lip movements were controlled by the temporal envelope of the speech, adjusting both timing and mouth size dynamically. His body motions were animated using natural talking gestures.”

While we do intent to make the dataset publicly available for other researchers, at this point we are not making the code for the VR classroom public. However, we are happy to share it on an individual-basis with other researchers who might find it useful for their own research in the future.

(3) "normalized to the same loudness level using the software Audacity". Please specify the Audacity function and parameters.

We have added these details (p.7)

“All sound-events were normalized to the same loudness level using the Normalize function in the audio-editing software Audacity (theaudacityteam.org, ver 3.4), with the peak amplitude parameter set to -5 dB, and trimmed to a duration of 300 milliseconds.“

(4) Did the authors check if the participants were already familiar with some of the content in the mini-lectures?

This is a good point. Since the mini-lectures spanned many different topics, we did not pre-screen participants for familiarity with the topics, and it is possible that some of the participants had some pre-existing knowledge.

In hindsight, it would have been good to have added some reflective questions regarding participants prior knowledge as well as other questions such as level of interest in the topic and/or how well they understood the content. These are elements that we hope to include in future versions of the VR classroom.

(5) "Independent Component Analysis (ICA) was then used to further remove components associated with horizontal or vertical eye movements and heartbeats". Please specify how this selection was carried out.

Selection of ICA components was done manually based on visual inspection of their time-course patterns and topographical distributions, to identify components characteristic of blinks, horizontal eye-movements and heartbeats). Examples of these distinct components are provided in Author response image 1 below. These is now specified in the methods section.

Author response image 1.

(6) "EEG data was further bandpass filtered between 0.8 and 20 Hz". If I understand correctly, the data was filtered a second time. If that's the case, please do not do that, as that will introduce additional and unnecessary filtering artifacts. Instead, the authors should replace the original filter with this one (so, filtering the data only once). Please see de Cheveigne and Nelkn, Neuron, 2019 for an explanation. Also, please provide an explanation of the rationale for further restricting the cut-off bands in the methods section. Finally, further details on the filters should be included (filter type and order, for example).

Yes, the data was indeed filtered twice. The first filter is done as part of the preprocessing procedure, in order to remove extremely high- and low- frequency noise but retain most activity within the range of “neural” activity. This broad range is mostly important for the ICA procedure, so as to adequately separate between ocular and neural contribution to the recorded signal.

However, since both the speech tracking responses and ERPs are typically less broadband and are comprised mostly of lower frequencies (e.g., those that make up the speech-envelope), a second narrower filter was applied to improve TRF model-fit and make ERPs more interpretable.

In both cases we used a fourth order zero-phase Butterworth IIR filter with 1-seconds of padding, as implemented in the Fieldtrip toolbox. We have added these details to the manuscript.

(7) "(~ 5 minutes of data in total), which is insufficient for deriving reliable TRFs". That is a bit pessimistic and vague. What does "reliable" mean? I would tend to agree when talking about individual subject TRFs, which 5 min per participant can be enough at the group level. Also, this depends on the specific speech material. If the features are univariate or multivariate. Etc. Please narrow down and clarify this statement.

We determined that the data in the Quiet condition (~5 min) was insufficient for performing reliable TRF analysis, by assessing whether its predictive-power was significantly better than chance. As shown in Author response image 2 below, the predictive power achieved using this data was not higher than values obtained in permuted data (p = 0.43). Therefore, we did not feel that it was appropriate to include TRF analysis of the Quiet condition in this manuscript. We have now clarified this in the manuscript (p. 10)

Author response image 2.

(8) "Based on previous research in by our group (Kaufman & Zion Golumbic 2023), we chose to use a constant regularization ridge parameter (λ= 100) for all participants and conditions". This is an insufficient explanation. I understand that there is a previous paper involved. However, such an unconventional choice that goes against the original definition and typical use of these methods should be clearly reported in this manuscript.

We apologize for not clarifying this point sufficiently, and have added an explanation of this methodological choice (p.11):

“The mTRF toolbox uses a ridge-regression approach for L2 regularization of the model to ensure better generalization to new data. We tested a range of ridge parameter values (λ's) and used a leave-one-out cross-validation procedure to assess the model’s predictive power, whereby in each iteration, all but one trials are used to train the model, and it is then applied to the left-out trial. The predictive power of the model (for each λ) is estimated as the Pearson’s correlation between the predicted neural responses and the actual neural responses, separately for each electrode, averages across all iterations. We report results of the model with the λ the yielded the highest predictive power at the group-level (rather than selecting a different λ for each participant which can lead to incomparable TRF models across participants; see discussion in Kaufman & Zion Golumbic 2023).”

Assuming that the explanation will be sufficiently convincing, which is not a trivial case to make, the next issue that I will bring up is that the lambda value depends on the magnitude of input and output vectors. While the input features are normalised, I don't see that described for the EEG signals. So I assume they are not normalized. In that case, the lambda would have at least to be adapted between subjects to account for their different magnitude.

We apologize for omitting this detail – yes, the EEG signals were normalized prior to conducting the TRF analysis. We have updated the methods section to explicitly state this pre-processing step (p.10).

Another clarification, is that value (i.e., 100) would not be comparable either across subjects or across studies. But maybe the authors have a simple explanation for that choice? (note that this point is very important as this could lead others to use TRF methods in an inappropriate way - but I understand that the authors might have specific reasons to do so here). Note that, if the issue is finding a reliable lambda per subject, a more reasonable choice would be to use a fixed lambda selected on a generic (i.e., group-level) model. However selecting an arbitrary lambda could be problematic (e.g., would the results replicate with another lambda; and similarly, what if a different EEG system was used, with different overall magnitude, hence the different impact of the regularisation).

We fully agree that selecting an arbitrary lambda is problematic (esp across studies). As clarified above, the group-level lambda chosen here for the encoding more was data-driven, optimized based on group-level predictive power.

(9) "L2 regularization of the model, to reduce its complexity". Could the authors explain what "reduce its complexity" refers to?

Our intension here was to state that the L2 regularization constrains the model’s weights so that it can better generalize between to left-out data. However, for clarity we have now removed this statement.

(10) The same lambda value was used for the decoding model. From personal experience, that is very unlikely to be the optimal selection. Decoding models typically require a different (usually larger) lambda than forward models, which can be due to different reasons (different SNR of "input" of the model and, crucially, very different dimensionality).

We agree with the reviewer that treatment of regularization parameters might not be identical for encoding and decoding models. Our initial search of lambda parameters was limited to λ= 0.01 - 100, with λ= 100 showing the best reconstruction correlations. However, following the reviewer’s suggestion we have now broadened the range and found that, in fact reconstruction correlations are further improved and the best lambda is λ= 1000 (see Author response image 3 below, left panel). Importantly, the difference in decoding reconstruction correlations between the groups is maintained regardless of the choice of lambda (although the effect-size varies; see Author response image 3, right panel). We have now updated the text to reflect results of the model with λ= 1000.

Author response image 3.

(11) Skin conductance analysis. Additional details are required. For example, how was the linear interpolation done exactly? The raw data was downsampled, sure. But was an anti-aliasing filter applied? What filter exactly? What implementation for the CDA was run exactly?

We have added the following details to the methods section (p. 14):

“The Skin Conductance (SC) signal was analyzed using the Ledalab MATLAB toolbox (version 3.4.9; Benedek and Kaernbach, 2010; http://www.ledalab.de/) and custom-written scripts. The raw data was downsampled to 16Hz using FieldTrip's ft_resampledata function, which applies a built-in anti-aliasing low-pass filter to prevent aliasing artifacts. Data were inspected manually for any noticeable artifacts (large ‘jumps’), and if present were corrected using linear interpolation in Ledalab. A continuous decomposition analysis (CDA) was employed to separate the tonic and phasic SC responses for each participant. The CDA was conducted using the 'sdeco' mode (signal decomposition), which iteratively optimizes the separation of tonic and phasic components using the default regularization settings.”

(12) "N1- and P2 peaks of the speech tracking response". Have the authors considered using the N1-P2 complex rather than the two peaks separately? Just a thought.

This is an interesting suggestion, and we know that this has been used sometimes in more traditional ERP literature. In this case, since neither peak was modulated across groups, we did not think this would yield different results. However, it is a good point to keep in mind for future work.

(13) Figure 4B. The ticks are missing. From what I can see (but it's hard without the ticks), the N1 seems later than in other speech-EEG tracking experiments (where is closer to ~80ms). Could the authors comment on that? Or maybe this looks similar to some of the authors' previous work?

We apologize for this and have added ticks to the figure.

In terms of time-course, a N1 peak at around 100ms is compatible with many of our previous studies, as well as those from other groups.

(14) Figure 4C. Strange thin vertical grey bar to remove.

Fixed.

(15) Figure 4B: What about the topographies for the TRF weights? Could the authors show that for the main components?

Yes. The topographies of the main TRF components are similar to those of the predictive power and are compatible with auditory responses. We have added them to Figure 4B.

(16) Figure 4B: I just noticed that this is a grand average TRF. That is ok (but not ideal) only because the referencing is to the mastoids. The more appropriate way of doing this is to look at the GFP, instead, which estimates the presence of dipoles. And then look at topographies of the components. Averaging across channels makes the plotted TRF weaker and noisier. I suggest adding the GFP to the plot. Also, the colour scale in Figure 4A is deceiving, as blue is usually used for +/- in plots of the weights. While that is a heatmap, where using a single colour or even yellow to red would be less deceiving at first look. Only cosmetics, indeed. The result is interesting nonetheless!

We apologize for this, and agree with the reviewer that it is better not to average across EEG channels. In the revised Figure, we now show the TRFs based on the average of electrodes FC1, FC2, and FCz, which exhibited the strongest activity for the two main components.

Following the previous comment, we have also included the topographical representation of the TRF main components, to give readers a whole-head perspective of the TRF.

We have also fixed the color-scales.

We are glad that the reviewer finds this result interesting!

(17) Figure 4C. This looks like a missed opportunity. That metric shows a significant difference overall. But is that underpinned but a generally lower envelope reconstruction correlation, or by a larger deviation in those correlations (so, that metric is as for the control in some moments, but it drops more frequently due to distractibility)?

We understand the reviewer’s point here, and ideally would like to be able to address this in a more fine-grained analysis, for example on a trial-by-trial basis. However, the design of the current experiment was not optimized for this, in terms of (for example) number of trials, the distribution of sound-events and behavioral outcomes. We hope to be able to address this issue in our future research.

(18) I am not a fan of the term "accuracy" for indicating envelope reconstruction correlations. Accuracy is a term typically associated with classification. Regression models are typically measured through errors, loss, and sometimes correlations. 'Accuracy' is inaccurate (no joke intended).

We accept this comment and now used the term “reconstruction correlation”.

(19) Discussion. "The most robust finding in". I suggest using more precise terminology. For example, "largest effect-size".

We agree and have changed the terminology (p. 31).

(20) "individuals who exhibited higher alpha-power [...]". I probably missed this. But could the authors clarify this result? From what I can see, alpha did not show an effect on the group. Is this referring to Table 2? Could the authors elaborate on that? How does that reconcile with the non-significant effect of the group? In that same sentence, do you mean "and were more likely"? If that's the case, and they were more likely to report attentional difficulties, how is it that there is no group-effect when studying alpha?

Yes, this sentence refers to the linear regression models described in Figure 10 and in Table 2. As the reviewer correctly points out, this is one place where there is a discrepancy between the results of the between-group analysis (ADHD diagnosis yes/no) and the regression analysis, which treats ADHD symptoms as a continuum, across both groups. The same is true for the gaze-shift data, which also did not show a significance between-group effect but was identified in the regression analysis as contributing to explaining the variance in ADHD symptoms.

We discuss this point on pages 30-31, noting that “although the two groups are clearly separable from each other, they are far from uniform in the severity of symptoms experienced”, which motivated the inclusion of both analyses in this paper.

At the bottom of p. 31 we specifically address the similarities and differences between the between-group and regression-based results. In our opinion, this pattern emphasizes that while neither approach is ‘conclusive’, looking at the data through both lenses contributes to an overall better understanding of the contributing factors, as well as highlighting that “no single neurophysiological measure alone is sufficient for explaining differences between the individuals – whether through the lens of clinical diagnosis or through report of symptoms”.

(21) "why in the latter case the neural speech-decoding accuracy did not contribute to explaining ASRS scores [...]". My previous point 1 on separating overall envelope decoding from its deviation could help there. The envelope decoding correlation might go up and down due to SNR, while you might be more interested in the dynamics over time (i.e., looking at the reconstructions over time).

Again, we appreciate this comment, but believe that this additional analysis is outside the scope of what would be reliably-feasible with the current dataset. However, since the data will be made publicly available, perhaps other researchers will have better ideas as to how to do this.

(22) Data and code sharing should be discussed. Also, specific links/names and version numbers should be included for the various libraries used.

We are currently working on organizing the data to make it publicly available on the Open Science Project.

We have updated links and version numbers for the various toolboxes/software used, throughout the manuscript.

Reviewer #2:

(1) While it is highly appreciated to study selective attention in a naturalistic context, the readers would expect to see whether there are any potential similarities or differences in the cognitive and neural mechanisms between contexts. Whether the classic findings about selective attention would be challenged, rebutted, or confirmed? Whether we should expect any novel findings in such a novel context? Moreover, there are some studies on selective attention in the naturalistic context though not in the classroom, it would be better to formulate specific hypotheses based on previous findings both in the strictly controlled and naturalistic contexts.

Yes, we fully agree that comparing results across different contexts would be extremely beneficial and important.

The current paper serves as an important proof-first-concept demonstrating the plausibility and scientific potential of using combined EEG-VR-eyetracking to study neurophysiological aspects of attention and distractibility, but is also the basis for formulating specific hypothesis that will be tested in follow-up studies.

If fact, a follow up study is already ongoing in our lab, where we are looking into this point, by testing users in different VR scenarios (e.g., classroom, café, office etc.), and assessing whether similar neurophysiological patterns are observed across contexts and to what degree they are replicable within and across individuals. We hope to share these data with the community in the near future.

(2) Previous studies suggest handedness and hemispheric dominance might impact the processing of information in each hemisphere. Whether these issues have been taken into consideration and appropriately addressed?

This is an interesting point. In this study we did not specifically control for handedness/hemispheric dominance, since most of the neurophysiological measured used here are sensory/auditory in their nature, and therefore potentially invariant to handedness. Moreover, the EEG signal is typically not very sensitive to hemispheric dominance, at least for the measures used here. However, this might be something to consider more explicitly in future studies. Nonetheless, we have added handedness information to the Methods section (p. 5): “46 right-handed, 3 left-handed”

(3) It would be interesting to know how students felt about the Virtual Classroom context, whether it is indeed close to the real classroom or to some extent different.

Yes, we agree. Obviously, the VR classroom differs in many ways from a real classroom, in terms of the perceptual experience, social aspects and interactive possibilities. We did ask participants about their VR experience after the experiment, and most reported feeling highly immersed in the VR environment and engaged in the task, with a strong sense of presence in the virtual-classroom.

We note that, in parallel to the VR studies in our lab, we are also conducting experiments in real classrooms, and we hope that the cross-study comparison will be able to shed more light on these similarities/differences.

(4) One intriguing issue is whether neural tracking of the teacher's speech can index students' attention, as the tracking of speech may be relevant to various factors such as sound processing without semantic access.

Another excellent point. While separating the ‘acoustic’ and ‘semantic’ contributions to the speech tracking response is non-trivial, we are currently working on methodological approaches to do this (again, in future studies) following, for example, the hierarchical TRF approach used by Brodbeck et al. and others.

(5) There are many results associated with various metrics, and many results did not show a significant difference between the ADHD group and the control group. It is difficult to find the crucial information that supports the conclusion. I suggest the authors reorganize the results section and report the significant results first, and to which comparison(s) the readers should pay attention.

We apologize if the organization of the results section was difficult to follow. This is indeed a challenge when collecting so many different neurophysiological metrics.

To facilitate this, we have now added a paragraph at the beginning of the result section, clarifying its structure (p.16):

The current dataset is extremely rich, consisting of many different behavioral, neural and physiological responses. In reporting these results, we have separated between metrics that are associated with paying attention to the teacher (behavioral performance, neural tracking of the teacher’s speech, and looking at the teacher), those capturing responses to the irrelevant sound-events (ERPs and event-related changes in SC and gaze); as well as more global neurophysiological measures that may be associated with the listeners’ overall ‘state’ of attention or arousal (alpha- and beta-power and tonic SC).

Moreover, within each section we have ordered the analysis such that the ones with significant effects are first. We hope that this contributes to the clarity of the results section.

(6) The difference between artificial and non-verbal humans should be introduced earlier in the introduction and let the readers know what should be expected and why.

We have added this to the Introduction (p. 4)

(7) It would be better to discuss the results against a theoretical background rather than majorly focusing on technical aspects.

We appreciate this comment. In our opinion, the discussion does contain a substantial theoretical component, both regarding theories of attention and attention-deficits, and also regarding their potential neural correlates. However, we agree that there is always room for more in depth discussion.

Reviewer #3:

Major:

(1) While the study introduced a well-designed experiment with comprehensive physiological measures and thorough analyses, the key insights derived from the experiment are unclear. For example, does the high ecological validity provide a more sensitive biomarker or a new physiological measure of attention deficit compared to previous studies? Or does the study shed light on new mechanisms of attention deficit, such as the simultaneous presence of inattention and distraction (as mentioned in the Conclusion)? The authors should clearly articulate their contributions.

Thanks for this comment.

We would not say that this paper is able to provide a ‘more sensitive biomarker’ or a ‘new physiological measure of attention’ – in order to make those type of grand statements we would need to have much more converging evidence from multiple studies and using both replication and generalization approaches.

Rather, from our perspective, the key contribution of this work is in broadening the scope of research regarding the neurophysiological mechanisms involved in attention and distraction.

Specifically, this work:

(1) Offers a significant methodological advancement of the field – demonstrating the plausibility and scientific potential of using combined EEG-VR-eyetracking to study neurophysiological aspects of attention and distractibility in contexts that ‘mimic’ real-life situations (rather than highly controlled computerized tasks).

(2) Provides a solid basis formulating specific mechanistic hypothesis regarding the neurophysiological metrics associated with attention and distraction, the interplay between them, and their potential relation to ADHD-symptoms. Rather than being an end-point, we see these results as a start-point for future studies that emphasize ecological validity and generalizability across contexts, that will hopefully lead to improved mechanisms understanding and potential biomarkers of real-life attentional capabilities (see also response to Rev #2 comment #1 above).

(3) Highlights differences and similarities between the current results and those obtained in traditional ‘highly controlled’ studies of attention (e.g., in the way ERPs to sound-events differ between ADHD and controls; variability in gaze and alpha-power; and more broadly about whether ADHD symptoms do or don’t map onto specific neurophysiological metrics). Again, we do not claim to give a definitive ’answer’ to these issues, but rather to provide a new type of data that can expands the conversation and address the ecological validity gap in attention research.

(2) Based on the multivariate analyses, ASRS scores correlate better with the physiological measures rather than the binary deficit category. It may be worthwhile to report the correlation between physiological measures and ASRS scores for the univariate analyses. Additionally, the correlation between physiological measures and behavioral accuracy might also be interesting.

Thanks for this. The beta-values reported for the regression analysis reflect the correlations between the different physiological measures and the ASRS scores (p. 30). From a statistical perspective, it is better to report these values rather than the univariate correlation-coefficients, since these represent the ‘unique’ relationship with each factor, after controlling for all the others.

The univariate correlations between the physiological measures themselves, as well as with behavioral accuracy, are reported in Figure 10

(3) For the TRF and decoding analysis, the authors used a constant regularization parameter per a previous study. However, the optimal regularization parameter is data-dependent and may differ between encoding and decoding analyses. Furthermore, the authors did not conduct TRF analysis for the quiet condition due to the limited ~5 minutes of data. However, such a data duration is generally sufficient to derive a stable TRF with significant predictive power (Mesik and Wojtczak, 2023).

The reviewer raises two important points, also raised by Rev #1 (see above).

Regarding the choice of regularization parameters, we have now clarified that although we used a common lambda value for all participants, it was selected in a data-driven manner, so as to achieve an optimal predictive power at the group-level.

See revised methods section:

“The mTRF toolbox uses a ridge-regression approach for L2 regularization of the model to ensure better generalization to new data. We tested a range of ridge parameter values (λ's) and used a leave-one-out cross-validation procedure to assess the model’s predictive power, whereby in each iteration, all but one trials are used to train the model, and it is then applied to the left-out trial. The predictive power of the model (for each λ) is estimated as the Pearson’s correlation between the predicted neural responses and the actual neural responses, separately for each electrode, averages across all iterations. We report results of the model with the λ the yielded the highest predictive power at the group-level (rather than selecting a different λ for each participant which can lead to incomparable TRF models across participants; see discussion in Kaufman & Zion Golumbic 2023).”

Regarding whether data was sufficient in the Quiet condition for performing TRF analysis – we are aware of the important work by Mesik & Wojtczak, and had initially used this estimate when designing our study. However, when assessing the predictive-power of the TRF model trained on data from the Quiet condition, we found that it was not significantly better than chance (see Author response image 2, ‘real’ predictive power vs. permuted data). Therefore, we ultimately did not feel that it was appropriate to include TRF analysis of the Quiet condition in this manuscript. We have now clarified this in the manuscript (p. 10)

(4) As shown in Figure 4, for ADHD participants, decoding accuracy appears to be lower than the predictive power of TRF. This result is surprising because more data (i.e., data from all electrodes) is used in the decoding analysis.

This is an interesting point – however, in our experience it is not necessarily the case that decoding accuracy (i.e., reconstruction correlation with the stimulus) is higher than encoding predictive-power. While both metrics use Pearson’s’ correlations, they quantify the similarity between two different types of signals (the EEG and the speech-envelope). Although the decoding procedure does use data from all electrodes, many of them don’t actually contain meaningful information regarding the stimulus, and thus could just as well hinder the overall performance of the decoding.

(5) Beyond the current analyses, the authors may consider analyzing inter-subject correlation, especially for the gaze signal analysis. Given that the area of interest during the lesson changes dynamically, the teacher might not always be the focal point. Therefore, the correlation of gaze locations between subjects might be better than the percentage of gaze duration on the teacher.

Thanks for this suggestion. We have tried to look into this, however working with eye-gaze in a 3-D space is extremely complex and we are not able to calculate reliable correlations between participants.

(6) Some preprocessing steps relied on visual and subjective inspection. For instance, " Visual inspection was performed to identify and remove gross artifacts (excluding eye movements) " (P9); " The raw data was downsampled to 16Hz and inspected for any noticeable artifacts " (P13). Please consider using objective processes or provide standards for subjective inspections.

We are aware of the possible differences between objective methods of artifact rejection vs. use of manual visual inspection, however we still prefer the manual (subjective) approach. As noted, in this case only very large artifacts were removed, exceeding ~ 4 SD of the amplitude variability, so as to preserve as many full-length trials as possible.

(7) Numerous significance testing methods were employed in the manuscript. While I appreciate the detailed information provided, describing these methods in a separate section within the Methods would be more general and clearer. Additionally, the authors may consider using a linear mixed-effects model, which is more widely adopted in current neuroscience studies and can account for random subject effects.

Indeed, there are many statistical tests in the paper, given the diverse types of neurophysiological data collected here. We actually thought that describing the statistics per method rather than in a separate “general” section would be easier to follow, but we understand that readers might diverge in their preferences.

Regarding the use of mixed-effect models – this is indeed a great approach. However, it requires deriving reliable metrics on a per-trial basis, and while this might be plausible for some of our metrics, the EEG and GSR metrics are less reliable at this level. This is why we ultimately chose to aggregate across trials and use a regular regression model rather than mixed-effects.

(8) Some participant information is missing, such as their academic majors. Given that only two lesson topics were used, the participants' majors may be a relevant factor.

To clarify – the mini-lectures presented here actually covered a large variety of topics, broadly falling within the domains of history, science and social-science and technology. Regarding participants’ academic majors, these were relatively diverse, as can be seen in Author response table 1 and Author response image 4.

Author response table 1.

Author response image 4.

(9) Did the multiple regression model include cross-validation? Please provide details regarding this.

Yes, we used a leave-one-out cross validation procedure. We have now clarified this in the methods section which now reads:

“The mTRF toolbox uses a ridge-regression approach for L2 regularization of the model to ensure better generalization to new data. We tested a range of ridge parameter values (λ's) and used a leave-one-out cross-validation procedure to assess the model’s predictive power, whereby in each iteration, all but one trials are used to train the model, and it is then applied to the left-out trial. The predictive power of the model (for each λ) is estimated as the Pearson’s correlation between the predicted neural responses and the actual neural responses, separately for each electrode, averages across all iterations. We report results of the model with the λ the yielded the highest predictive power at the group-level (rather than selecting a different λ for each participant which can lead to incomparable TRF models across participants; see discussion in Kaufman & Zion Golumbic 2023).”

Minor:

(10) Typographical errors: P5, "forty-nine 49 participants"; P21, "$ref"; P26, "Table X"; P4, please provide the full name for "SC" when first mentioned.

Thanks! corrected

eLife Assessment

In this useful study, the authors perform voltage imaging of CA1 pyramidal cells in head-fixed mice running on a track while local field potentials (LFPs) are recorded. The authors conclude that synchronous ensembles of neurons are differentially associated with different types of LFP patterns, namely theta and ripples. However, evidence for the claims in the paper remains incomplete, due to caveats of the experimental approach and claims that are based on a relatively sparse data set collected with a cutting-edge but still largely untested method.

Reviewer #1 (Public review):

Summary:

For many years, there has been extensive electrophysiological research investigating the relationship between local field potential patterns and individual cell spike patterns in the hippocampus. In this study, using state-of-the-art imaging techniques, they examined spike synchrony of hippocampal cells during locomotion and immobility states. In contrast to conventional understanding of the hippocampus, the authors demonstrated that hippocampal place cells exhibit prominent synchronous spikes locked to theta oscillations.

Strengths:

The voltage imaging used in this study is a highly novel method that allows recording not only suprathreshold-level spikes but also subthreshold-level activity. With its high frame rate, it offers time resolution comparable to electrophysiological recordings.

Comments on revisions: I have no further comments.

Reviewer #2 (Public review):

Summary:

This study employed voltage imaging in the CA1 region of the mouse hippocampus during the exploration of a novel environment. The authors report synchronous activity, involving almost half of the imaged neurons, occurred during periods of immobility. These events did not correlate with SWRs, but instead, occurred during theta oscillations and were phased locked to the trough of theta. Moreover, pairs of neurons with high synchronization tended to display non-overlapping place fields, leading the authors to suggest these events may play a role in binding a distributed representation of the context.

Strengths:

Technically this is an impressive study, using an emerging approach that allows single cell resolution voltage imaging in animals, that while head-fixed, can move through a real environment. The paper is written clearly and suggests novel observations about population level activity in CA1.

Comments on revisions:

I have no further major requests and thank the authors for the additional data and analyses.

Reviewer #3 (Public review):

Summary:

In the present manuscript, the authors use a few minutes of voltage imaging of CA1 pyramidal cells in head fixed mice running on a track while local field potential (LFPs) are recorded. The authors suggest that synchronous ensembles of neurons are differentially associated with different types of LFP patterns, theta and ripples. The experiments are flawed in that the LFP is not "local" but rather collected the other side of the brain.

Strengths:

The authors use a cutting-edge technique.

Weaknesses:

Although the authors have toned down their claims, the statement in the title ("Synchronous Ensembles of Hippocampal CA1 Pyramidal Neurons Associated with Theta but not Ripple Oscillations During Novel Exploration") is still unsupported.

One could write the same title while voltage imaging one mouse and recording LFP from another mouse.

To properly convey the results, the title should be modified to read "Synchronous Ensembles of Hippocampal CA1 Pyramidal Neurons Associated with Contralateral Theta but not with Contralateral Ripple Oscillations During Novel Exploration"

Without making this change, the title - and therefore the entire work - is misleading at best.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

For many years, there has been extensive electrophysiological research investigating the relationship between local field potential patterns and individual cell spike patterns in the hippocampus. In this study, using state-ofthe-art imaging techniques, they examined spike synchrony of hippocampal cells during locomotion and immobility states. In contrast to conventional understanding of the hippocampus, the authors demonstrated that hippocampal place cells exhibit prominent synchronous spikes locked to theta oscillations.

Strengths:

The voltage imaging used in this study is a highly novel method that allows recording not only suprathreshold-level spikes but also subthreshold-level activity. With its high frame rate, it offers time resolution comparable to electrophysiological recordings.

We thank the reviewer for a thorough review of our manuscript and for recognizing the strength of our study.

Reviewer #2 (Public review):

Summary:

This study employed voltage imaging in the CA1 region of the mouse hippocampus during the exploration of a novel environment. The authors report synchronous activity, involving almost half of the imaged neurons, occurred during periods of immobility. These events did not correlate with SWRs, but instead, occurred during theta oscillations and were phased locked to the trough of theta. Moreover, pairs of neurons with high synchronization tended to display non-overlapping place fields, leading the authors to suggest these events may play a role in binding a distributed representation of the context.

Strengths:

Technically this is an impressive study, using an emerging approach that allow single-cell resolution voltage imaging in animals, that while head-fixed, can move through a real environment. The paper is written clearly and suggests novel observations about population-level activity in CA1.

We thank the reviewer for a thorough review of our manuscript and for recognizing the strength of our study.

Weaknesses:

The evidence provided is weak, with the authors making surprising population-level claims based on a very sparse data set (5 data sets, each with less than 20 neurons simultaneously recorded) acquired with exciting, but less tested technology. Further, while the authors link these observations to the novelty of the context, both in the title and text, they do not include data from subsequent visits to support this. Detailed comments are below:

(1) My first question for the authors, which is not addressed in the discussion, is why these events have not been observed in the countless extracellular recording experiments conducted in rodent CA1 during exploration of novel environments. Those data sets often have 10x the neurons simultaneously recording compared to these present data, thus the highly synchronous firing should be very hard to miss. Ideally, the authors could confirm their claims via the analysis of publicly available electrophysiology data sets. Further, the claim of high extra-SWR synchrony is complicated by the observation that their recorded neurons fail to spike during the limited number of SWRs recorded during behavior- again, not agreeing with much of the previous electrophysiological recordings.

(2) The authors posit that these events are linked to the novelty of the context, both in the text, as well as in the title and abstract. However they do not include any imaging data from subsequent days to demonstrate the failure to see this synchrony in a familiar environment. If these data are available it would strengthen the proposed link to novelty is they were included.

(3) In the discussion the authors begin by speculating the theta present during these synchronous events may be slower type II or attentional theta. This can be supported by demonstrating a frequency shift in the theta recording during these events/immobility versus the theta recording during movement. (4) The authors mention in the discussion that they image deep layer PCs in CA1, however this is not mentioned in the text or methods. They should include data, such as imaging of a slice of a brain post-recording with immunohistochemistry for a layer specific gene to support this.

Comments on revisions:

I have no further major requests and thank the authors for the additional data and analyses.

We thank the reviewer for recognizing our efforts in revising the manuscript.

Reviewer #3 (Public review):

Summary:

In the present manuscript, the authors use a few minutes of voltage imaging of CA1 pyramidal cells in head-fixed mice running on a track while local field potentials (LFPs) are recorded. The authors suggest that synchronous ensembles of neurons are differentially associated with different types of LFP patterns, theta and ripples. The experiments are flawed in that the LFP is not "local" but rather collected the other side of the brain.

Strengths:

The authors use a cutting-edge technique.

We thank the reviewer for a thoughtful review of our manuscript and for pointing out the technical strength of our study.

Weaknesses:

The two main messages of the manuscript indicated in the title are not supported by the data. The title gives two messages that relate to CA1 pyramidal neurons in behaving head-fixed mice: (1) synchronous ensembles are associated with theta (2) synchronous ensembles are not associated with ripples. The main problem with the work is that the theta and ripple signals were recorded using electrophysiology from the opposite hemisphere to the one in which the spiking was monitored. However, both rhythms exhibit profound differences as a function of location.

Theta phase changes with the precise location along the proximo-distal and dorso-ventral axes, and importantly, even reverses with depth. Because the LFP was recorded using a single-contact tungsten electrode, there is no way to know whether the electrode was exactly in the CA1 pyramidal cell layer, or in the CA1 oriens, CA1 radiatum, or perhaps even CA3 - which exhibits ripples and theta which are weakly correlated and in anti-phase with the CA1 rhythms, respectively. Thus, there is no way to know whether the theta phase used in the analysis is the phase of the local CA1 theta.

Although the occurrence of CA1 ripples is often correlated across parts of the hippocampus, ripples are inherently a locally-generated rhythm. Independent ripples occur within a fraction of a millimeter within the same hemisphere. Ripples are also very sensitive to the precise depth - 100 micrometers up or down, and only a positive deflection/sharp wave is evident. Thus, even if the LFP was recorded from the center of the CA1 pyramidal layer in the contralateral hemisphere, it would not suffice for the claim made in the title.

We thank the reviewer for pointing out the issue regarding the claim made in the title. We have revised the manuscript to clarify that the theta and ripple oscillations referenced in the title refer to specific frequency bands of intracellular and contralaterally recorded field potentials rather than field potentials recorded at the same site as the neuronal activity.

Abstract (line19):

“… Notably, these synchronous ensembles were not associated with contralateral ripple oscillations but were instead phase-locked to theta waves recorded in the contralateral CA1 region. Moreover, the subthreshold membrane potentials of neurons exhibited coherent intracellular theta oscillations with a depolarizing peak at the moment of synchrony.”

Introduction (line68):

“… Surprisingly, these synchronous ensembles occurred outside of contralateral ripples and were phase-locked to intracellular theta oscillations as well as extracellular theta oscillations recorded from the contralateral CA1 region.”

To address concerns about electrode placement, we have now included posthoc histological verification of electrode locations, confirming that they were positioned in the contralateral CA1 pyramidal layer (Author response image 1). 

Author response image 1.

Post-hoc histological section showing the location of a DiI-coated electrode in the contralateral CA1 pyramidal layer. Scale bar: 300 μm.

While we appreciate that theta and ripple oscillations exhibit regional variations in phase and amplitude, previous studies have demonstrated a strong co-occurrence and synchrony of these oscillations between both hippocampi1-3. Given that our primary objective was to examine how neuronal ensembles relate to large-scale hippocampal oscillation states rather than local microcircuit-level fluctuations, we recorded theta and ripple oscillations from the contralateral CA1 region.

However, we acknowledge that contralateral recordings do not capture all ipsilateral-specific dynamics. Theta phases vary with depth and precise location, and local ripple events may be independently generated across small spatial scales. To reflect this, we have now explicitly acknowledged these considerations in the discussion. 

Discussion (line527):

While contralateral LFP recordings reliably capture large-scale hippocampal theta and ripple oscillations, they may not fully account for ipsilateral-specific dynamics, such as variations in theta phase alignment or locally generated ripple events. Although contralateral recordings serve as a well-established proxy for large-scale hippocampal oscillatory states, incorporating simultaneous ipsilateral field potential recordings in future studies could refine our understanding of local-global network interactions. Despite these considerations, our findings provide robust evidence for the existence of synchronous neuronal ensembles and their role in coordinating newly formed place cells. These results advance our understanding of how synchronous neuronal ensembles contribute to spatial memory acquisition and hippocampal network coordination.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have provided sufficient experimental and analytical data addressing my comments, particularly regarding consistency with past electrophysiological data and the exclusion of potential imaging artifacts.

We thank the reviewer for recognizing our efforts in revising the manuscript.

Minor comment: In Figure 2C and Figure 5-figure supplement 1, 'paired Student's t-test' is not entirely appropriate. More precisely, either 'paired t-test' or 'Student's t-test' would better indicate the correct statistical method. Please verify whether these data comparisons are within-group or between-group.

Thank you for the comment. We have revised the manuscript as suggested.

Reviewer #2 (Recommendations for the authors):

I have no further major requests and thank the authors for the additional data and analyses.

We thank the reviewer for recognizing our efforts in revising the manuscript.

Minor points- line 169- typo, correct grant to grand

Thank you for pointing it out. The typo has been corrected.

(1) Buzsaki, G. et al. Hippocampal network patterns of activity in the mouse. Neuroscience 116, 201-211 (2003). https://doi.org:10.1016/s03064522(02)00669-3

(2) Szabo, G. G. et al. Ripple-selective GABAergic projection cells in the hippocampus. Neuron 110, 1959-1977 e1959 (2022). https://doi.org:10.1016/j.neuron.2022.04.002

(3) Huang, Y. C. et al. Dynamic assemblies of parvalbumin interneurons in brain oscillations. Neuron 112, 2600-2613 e2605 (2024). https://doi.org:10.1016/j.neuron.2024.05.015

eLife Assessment

The authors present a biologically plausible framework for action selection and learning in the striatum that is a fundamental advance in our understanding of possible neural implementations of reinforcement learning in the basal ganglia. They provide compelling evidence that their model can reconcile realistic neural plasticity rules with the distinct functional roles of the direct and indirect spiny projection neurons of the striatum, recapitulating experimental findings regarding the activity profiles of these distinct neural populations and explaining a key aspect of striatal function.

Reviewer #1 (Public review):

Summary:

The authors propose a new model of biologically realistic reinforcement learning in the direct and indirect pathway spiny projection neurons in the striatum. These pathways are widely considered to provide a neural substrate for reinforcement learning in the brain. However, we do not yet have a full understanding of mechanistic learning rules that would allow successful reinforcement learning like computations in these circuits. The authors outline some key limitations of current models and propose an interesting solution by leveraging learning with efferent inputs of selected actions. They show that the model simulations are able to recapitulate experimental findings about the activity profile in these populations in mice during spontaneous behavior. They also show how their model is able to implement off-policy reinforcement learning.

Strengths:

The manuscript has been very clearly written and the results have been presented in a readily digestible manner. The limitations of existing models, that motive the presented work, have been clearly presented and the proposed solution seems very interesting. The novel contribution in the proposed model is the idea that different patterns of activity drive current action selection and learning. Not only does this allow the model is able to implement reinforcement learning computations well, this suggestion may have interesting implications regarding why some processes selectively affect ongoing behavior and others affect learning. The model is able to recapitulate some interesting experimental findings about various activity characteristics of dSPN and iSPN pathway neuronal populations in spontaneously behaving mice. The authors also show that their proposed model can implement off-policy reinforcement learning algorithms with biologically realistic learning rules. This is interesting since off-policy learning provides some unique computational benefits and it is very likely that learning in neural circuits may, at least to some extent, implement such computations.

Weaknesses:

A weakness in this work is that it isn't clear how a key component in the model - an efferent copy of selected actions - would be accessible to these striatal populations. The authors propose several plausible candidates, but future work may clarify the feasibility of this proposal.

Reviewer #2 (Public review):

Summary:

The basal ganglia is often understood within a reinforcement learning (RL) framework, where dopamine neurons convey a reward prediction error which modulates cortico-striatal connections onto spiny projection neurons (SPNS) in the striatum. However, current models of plasticity rules are inconsistent with learning in a reinforcement learning framework.

This paper proposes a new model that describes how distinct learning rules in direct and indirect pathway striatal neurons allows them to implement reinforcement learning models. It proposes that two distinct component of striatal activity affect action selection and learning. They show that the proposed implementation allows learning in simple tasks and is consistent with experimental data from calcium imaging data in direct and indirect SPNs in freely moving mouse.

Strengths:

Despite the success of reward prediction errors at characterizing the responses of dopamine neurons as the temporal difference error within an RL framework, the implementation of RL algorithms in the rest of the basal ganglia has been unclear. A key missing aspect has been the lack of a RL implementation that is consistent with the distinction of direct- and indirect SPNs. This paper proposes a new model that is able to learn successfully in simple RL tasks and explains recent experimental results.

The author shows that their proposed model, unlike previous implementations, this model can perform well in RL tasks. The new model allows them to make experimental predictions. They test some of these predictions and show that the dynamics of dSPNs and iSPNs correspond to model predictions.

More generally, this new model can be used to understand striatal dynamics across direct and indirect SPNs in future experiments.

Weaknesses:

The authors could characterize better the reliability of their experimental predictions and the description of the parameters of some of the simulations

The authors propose some ideas about how the specificity of the striatal efferent inputs but should highlight better that this is a key feature of the model whose anatomical implementation has yet to be resolved.

Comments on revisions:

I thank the authors for their response to public and private reviews and for the clarifications and changes to the manuscript which have strengthened it. I understand the inability to implement some of the proposed additional simulation due to authors having left academia and the request for a version of record.

Reviewer #3 (Public review):

Summary:

This paper points out an inconsistency of the roles of the striatal spiny neurons projecting to the indirect pathway (iSPN) and the synaptic plasticity rule of those neurons expressing dopamine D2 receptors, and proposes a novel, intriguing mechanisms that iSPNs are activated by the efference copy of the chosen action that they are supposed to inhibit.

The proposed model was supported by simulations and analysis of the neural recording data during spontaneous behaviors.

Strengths:

Previous models suggested that the striatal neurons learn action values functions, but how the information about the chosen action is fed back to the striatum for learning was not clear. The author pointed out that this is a fundamental problem for iSPNs that are supposed to inhibit specific actions and its synaptic inputs are potentiated with dopamine dips.

The authors proposes a novel hypothesis that iSPNs are activated by efference copy of the selected action which they are supposed to inhibit during action selection. Even though intriguing and seemingly unnatural, the authors demonstrated that the model based on the hypothesis can circumvent the problem of iSPNs learning to disinhibit the actions associated with negative reward errors. They further showed by analyzing the cell-type specific neural recording data by Markowitz et al. (2018) that iSPN activities tend to be anti-correlated before and after action selection.

Weaknesses:

(1) It is not correct to call the action value learning using the externally-selected action as "off-policy." Both off-policy algorithm Q-learning and on-policy algorithm SARSA update the action value of the chosen action, which can be different from the greedy action implicated by the present action values. In standard reinforce learning terminology, on-policy or off-policy is regarding the actions in the subsequent state, whether to use the next action value of (to be) chosen action or that of greedy choice as in equation (7).<br /> It is worth noting that this paper suggested that dopamine neurons encode on-policy TD errors: Morris G, Nevet A, Arkadir D, Vaadia E, Bergman H (2006). Midbrain dopamine neurons encode decisions for future action. Nat Neurosci, 9, 1057-63. https://doi.org/10.1038/nn1743

(2) It is also confusing to contract TD learning and Q-learning, as the latter is considered as on type of TD learning. In the TD error signal by state value function (6) is dependent on the chosen action a_{t-1} implicitly in r_t and s_t based on the reward and state transition function.

(3) It is not clear why interferences of the activities for action selection and learning can be avoided, especially when actions are taken with short intervals or even temporal overlaps. How can the efference copy activation for the previous action be dissociated with the sensory cued activation for the next action selection?

(4) Although it may be difficult to single out the neural pathway that carries the efference copy signal to the striatum, it is desired to consider their requirements and difference possibilities. A major issue is that the time delay from actions to reward feedback can be highly variable.

An interesting candidate is the long-latency neurons in the CM thalamus projecting to striatal cholinergic interneurons, which are activated following low-reward actions:<br /> Minamimoto T, Hori Y, Kimura M (2005). Complementary process to response bias in the centromedian nucleus of the thalamus. Science, 308, 1798-801. https://doi.org/10.1126/science.1109154

(5) In the paragraph before Eq. (3), Eq (1) should be Eq. (2) for the iSPN.

Here are comments back to the authors' replies with the revised version:

(1) I do not agree on the use of inaccurate technical terms. On-policy does not require that the policy is greedy with respect to the actions values, as authors seem to assume here.

In fact, the policy (10) is just a standard soft-max action selection based on the action values by the difference of dSPN and iSPN outputs.

Furthermore, in the immediate reward setting tested in this paper, action values are independent of the policy, so there is no distinction between on-policy vs. off-policy. This is also apparent from the "TD" errors in (19) and (21), where there is no TD.

(2) To really compare the different forms of TD, multi-step RL tasks should be used.

(3) This fundamental limitation should be explicitly documented in the manuscript. This is not just the same as any RL algorithms. Having two action representations within each action step make temporal credit assignment more difficult.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

Summary:

The authors propose a new model of biologically realistic reinforcement learning in the direct and indirect pathway spiny projection neurons in the striatum. These pathways are widely considered to provide a neural substrate for reinforcement learning in the brain. However, we do not yet have a full understanding of mechanistic learning rules that would allow successful reinforcement learning like computations in these circuits. The authors outline some key limitations of current models and propose an interesting solution by leveraging learning with efferent inputs of selected actions. They show that the model simulations are able to recapitulate experimental findings about the activity profile in these populations of mice during spontaneous behavior. They also show how their model is able to implement off-policy reinforcement learning.

Strengths:

The manuscript has been very clearly written and the results have been presented in a readily digestible manner. The limitations of existing models, that motivate the presented work, have been clearly presented and the proposed solution seems very interesting. The novel contribution of the proposed model is the idea that different patterns of activity drive current action selection and learning. Not only does this allow the model is able to implement reinforcement learning computations well, but this suggestion may have interesting implications regarding why some processes selectively affect ongoing behavior and others affect learning. The model is able to recapitulate some interesting experimental findings about various activity characteristics of dSPN and iSPN pathway neuronal populations in spontaneously behaving mice. The authors also show that their proposed model can implement off-policy reinforcement learning algorithms with biologically realistic learning rules. This is interesting since off-policy learning provides some unique computational benefits and it is very likely that learning in neural circuits may, at least to some extent, implement such computations.

We thank the reviewer for the positive comments.

Weaknesses:

A weakness in this work is that it isn’t clear how a key component in the model - an efferent copy of selected actions - would be accessible to these striatal populations. The authors propose several plausible candidates, but future work may clarify the feasibility of this proposal.

We agree that the biological substrate of the efference copy remains a key open question. We discuss potential pathways in the Discussion section of our manuscript and hope that future experimental studies clarify the question.

Reviewer #2:

Summary:

The basal ganglia is often understood within a reinforcement learning (RL) framework, where dopamine neurons convey a reward prediction error that modulates cortico-striatal connections onto spiny projection neurons (SPNS) in the striatum. However, current models of plasticity rules are inconsistent with learning in a reinforcement learning framework.

This paper proposes a new model that describes how distinct learning rules in direct and indirect pathway striatal neurons allow them to implement reinforcement learning models. It proposes that two distinct components of striatal activity affect action selection and learning. They show that the proposed implementation allows learning in simple tasks and is consistent with experimental data from calcium imaging data in direct and indirect SPNs in freely moving mice.

Strengths:

Despite the success of reward prediction errors at characterizing the responses of dopamine neurons as the temporal difference error within an RL framework, the implementation of RL algorithms in the rest of the basal ganglia has been unclear. A key missing aspect has been the lack of a RL implementation that is consistent with the distinction of direct- and indirect SPNs. This paper proposes a new model that is able to learn successfully in simple RL tasks and explains recent experimental results.

The author shows that their proposed model, unlike previous implementations, this model can perform well in RL tasks. The new model allows them to make experimental predictions. They test some of these predictions and show that the dynamics of dSPNs and iSPNs correspond to model predictions.

More generally, this new model can be used to understand striatal dynamics across direct and indirect SPNs in future experiments.

We thank the reviewer for the positive comments.

Weaknesses:

The authors could characterize better the reliability of their experimental predictions and the description of the parameters of some of the simulations.

In addition to the descriptions in the Methods, we have provided code implementing the key features of our simulations, which should contribute to reproducibility of our results.

The authors propose some ideas about how the specificity of the striatal efferent inputs but should highlight better that this is a key feature of the model whose anatomical implementation has yet to be resolved.

We have clarified in the Discussion section “Biological substrates of striatal efferent inputs” that these represent assumptions or predictions that have not yet been demonstrated experimentally.

Reviewer #3:

Summary:

This paper points out an inconsistency of the roles of the striatal spiny neurons projecting to the indirect pathway (iSPN) and the synaptic plasticity rule of those neurons expressing dopamine D2 receptors and proposes a novel, intriguing mechanisms that iSPNs are activated by the efference copy of the chosen action that they are supposed to inhibit.

The proposed model was supported by simulations and analysis of the neural recording data during spontaneous behaviors.

Strengths:

Previous models suggested that the striatal neurons learn action-value functions, but how the information about the chosen action is fed back to the striatum for learning was not clear. The author pointed out that this is a fundamental problem for iSPNs that are supposed to inhibit specific actions and its synaptic inputs are potentiated with dopamine dips.

The authors propose a novel hypothesis that iSPNs are activated by efference copy of the selected action which they are supposed to inhibit during action selection. Even though intriguing and seemingly unnatural, the authors demonstrated that the model based on the hypothesis can circumvent the problem of iSPNs learning to disinhibit the actions associated with negative reward errors. They further showed by analyzing the cell-type specific neural recording data by Markowitz et al. (2018) that iSPN activities tend to be anti-correlated before and after action selection.

We thank the reviewer for the positive comments.

Weaknesses:

It is not correct to call the action value learning using the externally-selected action as “offpolicy.” Both off-policy algorithm Q-learning and on-policy algorithm SARSA update the action value of the chosen action, which can be different from the greedy action implicated by the present action values. In standard reinforcement learning terminology, on-policy or off-policy is regarding the actions in the subsequent state, whether to use the next action value of (to be) chosen action or that of greedy choice as in equation (7).

It is worth noting that this paper suggested that dopamine neurons encode on-policy TD errors: Morris G, Nevet A, Arkadir D, Vaadia E, Bergman H (2006). Midbrain dopamine neurons encode decisions for future action. Nat Neurosci, 9, 1057-63. https://doi.org/10.1038/nn1743.

We regret that we do not completely follow the reviewer’s comment. We use “off-policy” to refer to the fact that, considered in isolation, the basal ganglia reinforcement learning system that we model learns a target policy that may be distinct from the behavioral policy of the organism as a whole.

It is also confusing to contract TD learning and Q-learning, as the latter is considered as one type of TD learning. In the TD error signal by state value function (6) is dependent on the chosen action at−1 implicitly in rt and st based on the reward and state transition function.

We agree that this was confusing. We have therefore changed the places in our paper where we intended to refer to “TD learning of a value function V (s)” to specifically mention V (s), rather than just “TD learning.”

It is not clear why interferences of the activities for action selection and learning can be avoided, especially when actions are taken with short intervals or even temporal overlaps. How can the efference copy activation for the previous action be dissociated with the sensory cued activation for the next action selection?

The non-interference arises from the orthogonality of the difference (action selection) and sum (efference copy) modes, as described in Figure 3. However, we agree with the reviewer that the problem of temporal credit assignment, when many actions are taken before reward feedback is obtained, is present in our model, as in any standard RL model.

Although it may be difficult to single out the neural pathway that carries the efference copy signal to the striatum, it is desired to consider their requirements and difference possibilities. A major issue is that the time delay from actions to reward feedback can be highly variable.

An interesting candidate is the long-latency neurons in the CM thalamus projecting to striatal cholinergic interneurons, which are activated following low-reward actions: Minamimoto T, Hori Y, Kimura M (2005). Complementary process to response bias in the centromedian nucleus of the thalamus. Science, 308, 1798-801. https://doi.org/10.1126/science.1109154.

We are grateful for the interesting suggestion and reference, which we have added to the manuscript. However, we note that the issue of delayed reward feedback may also be partially addressed by using a sufficiently long eligibility trace.

In the paragraph before Eq. (3), Eq. (1) should be Eq. (2) for the iSPN.

Corrected.

eLife assessment

Using an elegant and thorough experimental design, Thomazeau et al show that, in the developing mouse visual cortex, presynaptic NMDA receptors at layer 5 neocortical synapses mediate spike-timing dependent LTD via JNK2, non-ionotropic signaling. These fundamental findings shed light on how NMDA receptors can tune synaptic function without acting as coincidence detectors. The experiments are supported by compelling evidence, gathered through optogenetics and quadruple patch clamp recordings from cortical slices.

Reviewer #1 (Public review):

Summary:

The results offer compelling evidence that L5-L5 tLTD depends on presynaptic NMDARs, a concept that has previously been somewhat controversial.

It documents the novel finding that presynaptic NMDARs facilitate tLTD through their metabotropic signaling mechanism.

Strengths:

The experimental design is clever and clean.

The approach of comparing the results in cell pairs where NMDA is deleted either presynaptically or postsynaptically is technically insightful and yields decisive data.

The MK801 experiments are also compelling.

Weaknesses:

No major weaknesses were noted by this reviewer.

Reviewer #2 (Public review):

Summary:

The study characterized the dependence of spike-timing-dependent long-term depression (tLTD) on presynaptic NMDA receptors and the intracellular cascade after NMDAR activation possibly involved in the observed decrease in glutamate probability release at L5-L5 synapses of the visual cortex in mouse brain slices.

Strengths:

The genetic and electrophysiological experiments are thorough. The experiments are well-reported and mainly support the conclusions. This study confirms and extends current knowledge by elucidating additional plasticity mechanisms at cortical synapses, complementing existing literature.

Weaknesses:

While one of the main conclusions (preNMDARs mediating presynaptic LTD) is resolved in a very convincing genetic approach, the second main conclusion of the manuscript (non-ionotropic preNMDARs) relies on the use of a high concentration of extracellular blockers (MK801, 2 mM; 7-clorokinurenic acid: 100 microM), but no controls for the specific actions of these compounds are shown. In addition, no direct testing for ions passing through preNMDAR has been performed.

It is not known if the results can be extrapolated to adult brain as the data were obtained from 11-18 days-old mice slices, a period during which synapses are still maturing and the cortex is highly plastic.

Reviewer #3 (Public review):

Summary:

In this manuscript, "Neocortical Layer-5 tLTD Relies on Non-Ionotropic Presynaptic NMDA Receptor Signaling", Thomazeau et al. seek to determine the role of presynaptic NMDA receptors and the mechanism by which they mediate expression of frequency-independent timing-dependent long-term depression (tLTD) between layer-5 (L5) pyramidal cells (PCs) in the developing mouse visual cortex. By utilizing sophisticated methods, including sparse Cre-dependent deletion of GluN1 subunit via neonatal iCre-encoding viral injection, in vitro quadruple patch clamp recordings, and pharmacological interventions, the authors elegantly show that L5 PC->PC tLTD is (1) dependent on presynaptic NMDA receptors, (2) mediated by non-ionotropic NMDA receptor signaling, and (3) is reliant on JNK2/Syntaxin-1a (STX1a) interaction (but not RIM1αβ) in the presynaptic neuron. The study elegantly and pointedly addresses a long-standing conundrum regarding the lack of frequency dependence of tLTD.

Strengths:

The authors did a commendable job presenting a very polished piece of work with high-quality data that this Reviewer feels enthusiastic about. The manuscript has several notable strengths. Firstly, the methodological approach used in the study is highly sophisticated and technically challenging and successfully produced high-quality data that were easily accessible to a broader audience. Secondly, the pharmacological interventions used in the study targeted specific players and their mechanistic roles, unveiling the mechanism in question step-by-step. Lastly, the manuscript is written in a well-organized manner that is easy to follow. Overall, the study provides a series of compelling evidence that leads to a clear illustration of mechanistic understanding.

I have a couple of small items below, which the authors can address in a minor revision if they so wish.

Minor comments:

(1) For the broad readership, a brief description of JNK2-mediated signaling cascade underlying tLTD, including its intersection with CB1 receptor signaling may be desired.

(2) The authors used juvenile mice, P11 to P18 of age. It is a typical age range used for plasticity experiments, but it is also true that this age range spans before and after eye-opening in mice (~P13) and is a few days before the onset of the classical critical period for ocular dominance plasticity in the visual cortex. Given the mechanistic novelty reported in the study, can authors comment on whether this signaling pathway may be age-dependent?

eLife Assessment

This valuable work provides a robust yet simple protocol to isolate small extracellular vesicles from small volumes of plasma. The evidence supporting the conclusions is convincing, although a more thorough statistical comparison of the different techniques and technique combinations explored in the study would have been appreciated. The work will be of broad interest to cell biologists and biochemists.

eLife Assessment

This work provides a simple, rapid and valuable protocol for the isolation of small extracellular vesicles from small volumes of plasma, using two well-known methodologies, in tandem: size exclusion chromatography (SEC) and density gradient ultracentrifugation (DGUC). The authors exhaustively test these methodologies separately and in combination, showing superior results for the SEC-DGUC in terms of purity and yield. The results obtained in this work are convincing, using multiple state-of-art methodologies for the characterization of the isolates that support their conclusions.

eLife Assessment

This important study advances our understanding of genome annotations for chiton genomes. It provides a solid estimation of syntentic relationships for the chromosomes of the four new genomes plus an analysis linking these to other available chiton genomes, and an update for how these relate to molluscan genomes.

eLife Assessment

This fundamental study explores how genotypic changes relate to phenotypic stasis or variation within chitons, a molluscan group. Chitons are significant because their ancient body plan has remained largely unchanged for millions of years, yet the paper reveals rapid and large-scale genomic changes. This convincing study is a splendid advance in approximately doubling the number of sequenced chiton genomes, providing what appears to be among the best genome annotations for chiton genomes available to date. The study's key focus is on the genomic rearrangements across five reference-quality genomes of chitons and their implications for understanding evolutionary mechanisms, particularly in comparison to other molluscan clades.

eLife Assessment

This manuscript offers important insights into how polyphosphate (polyP) influences protein phase separation differently from DNA. The authors present compelling evidence that polyP distinguishes between protein conformational states, leading to diverse condensate behaviors. However, differences in charge density between polyP and DNA complicate direct comparisons, and the extent to which polyP-driven phase transitions reveal initial protein states remains unclear. Addressing these concerns would strengthen the manuscript's impact for researchers interested in biomolecular condensates, protein dynamics, and stress response mechanisms.

Reviewer #1 (Public review):

Summary:

In the article titled "Polyphosphate discriminates protein conformational ensembles more efficiently than DNA promoting diverse assembly and maturation behaviors," Goyal and colleagues investigate the role of negatively charged biopolymers, i.e., polyphosphate (polyP) and DNA, play in phase separation of cytidine repressor (CytR) and fructose repressor (FruR). The authors find that both negative polymers drive the formation of metastable protein/polymer condensates. However, polyP-driven condensates form more gel- or solid-like structures over time while DNA-driven condensates tend to dissipate over time. The authors link this disparate condensate behavior to polyP-induced structures within the enzymes. Specifically, they observe the formation of polyproline II-like structures within two tested enzyme variants in the presence of polyP. Together their results provide a unique insight into the physical and structural mechanism by which two unique negatively charged polymers can induce distinct phase transitions with the same protein. This study will be a welcomed addition to the condensate field and provide new molecular insights into how binding partner-induced structural changes within a given protein can affect the mesoscale behavior of condensates. The concerns outlined below are meant to strengthen the manuscript.

Strengths:

Throughout the article, the authors used the correct techniques to probe physical changes within proteins that can be directly linked to phase transition behaviors. Their rigorous experiments create a clear picture of what occurs at the molecular level with CytR and FruR are exposed to either DNA or polyP, which are unique, highly negatively charged biopolymers found within bacteria. This work provides a new view of mechanisms by which bacteria can regulate the cytoplasmic organization upon the induction of stress. Furthermore, this is likely applicable to mammalian and plant cells and likely to numerous proteins that undergo condensation with nucleic acids and other charged biopolymers.

Weaknesses:

The biggest weakness of this study is that compares the phase behavior of enzymes driven by negatively charged polymers that have intrinsic differences in net charge and charge density. Because these properties are extremely important for controlling phase separation, any differences may result in the observed phase transitions driven by DNA and polyP. The authors should perform an additional experiment to control for these differences as best they can. The results from these experiments will provide additional insight into the importance of charge-based properties for controlling phase transitions.

Reviewer #2 (Public review):

Summary:

In this study, Goyal et al demonstrate that the assembly of proteins with polyphosphate into either condensates or aggregates can reveal information on the initial protein ensemble. They show that, unlike DNA, polyphosphate is able to effectively discriminate against initial protein ensembles with different conformational heterogeneity, structure, and compactness. The authors further show that the protein native ensemble is vital on whether polyphosphate induces phase separation or aggregation, whereas DNA induces a similar outcome regardless of the initial protein ensemble. This work provides a way to improve our mechanistic understanding of how conformational transitions of proteins may regulate or drive LLPS condensate and aggregate assemblies within biological systems.

Strengths:

This is a thoroughly conducted study that provides an alternative route for inducing phase separation that is more informative on the initial protein ensemble involved. This is particularly useful and a complementary means to investigate the role played by protein dynamics and plasticity in phase transitions. The authors use an appropriate set of techniques to investigate unique phase transitions within proteins induced by polyphosphates. An alternative protein system is used to corroborate their findings that the unique assemblies induced by polyphosphates when compared to DNA are not restricted to a single system. The work here is well-documented, easy to interpret, and of relevance for the condensate community.

Weaknesses:

The major weakness of this manuscript is that it is unclear if the information on the initial protein conformational ensemble can be determined solely from the assembly and maturation behavior and the discrimination abilities of polyphosphates. In both systems studied (CytR and FruR), polyphosphate discriminates and results in unique assemblies and maturation behaviors based on the initial protein ensemble. However, it seems the assembly and maturation behavior are not a direct result of the degree of conformational dynamics and plasticity in the initial protein. In the case of CytR, the fully-folded system forms condensates that resolubilize, while the highly disordered state immediately aggregates. Whereas, in the case of FruR, the folded state induces spontaneous aggregation, and the more dynamic, molten globular, system results in short-lived condensates. These results seem to suggest the polyphosphates' ability to discriminate between the initial protein ensemble may not be able to reveal what that initial protein ensemble is unless it is already known.

Author response:

eLife Assessment

This manuscript offers important insights into how polyphosphate (polyP) influences protein phase separation differently from DNA. The authors present compelling evidence that polyP distinguishes between protein conformational states, leading to diverse condensate behaviors. However, differences in charge density between polyP and DNA complicate direct comparisons, and the extent to which polyP-driven phase transitions reveal initial protein states remains unclear. Addressing these concerns would strengthen the manuscript's impact for researchers interested in biomolecular condensates, protein dynamics, and stress response mechanisms.

We thank the editorial team for the favorable assessment. We, however, contend the specific point on the difference in charge density. We have already performed experiments wherein a higher concentration of DNA is used to match the overall ‘concentration of charges’ as in the experiments with polyP (see Figure S6), and we do not identify or observe any differences in the maturation behavior with DNA, i.e. we see only dissolution at both higher and lower concentrations of DNA. Charge density (i.e. the number of charges per unit volume of the polymer), on the other hand, is an intrinsic feature of the polymer which is naturally different between DNA and polyP. In fact, the primary result of our work is our observation that polyP can discern the starting ensembles more efficiently, likely through actively engaging and interacting with the ensemble while DNA appears to be a passive player. 

Reviewer #1 (Public review):

Summary:

In the article titled "Polyphosphate discriminates protein conformational ensembles more efficiently than DNA promoting diverse assembly and maturation behaviors," Goyal and colleagues investigate the role of negatively charged biopolymers, i.e., polyphosphate (polyP) and DNA, play in phase separation of cytidine repressor (CytR) and fructose repressor (FruR). The authors find that both negative polymers drive the formation of metastable protein/polymer condensates. However, polyPdriven condensates form more gel- or solid-like structures over time while DNA-driven condensates tend to dissipate over time. The authors link this disparate condensate behavior to polyP-induced structures within the enzymes. Specifically, they observe the formation of polyproline II-like structures within two tested enzyme variants in the presence of polyP. Together their results provide a unique insight into the physical and structural mechanism by which two unique negatively charged polymers can induce distinct phase transitions with the same protein. This study will be a welcomed addition to the condensate field and provide new molecular insights into how binding partner-induced structural changes within a given protein can affect the mesoscale behavior of condensates. The concerns outlined below are meant to strengthen the manuscript.

Strengths:

Throughout the article, the authors used the correct techniques to probe physical changes within proteins that can be directly linked to phase transition behaviors. Their rigorous experiments create a clear picture of what occurs at the molecular level with CytR and FruR are exposed to either DNA or polyP, which are unique, highly negatively charged biopolymers found within bacteria. This work provides a new view of mechanisms by which bacteria can regulate the cytoplasmic organization upon the induction of stress. Furthermore, this is likely applicable to mammalian and plant cells and likely to numerous proteins that undergo condensation with nucleic acids and other charged biopolymers.

Weaknesses:

The biggest weakness of this study is that compares the phase behavior of enzymes driven by negatively charged polymers that have intrinsic differences in net charge and charge density. Because these properties are extremely important for controlling phase separation, any differences may result in the observed phase transitions driven by DNA and polyP. The authors should perform an additional experiment to control for these differences as best they can. The results from these experiments will provide additional insight into the importance of charge-based properties for controlling phase transitions.

We thank the reviewer for providing a positive review of our work. On the comment related to the final paragraph, we note that we have already conducted an experiment with a higher DNA concentration (11.24 µM) to explore if the concentration of charges plays any significant role. The results of this experiment are presented in Figure S6. We observe that even at a higher DNA concentration, the condensates dissolve over time. Therefore, the difference in the maturation behavior of condensates with varying initial protein ensembles is due to the nature of polyP (likely through its enhanced flexibility). 

Reviewer #2 (Public review):

Summary:

In this study, Goyal et al demonstrate that the assembly of proteins with polyphosphate into either condensates or aggregates can reveal information on the initial protein ensemble. They show that, unlike DNA, polyphosphate is able to effectively discriminate against initial protein ensembles with different conformational heterogeneity, structure, and compactness. The authors further show that the protein native ensemble is vital on whether polyphosphate induces phase separation or aggregation, whereas DNA induces a similar outcome regardless of the initial protein ensemble. This work provides a way to improve our mechanistic understanding of how conformational transitions of proteins may regulate or drive LLPS condensate and aggregate assemblies within biological systems.

Strengths:

This is a thoroughly conducted study that provides an alternative route for inducing phase separation that is more informative on the initial protein ensemble involved. This is particularly useful and a complementary means to investigate the role played by protein dynamics and plasticity in phase transitions. The authors use an appropriate set of techniques to investigate unique phase transitions within proteins induced by polyphosphates. An alternative protein system is used to corroborate their findings that the unique assemblies induced by polyphosphates when compared to DNA are not restricted to a single system. The work here is well-documented, easy to interpret, and of relevance for the condensate community.

Weaknesses:

The major weakness of this manuscript is that it is unclear if the information on the initial protein conformational ensemble can be determined solely from the assembly and maturation behavior and the discrimination abilities of polyphosphates. In both systems studied (CytR and FruR), polyphosphate discriminates and results in unique assemblies and maturation behaviors based on the initial protein ensemble. However, it seems the assembly and maturation behavior are not a direct result of the degree of conformational dynamics and plasticity in the initial protein. In the case of CytR, the fully-folded system forms condensates that resolubilize, while the highly disordered state immediately aggregates. Whereas, in the case of FruR, the folded state induces spontaneous aggregation, and the more dynamic, molten globular, system results in short-lived condensates. These results seem to suggest the polyphosphates' ability to discriminate between the initial protein ensemble may not be able to reveal what that initial protein ensemble is unless it is already known.

We thank the reviewer for providing constructive comments on our work. On the final paragraph: we agree that the outcome does not provide information on nature of the starting ensemble. As of now, our experimental results are primarily observations on questions related to maturation outcomes when protein ensembles of varying structure, compactness and stability interact with polyP. if there are differences in the native ensemble due to mutations (which at times cannot be revealed by ensemble probes), polyP appears to discern it more efficiently than DNA.

eLife Assessment

This valuable study reveals the pro-locomotor effects of activating a deep brain region containing diverse range of neurons in both healthy and Parkinson's disease mouse models. While the findings are solid, mechanistic insights remain limited due to the small sample size. This research is relevant to motor control researchers and offers clinical perspectives.

Reviewer #1 (Public review):

Summary:

This study aimed to investigate the effects of optically stimulating the A13 region in healthy mice and a unilateral 6-OHDA mouse model of Parkinson's disease (PD). The primary objectives were to assess changes in locomotion, motor behaviors, and the neural connectome. For this, the authors examined the dopaminergic loss induced by 6-OHDA lesioning. They found a significant loss of tyrosine hydroxylase (TH+) neurons in the substantia nigra pars compacta (SNc) while the dopaminergic cells in the A13 region were largely preserved. Then, they optically stimulated the A13 region using a viral vector to deliver the channelrhodopsine (CamKII promoter). In both sham and PD model mice, optogenetic stimulation of the A13 region induced pro-locomotor effects, including increased locomotion, more locomotion bouts, longer durations of locomotion, and higher movement speeds. Additionally, PD model mice exhibited increased ipsilesional turning during A13 region photoactivation. Lastly, the authors used whole-brain imaging to explore changes in the A13 region's connectome after 6-OHDA lesions. These alterations involved a complex rewiring of neural circuits, impacting both afferent and efferent projections. In summary, this study unveiled the pro-locomotor effects of A13 region photoactivation in both healthy and PD model mice. The study also indicates the preservation of A13 dopaminergic cells and the anatomical changes in neural circuitry following PD-like lesions that represent the anatomical substrate for a parallel motor pathway.

Strengths:

These findings hold significant relevance for the field of motor control, providing valuable insights into the organization of the motor system in mammals. Additionally, they offer potential avenues for addressing motor deficits in Parkinson's disease (PD). The study fills a crucial knowledge gap, underscoring its importance, and the results bolster its clinical relevance and overall strength.

The authors adeptly set the stage for their research by framing the central questions in the introduction, and they provide thoughtful interpretations of the data in the discussion section. The results section, while straightforward, effectively supports the study's primary conclusion-the pro-locomotor effects of A13 region stimulation, both in normal motor control and in the 6-OHDA model of brain damage.

Weaknesses:

(1) Anatomical investigation. I have a major concern regarding the anatomical investigation of plastic changes in the A13 connectome (Figures 4 and 5). While the methodology employed to assess the connectome is technically advanced and powerful, the results lack mechanistic insight at the cell or circuit level into the pro-locomotor effects of A13 region stimulation in both physiological and pathological conditions. This concern is exacerbated by a textual description of results that doesn't pinpoint precise brain areas or subareas but instead references large brain portions like the cortical plate, making it challenging to discern the implications for A13 stimulation. Lastly, the study is generally well-written with a smooth and straightforward style, but the connectome section presents challenges in readability and comprehension. The presentation of results, particularly the correlation matrices and correlation strength, doesn't facilitate biological understanding. It would be beneficial to explore specific pathways responsible for driving the locomotor effects of A13 stimulation, including examining the strength of connections to well-known locomotor-associated regions like the Pedunculopontine nucleus, Cuneiformis nucleus, LPGi, and others in the diencephalon, midbrain, pons, and medulla. Additionally, identifying the primary inputs to A13 associated with motor function would enhance the study's clarity and relevance.

The study raises intriguing questions about compensatory mechanisms in Parkinson's disease a new perspective with the preservation of dopaminergic cells in A13, despite the SNc degeneration, and the plastic changes to input/output matrices. To gain inspiration for a more straightforward reanalysis and discussion of the results, I recommend the authors refer to the paper titled "Specific populations of basal ganglia output neurons target distinct brain stem areas while collateralizing throughout the diencephalon from the David Kleinfeld laboratory." This could guide the authors in investigating motor pathways across different brain regions.

(2) Description of locomotor performance. Figure 3 provides valuable data on the locomotor effects of A13 region photoactivation in both control and 6-OHDA mice. However, a more detailed analysis of the changes in locomotion during stimulation would enhance our understanding of the pro-locomotor effects, especially in the context of 6-OHDA lesions. For example, it would be informative to explore whether the probability of locomotion changes during stimulation in the control and 6-OHDA groups. Investigating reaction time, speed, total distance, and even kinematic aspects during stimulation could reveal how A13 is influencing locomotion, particularly after 6-OHDA lesions. The laboratory of Whelan has a deep knowledge of locomotion and the neural circuits driving it so these features may be instructive to infer insights on the neural circuits driving movement. On the same line, examining features like the frequency or power of stimulation related to walking patterns may help elucidate whether A13 is engaging with the Mesencephalic Locomotor Region (MLR) to drive the pro-locomotor effects. These insights would provide a more comprehensive understanding of the mechanisms underlying A13-mediated locomotor changes in both healthy and pathological conditions.

(3) Figure 2 indeed presents valuable information regarding the effects of A13 region photoactivation. To enhance the comprehensiveness of this figure and gain a deeper understanding of the neurons driving the pro-locomotor effect of stimulation, it would be beneficial to include quantifications of various cell types:

• cFos-Positive Cells/TH-Positive Cells: it can help determine the impact of A13 stimulation on dopaminergic neurons and the associated pro-locomotor effect in healthy condition and especially in the context of Parkinson's disease (PD) modeling.

• cFos-Positive Cells /TH-Negative Cells: Investigating the number of TH-negative cells activated by stimulation is also important, as it may reveal non-dopaminergic neurons that play a role in locomotor responses. Identifying the location and characteristics of these TH-negative cells can provide insights into their functional significance.<br /> Incorporating these quantifications into Figure 2 would enhance the figure's informativeness and provide a more comprehensive view of the neuronal populations involved in the locomotor effects of A13 stimulation.

(4) Referred to Figure 3. In the main text (page 5) when describing the animal with 6-OHDA the wrong panels are indicated. It is indicated in Figure 2A-E but it should be replaced with 3A-E. Please do that.

Summary of the Study after revision

The revised manuscript reflects significant efforts to improve clarity, organization, and data interpretation. The refinements in anatomical descriptions, behavioral analyses, and contextual framing have strengthened the manuscript considerably. However, the study still lacks direct causal evidence linking anatomical remodeling to behavioral improvements, and the small sample size in the anatomical analyses remains a concern. The authors have addressed many points raised in the initial review, but further acknowledgement of the exploratory nature of these findings would enhance the scientific rigor of the work.

Key Improvements in the Revision

The revised manuscript demonstrates considerable progress in clarifying data presentation, refining behavioral analyses, and improving the contextualization of anatomical findings. The restructuring of the anatomical section now provides greater precision in describing motor-related pathways, integrating terminology from the Allen Brain Atlas. The addition of new figures (Figures 4 and 5) strengthens the accessibility of these findings by illustrating key connectivity patterns more effectively. Furthermore, the correlation matrices have been adjusted to improve interpretability, ensuring that the presented data contribute meaningfully to the overall narrative of the study.

The authors have also made significant improvements in their behavioral analyses, particularly in the organization and presentation of locomotor data. Figure 3 has been revised to distinctly separate results from 6-OHDA and sham animals, providing a clearer comparison of locomotor outcomes. Additional metrics, such as reaction time, locomotion bouts, and movement speed, further enhance the granularity of the analysis, making the results more informative.

The discussion surrounding anatomical connectivity has also been strengthened. The revised manuscript now places greater emphasis on motor-related pathways and refines its analysis of A13 efferents and afferents. A newly introduced figure provides a concise summary of these connections, improving the contextualization of the anatomical data within the study's broader scope. Moreover, the authors have addressed the translational relevance of their findings by acknowledging the differences between optogenetic stimulation and deep brain stimulation (DBS). Their discussion now better situates the findings within existing literature on PD-related motor circuits, providing a more balanced perspective on the potential implications of A13 stimulation.

Remaining Concerns

Despite these substantial improvements, a number of critical concerns remain. The anatomical findings, though insightful, remain largely correlative and do not establish a causal link between structural remodeling and locomotor recovery. While the authors argue that these data will serve as a reference for future investigations, their necessity for the core conclusions of the study is not entirely clear. Additionally, while the anatomical data offer an interesting perspective on A13 connectivity, their direct relevance to the study's primary goal-demonstrating the role of A13 in locomotor recovery-remains uncertain. The authors emphasize that these data will be valuable for future research, yet their integration into the study's main narrative feels somewhat supplementary. Based on this last thought of the authors it is even more relevant another key limitation lying in the small sample size used for connectivity analyses. With only two sham and three 6-OHDA animals included, the statistical confidence in the findings is inherently limited. The absence of direct statistical comparisons between ipsilesional and contralesional projections further weakens the conclusions drawn from these anatomical studies. The authors have acknowledged that obtaining the necessary samples, acquiring the data, and analyzing them is a prolonged and resource-intensive process. While this may be a valid practical limitation, it does not justify the lack of a robust statistical approach. A more rigorous statistical framework should be employed to reinforce the findings, or alternative techniques should be considered to provide additional validation. Given these constraints, it remains unclear why the authors have not opted for standard immunohistochemistry, which could provide a complementary and more statistically accessible approach to validate the anatomical findings. Employing such an approach would not only increase the robustness of the results but also strengthen the study's impact by providing an independent confirmation of the observed structural changes.

Reviewer #2 (Public review):

Summary:

The paper by Kim et al. investigates the potential of stimulating the dopaminergic A13 region to promote locomotor restoration in a Parkinson's mouse model. Using wild-type mice, 6-OHDA injection depletes dopaminergic neurons in the substantia nigra pars compacta, without impairing those of the A13 region and the ventral tegmentum area, as previously reported in humans. Moreover, photostimulation of presumably excitatory (CAMKIIa) neurons in the vicinity of the A13 region improves bradykinesia and akinetic symptoms after 6-OHDA injection. Whole-brain imaging with retrograde and anterograde tracers reveals that the A13 region undergoes substantial changes in the distribution of its afferents and projections after 6-OHDA injection, thus suggesting a remodeling of the A13 connectome. Whether this remodelling contributes to pro-locomotor effects of the photostimulation of the A13 region remains unknown as causality was not addressed.

Strengths:

Photostimulation of presumably excitatory (CAMKIIa) neurons in the vicinity of the A13 region promotes locomotion and locomotor recovery of wild-type mice 1 month after 6-OHDA injection in the medial forebrain bundle, thus identifying a new potential target for restoring motor functions in Parkinson's disease patients. The study also provides a description of the A13 region connectome pertaining to motor behaviors and how it changes after a dopaminergic lesion. Although there is no causal link between anatomical and behavioral data, it raises interesting questions for further studies.

Weaknesses:

Although CAMKIIa is a marker of presumably excitatory neurons and can be used as an alternative marker of dopaminergic neurons, some uncertainty remains regarding the phenotype of neurons underlying recovery of akinesia and improvement of bradykinesia.

Figure 4 is improved, but the results from the correlation analyses remain difficult to interpret, as they may reflect changes in various impaired brain regions independently of the A13 region. While the analysis offers a snapshot of correlated changes within the connectome, it does not identify which specific cell or axonal populations are actually increasing or decreasing. Although functional MRI connectome analyses are well-established, anatomical data seem less suitable for this purpose. How can one interpret correlated changes in anatomical inputs or outputs between two distinct regions?

Figure 5 is also improved, but there is room for further enhancement. As currently presented, it is difficult to distinguish the differences between the sham and 6-OHDA groups. The first column could compare afferents, while the second column could compare efferents. Given the small sample size, it would be more appropriate to present individual data rather than the mean and standard deviation.

Appraisal and impact

Although the behavioral experiments are convincing, the low number of animals in the anatomical studies is insufficient to make any relevant statistical conclusions due to extremely low statistical power.

Reviewer #3 (Public review):

Kim, Lognon et al. present an important finding on pro-locomotor effects of optogenetic activation of the A13 region, which they identify as a dopamine-containing area of the medial zona incerta that undergoes profound remodeling in terms of afferent and efferent connectivity after administration of 6-OHDA to the MFB. The authors claim to address a model of PD-related gait dysfunction, a contentious problem that can be difficult to treat by dopaminergic medication or DBS in conventional targets. They make use of an impressive array of technologies to gain insight into the role of A13 remodeling in the 6-OHDA model of PD. The evidence provided is solid and the paper is well written, but there are several general issues that reduce the value of the paper in its current form, and a number of specific, more minor ones. Also some suggestions, that may improve the paper compared to its recent form, come to mind.

The most fundamental issue that needs to be addressed is the relation of the structural to the behavioral findings. It would be very interesting to see whether the structural heterogeneity in afferent/effects projections induced by 6-OHDA is related to the degree of symptom severity and motor improvement during A13 stimulation.

The authors provide extensive interrogation of large-scale changes in the organization of the A13 region afferent and efferent distributions. It remains unclear how many animals were included to produce Fig 4 and 5. Fig S5 suggests that only 3 animals were used, is that correct? Please provide details about the heterogeneity between animals. Please provide a table detailing how many animals were used for which experiment. Were the same animals used for several experiments?

While the authors provide evidence that photoactivation of the A13 is sufficient in driving locomotion in the OFT, this pro-locomotor effect seems to be independent of 6-OHDA induced pathophysiology. Only in the pole test do they find that there seems to be a difference between Sham vs 6-OHDA concerning effects of photoactivation of the A13. Because of these behavioral findings, optogenic activation of A13 may represent a gain of function rather than disease-specific rescue. This needs to be highlighted more explicitly in the title, abstract and conclusion.

The authors claim that A13 may be a possible target for DBS to treat gait dysfunction. However, the experimental evidence provided (in particular lack of disease-specific changes in the OFT) seem insufficient to draw such conclusions. It needs to be highlighted that optogenetic activation does not necessarily have the same effects as DBS (see the recent review from Neumann et al. in Brain: https://pubmed.ncbi.nlm.nih.gov/37450573/). This is important because ZI-DBS so far had very mixed clinical effects. The authors should provide plausible reasons for these discrepancies. Is cell-specificity, that only optogenetic interventions can achieve, necessary? Can new forms of cyclic burst DBS achieve similar specificity (Spix et al, Science 2021)? Please comment.

In a recent study, Jeon et al (Topographic connectivity and cellular profiling reveal detailed input pathways and functionally distinct cell types in the subthalamic nucleus, 2022, Cell Reports) provided evidence on the topographically graded organization of STN afferents and McElvain et al. (Specific populations of basal ganglia output neurons target distinct brain stem areas while collateralizing throughout the diencephalon, 2021, Neuron) have shown similar topographical resolution for SNr efferents. Can a similar topographical organization of efferents and afferents be derived for the A13/ ZI in total?

In conclusion, this is an interesting study that can be improved taking into consideration the points mentioned above.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study aimed to investigate the effects of optically stimulating the A13 region in healthy mice and a unilateral 6-OHDA mouse model of Parkinson's disease (PD). The primary objectives were to assess changes in locomotion, motor behaviors, and the neural connectome. For this, the authors examined the dopaminergic loss induced by 6-OHDA lesioning. They found a significant loss of tyrosine hydroxylase (TH+) neurons in the substantia nigra pars compacta (SNc) while the dopaminergic cells in the A13 region were largely preserved. Then, they optically stimulated the A13 region using a viral vector to deliver the channelrhodopsine (CamKII promoter). In both sham and PD model mice, optogenetic stimulation of the A13 region induced pro-locomotor effects, including increased locomotion, more locomotion bouts, longer durations of locomotion, and higher movement speeds. Additionally, PD model mice exhibited increased ipsi lesional turning during A13 region photoactivation. Lastly, the authors used whole-brain imaging to explore changes in the A13 region's connectome after 6-OHDA lesions. These alterations involved a complex rewiring of neural circuits, impacting both afferent and efferent projections. In summary, this study unveiled the pro-locomotor effects of A13 region photoactivation in both healthy and PD model mice. The study also indicates the preservation of A13 dopaminergic cells and the anatomical changes in neural circuitry following PD-like lesions that represent the anatomical substrate for a parallel motor pathway.

Strengths:

These findings hold significant relevance for the field of motor control, providing valuable insights into the organization of the motor system in mammals. Additionally, they offer potential avenues for addressing motor deficits in Parkinson's disease (PD). The study fills a crucial knowledge gap, underscoring its importance, and the results bolster its clinical relevance and overall strength.

The authors adeptly set the stage for their research by framing the central questions in the introduction, and they provide thoughtful interpretations of the data in the discussion section. The results section, while straightforward, effectively supports the study's primary conclusion - the pro-locomotor effects of A13 region stimulation, both in normal motor control and in the 6-OHDA model of brain damage.

We thank the reviewer for their positive comments.

Weaknesses:

(1) Anatomical investigation. I have a major concern regarding the anatomical investigation of plastic changes in the A13 connectome (Figures 4 and 5). While the methodology employed to assess the connectome is technically advanced and powerful, the results lack mechanistic insight at the cell or circuit level into the pro-locomotor effects of A13 region stimulation in both physiological and pathological conditions. This concern is exacerbated by a textual description of results that doesn't pinpoint precise brain areas or subareas but instead references large brain portions like the cortical plate, making it challenging to discern the implications for A13 stimulation. Lastly, the study is generally well-written with a smooth and straightforward style, but the connectome section presents challenges in readability and comprehension. The presentation of results, particularly the correlation matrices and correlation strength, doesn't facilitate biological understanding. It would be beneficial to explore specific pathways responsible for driving the locomotor effects of A13 stimulation, including examining the strength of connections to well-known locomotor-associated regions like the Pedunculopontine nucleus, Cuneiformis nucleus, LPGi, and others in the diencephalon, midbrain, pons, and medulla.

We initially considered two approaches. The first was to look at specific projections to the motor regions, focusing on the MLR. The second was to utilize a whole-brain analysis, which is presented here. Given what we know about the zona incerta, especially its integrative role, we felt that examining the full connectome was a reasonable starting point.

The value of the whole-brain approach is that it provides a high-level overview of the afferents and efferents to the region. The changes in the brain that occur following Parkinson-like lesions, such as those in the nigrostriatal pathway, are complex and can affect neighbouring regions such as the A13. Therefore, we wished to highlight the A13, which we considered a therapeutic target, and examine changes in connectivity that could occur following acute lesions affecting the SNc. We acknowledge that this study does not provide a causal link, but it presents the fundamental background information for subsequent hypothesis-driven, focused, region-specific analysis.

The terms provided were taken from the Allen Brain Atlas terminology and presented as abbreviations. We have added two new figures focusing on motor regions to make the information more comprehensible (new Figures 4 and 5) and rewrote the connectomics section to make it easier to understand.

Additionally, identifying the primary inputs to A13 associated with motor function would enhance the study's clarity and relevance.

This is a great point to help simplify the whole-brain results. We have presented the motor-related inputs and outputs as part of a new figure in the main paper (Figure 5) and added accompanying text in the results section. We have also updated the correlation matrices to concentrate on motor regions (Figure 4). This highlights possible therapeutic pathways. We have also enhanced our discussion of these motor-related pathways. We have retained the entire dataset and added it to our data repository for those interested.

The study raises intriguing questions about compensatory mechanisms in Parkinson's disease and a new perspective on the preservation of dopaminergic cells in A13, despite the SNc degeneration, and the plastic changes to input/output matrices. To gain inspiration for a more straightforward reanalysis and discussion of the results, I recommend the authors refer to the paper titled "Specific populations of basal ganglia output neurons target distinct brain stem areas while collateralizing throughout the diencephalon from the David Kleinfeld laboratory." This could guide the authors in investigating motor pathways across different brain regions.

Thank you for the advice. As pointed out, Kleinfeld’s group presented their data in a nice, focused way. For the connectomic piece, we have added Figure 5, which provides a better representation than our previous submission.

(2) Description of locomotor performance. Figure 3 provides valuable data on the locomotor effects of A13 region photoactivation in both control and 6-OHDA mice. However, a more detailed analysis of the changes in locomotion during stimulation would enhance our understanding of the pro-locomotor effects, especially in the context of 6-OHDA lesions. For example, it would be informative to explore whether the probability of locomotion changes during stimulation in the control and 6-OHDA groups. Investigating reaction time, speed, total distance, and could reveal how A13 is influencing locomotion, particularly after 6-OHDA lesions. The laboratory of Whelan has a deep knowledge of locomotion and the neural circuits driving it so these features may be instructive to infer insights on the neural circuits driving movement. On the same line, examining features like the frequency or power of stimulation related to walking patterns may help elucidate whether A13 is engaging with the Mesencephalic Locomotor Region (MLR) to drive the pro-locomotor effects. These insights would provide a more comprehensive understanding of the mechanisms underlying A13-mediated locomotor changes in both healthy and pathological conditions.

Thank you for these suggestions. We have reorganized Figure 3 to highlight the metrics by separating the 6-OHDA from the Sham experiments (3F-J, which highlights distance travelled, average speed and duration). We have also added additional text to highlight these metrics better in the text. We have relabelled Supplementary Figure S3, which presents reaction time as latency to initiate locomotion and updated the main text to address the reviewers' points.

Reviewer #2 (Public Review):

Summary:

The paper by Kim et al. investigates the potential of stimulating the dopaminergic A13 region to promote locomotor restoration in a Parkinson's mouse model. Using wild-type mice, 6-OHDA injection depletes dopaminergic neurons in the substantia nigra pars compacta, without impairing those of the A13 region and the ventral tegmentum area, as previously reported in humans. Moreover, photostimulation of presumably excitatory (CAMKIIa) neurons in the vicinity of the A13 region improves bradykinesia and akinetic symptoms after 6-OHDA injection. Whole-brain imaging with retrograde and anterograde tracers reveals that the A13 region undergoes substantial changes in the distribution of its afferents and projections after 6-OHDA injection. The study suggests that if the remodeling of the A13 region connectome does not promote recovery following chronic dopaminergic depletion, photostimulation of the A13 region restores locomotor functions.

Strengths:

Photostimulation of presumably excitatory (CAMKIIa) neurons in the vicinity of the A13 region promotes locomotion and locomotor recovery of wild-type mice 1 month after 6-OHDA injection in the medial forebrain bundle, thus identifying a new potential target for restoring motor functions in Parkinson's disease patients.

Weaknesses:

Electrical stimulation of the medial Zona Incerta, in which the A13 region is located, has been previously reported to promote locomotion (Grossman et al., 1958). Recent mouse studies have shown that if optogenetic or chemogenetic stimulation of GABAergic neurons of the Zona Incerta promotes and restores locomotor functions after 6-OHDA injection (Chen et al., 2023), stimulation of glutamatergic ZI neurons worsens motor symptoms after 6-OHDA (Lie et al., 2022).

Thank you - we have added this reference. It is helpful as Grossman did stimulate the zona incerta in the cat and elicit locomotion, suggesting that stimulation of the area in normal mice has external validity. Grossman’s results prompted a later clinical examination of the zona incerta, but it concentrated on the zona incerta regions close to the subthalamic regions (Ossowska 2019), further caudal to the area we focused on. Chen et al. (2023) targeted the area in the lateral aspect of central/medial zona incerta, formed by dorsal and ventral zona incerta, which may account for the differing results. Our data were robust for stimulation of the medial aspect of the rostromedial zona incerta. The thigmotactic behaviour that we observed in our work that focused on CamKII neurons has not been observed with chemogenetic, optogenetic activation or with photoinhibition of GABAergic central/medial ZI (Chen et al. 2023).

GABAergic activation of mZI to Cuneiform projections (Sharma et al. 2024) also did not produce thigmotactic behavior. We have added these points to the discussion.

Although CAMKIIa is a marker of presumably excitatory neurons and can be used as an alternative marker of dopaminergic neurons, behavioral results of this study raise questions about the neuronal population targeted in the vicinity of the A13 region. Moreover, if YFP and CHR2-YFP neurons express dopamine (TH) within the A13 region (Fig. 2), there is also a large population of transduced neurons within and outside of the A13 region that do not, thus suggesting the recruitment of other neuronal cell types that could be GABAergic or glutamatergic.

We found that CamKII transfection of the A13 region was extremely effective in promoting locomotor activity, which was critical for our work in exploring its possible therapeutic potential. We have since quantified the cell number, we found that the c-fos cell number was increased following ChR2 activation. There is evidence of TH activation - but the data suggest that other cell types contribute. C-fos alone is a blunt tool to assess specificity - rather, it is better at showing overall photostimulus efficacy - which we have demonstrated. Moreover, there is evidence that cell types are not purely dopaminergic, with GABA co-localized (Negishi et al. 2020). We acknowledge that specific viral approaches that target the GABAergic, glutamatergic, and dopaminergic circuits would be very useful. The range of tools to target A13 dopaminergic circuits is more limited than the SNc, for example, because the A13 region lacks DAT, and TH-IRES-Cre approaches, while helpful, are less specific than DAT-Cre mouse models. Intersectional approaches targeting multiple transmitters (glutamate & dopamine, for example) may be one solution as we do not expect that a single transmitter-specific pathway would work, as well as broad targeting of the A13 region. Our recent work suggests that GABAergic neuron activation may have more general effects on behaviour rather than control of ongoing locomotor parameters (Sharma et al. 2024). Recent work shows a positive valence effect of dopamine A13 activation on motivated food-seeking behavior, which differs from consummatory behavior observed with GABAergic modulation (Ye, Nunez, and Zhang 2023). Chemogenetic inactivation and ablation of dopaminergic A13 revealed that they contribute to grip strength and prehensile movements, uncoupling food-seeking grasping behavior from motivational factors (Garau et al. 2023). Overall, this suggests differing effects of GABA compared to DA and/or glutamatergic cell types, consistent with our effects of stimulating CamKII. The discussion has been updated.

Regarding the analysis of interregional connectivity of the A13 region, there is a lack of specificity (the viral approach did not specifically target the A13 region), the number of mice is low for such correlation analyses (2 sham and 3 6-OHDA mice), and there are no statistics comparing 6-OHDA versus sham (Fig. 4) or contra- versus ipsilesional sides (Fig. 5). Moreover, the data are too processed, and the color matrices (Fig. 4) are too packed in the current format to enable proper visualization of the data. The A13 afferents/efferents analysis is based on normalized relative values; absolute values should also be presented to support the claim about their upregulation or downregulation.

Generally, papers using tissue-clearing imaging approaches have low sample sizes due to technical complexity and challenges. The technical challenges of obtaining these data were substantial in both collection and analysis. There are multiple technical complexities arising from dual injections (A13 and MFB coordinates) and targeting the area correctly. The A13 region is difficult to target as it spans only around 300 µm in the anterior-posterior axis. While clearing the brain takes weeks, and light-sheet imaging also takes time, the time necessary to analyze the tissue using whole-brain quantification is labor intensive, especially with a lack of a standardized analysis pipeline from atlas registrations, signal segmentations, and quantifications. The field is still relatively new, requiring additional time to refine pipelines.

Correlation matrices are often used in analyzing connectivity patterns on a brain-wide scale, as they can identify any observable patterns within a large amount of data. We used correlation matrices to display estimated correlation coefficients between the afferent and efferent proportions from one brain subregion to another across 251 brain regions in total in a pairwise manner (not for hypothesis testing). We provided descriptive statistics (mean and error bars) in the original Figure 5C and G. As mentioned in comments for Reviewer 1, we have now presented the data in revised Figure 4 and 5 that focuses specifically on motor-related pathways to provide information on possible pathways. The has simplified the correlation matrices and highlighted the differences in 6-OHDA efferent data especially. As suggested, raw values are shared in a supplemental file on our data repository.

In the absence of changes in the number of dopaminergic A13 neurons after 6-OHDA injection, results from this correlation analysis are difficult to interpret as they might reflect changes from various impaired brain regions independently of the A13 region.

We acknowledge that models of Parkinson’s disease, particularly those using 6-OHDA, induce plasticity in various regions, which may subsequently affect A13 connectivity. We aim to emphasize the residual, intact A13 pathways that could serve as therapeutic targets in future investigations. This emphasis is pertinent in the context of potential clinical applications, as the overall input and output to the region fundamentally dictate the significance of the A13 region in lesioned nigrostriatal models. We agree with the reviewer that the changes certainly can be independent of A13; however, the fact that there was a significant change in the connectome post-6-OHDA injection and striatonigral degeneration is in and of itself important to document. We have added a sentence acknowledging this limitation to the discussion.

There is no causal link between anatomical and behavioral data, which raises questions about the relevance of the anatomical data.

This point was also addressed earlier in response to a comment from Reviewer 1. Focusing on specific motor pathways is one avenue to explore. However, given that the zona incerta acts as an integrative hub, we believed it is prudent to initially examine both afferent and efferent pathways using a brain-wide approach. For instance, without employing this methodology, the potential significance of cortical interconnectivity to the A13 region might not have been fully appreciated. As mentioned previously, we will place additional emphasis on motor-related regions in our revised paper, thereby enhancing the relevance of the anatomical data presented. With these modifications, we anticipate that our data will underscore specific motor-related targets for future exploration, employing optogenetic targeting to assess necessity and sufficiency.

Overall, the study does not take advantage of genetic tools accessible in the mouse to address the direct or indirect behavioral and anatomical contributions of the A13 region to motor control and recovery after 6-OHDA injection.

Our study has not specifically targeted neurons that express dopaminergic, glutamatergic, or GABAergic properties (refer to earlier comment for more detail). However, like others, we find that targeting one neuronal population often does not result in a pure transmitter phenotype. For instance, evidence suggests co-localization of dopamine neurons with a subpopulation of GABA neurons in the A13/medial zona incerta (Negishi et al. 2020). In the hypothalamus, research by Deisseroth and colleagues (Romanov et al. 2017) indicates the presence of multiple classes of dopamine cells, each containing different ratios of co-localized peptides and/or fast neurotransmitters. Consequently, we believe our work lays the foundation for the investigations suggested by the reviewer. Furthermore, if one considers this work in the context of a preclinical study to determine whether the A13 might be a target in human Parkinson's disease, the existing technology that could be utilized is deep brain stimulation (DBS) or electrical modulation, which would also affect different neuronal populations in a non-specific manner.

While optogenetic stimulation therapy is longer term, using CamKII combined with the DJ hybrid AAV could be a translatable strategy for targeting A13 neuronal populations in non-human primates (Watakabe et al. 2015; Watanabe et al. 2020). We have added to the discussion.

Reviewer #3 (Public Review):

Kim, Lognon et al. present an important finding on pro-locomotor effects of optogenetic activation of the A13 region, which they identify as a dopamine-containing area of the medial zona incerta that undergoes profound remodeling in terms of afferent and efferent connectivity after administration of 6-OHDA to the MFB. The authors claim to address a model of PD-related gait dysfunction, a contentious problem that can be difficult to treat with dopaminergic medication or DBS in conventional targets. They make use of an impressive array of technologies to gain insight into the role of A13 remodeling in the 6-OHDA model of PD. The evidence provided is solid and the paper is well written, but there are several general issues that reduce the value of the paper in its current form, and a number of specific, more minor ones. Also, some suggestions, that may improve the paper compared to its recent form, come to mind.

Thank you for the suggestions and careful consideration of our work - it is appreciated.

The most fundamental issue that needs to be addressed is the relation of the structural to the behavioral findings. It would be very interesting to see whether the structural heterogeneity in afferent/effects projections induced by 6-OHDA is related to the degree of symptom severity and motor improvement during A13 stimulation.

As mentioned in comments for Reviewer 1, we have performed additional analysis and present this in Figure 5. We have also revised Figure 4, focusing on motor regions. Our work will provide a roadmap for future studies to disentangle divergent or convergent A13 pathways that are involved in different or all PD-related motor symptoms. Because we could not measure behavioural change in the same animals studied with the anatomic study (essentially because the optrode would have significantly disrupted the connectome we are measuring), we cannot directly compare behaviour to structure.

The authors provide extensive interrogation of large-scale changes in the organization of the A13 region afferent and efferent distributions. It remains unclear how many animals were included to produce Fig 4 and 5. Fig S5 suggests that only 3 animals were used, is that correct? Please provide details about the heterogeneity between animals. Please provide a table detailing how many animals were used for which experiment. Were the same animals used for several experiments?

The behavioral set and the anatomical set were necessarily distinct. In the anatomical experiments, we employed both anterograde and retrograde viral approaches to target the afferent and efferent A13 populations with fluorescent proteins. For the behavioral approach, a single ChR2 opsin was utilized to photostimulate the A13 region; hence combining the two populations was not feasible. We were also concerned that the optrode itself would interfere with connectomics. A lower number of animals were used for the whole-brain work due to technical limitations described earlier. We have now provided additional information regarding numbers in all figures and the text. Using Spearman’s correlation analysis, we found afferent and efferent proportions across animals to be consistent, with an average correlation of 0.91, which is reported in Figure S6.

While the authors provide evidence that photoactivation of the A13 is sufficient in driving locomotion in the OFT, this pro-locomotor effect seems to be independent of 6-OHDA-induced pathophysiology. Only in the pole test do they find that there seems to be a difference between Sham vs 6-OHDA concerning the effects of photoactivation of the A13. Because of these behavioral findings, optogenic activation of A13 may represent a gain of function rather than disease-specific rescue. This needs to be highlighted more explicitly in the title, abstract, and conclusion.

Optogenetic activation of A13 may represent a gain of function in both healthy and 6-OHDA mice, highlighting a parallel descending motor pathway that remains intact. 6-OHDA lesions have multiple effects on motor and cognitive function. This makes a single pathway unlikely to rescue all deficits observed in 6-OHDA models. The lack of locomotion observed in 6-OHDA models can be reversed by A13 region photostimulation. Therefore, this is a reversal of a loss of function, in this case. However, the increase in turning represents a gain of function. We have highlighted this as suggested in the discussion.

The authors claim that A13 may be a possible target for DBS to treat gait dysfunction. However, the experimental evidence provided (in particular the lack of disease-specific changes in the OFT) seems insufficient to draw such conclusions. It needs to be highlighted that optogenetic activation does not necessarily have the same effects as DBS (see the recent review from Neumann et al. in Brain: https://pubmed.ncbi.nlm.nih.gov/37450573/). This is important because ZI-DBS so far had very mixed clinical effects. The authors should provide plausible reasons for these discrepancies. Is cell-specificity, which only optogenetic interventions can achieve, necessary? Can new forms of cyclic burst DBS achieve similar specificity (Spix et al, Science 2021)? Please comment.

Thank you for the valuable comments. They have been incorporated into the discussion.

Our study highlights a parallel motor pathway provided by the A13 region that remains intact in 6-OHDA mice and can be sufficiently driven to rescue the hypolocomotor pathology observed in the OFT and overcome bradykinesia and akinesia. The photoactivation of ipsilesional A13 also has an overall additive effect on ipsiversive circling, representing a gain of function on the intact side that contributes to the magnitude of overall motor asymmetry against the lesioned side. The effects of DBS are rather complex, ranging from micro-, meso-, to macro-scales, involving activation, inhibition, and informational lesioning, and network interactions. This could contribute to the mixed clinical effects observed with ZI-DBS, in addition to differences in targeting and DBS programming among the studies (see review (Ossowska 2019) ). Also the DBS studies targeting ZI have never targeted the rostromedial ZI which extends towards the hypothalamus and contains the A13. Furthermore, DBS and electrical stimulation of neural tissue, in general, are always limited by current spread and lower thresholds of activation of axons (e.g., axons of passage), both of which can reduce the specificity of the true therapeutic target. Optogenetic studies have provided mechanistic insights that could be leveraged in overcoming some of the limitations in targeting with conventional DBS approaches. Spix et al. (2021) provided an interesting approach highlighting these advancements. They devised burst stimulation to facilitate population-specific neuromodulation within the external globus pallidus. Moreover, they found a complementary role for optogenetics in exploring the pathway-specific activation of neurons activated by DBS. To ascertain whether A13 DBS may be a viable therapy for PD gait, it will be necessary to perform many more preclinical experiments, and tuning of DBS parameters could be facilitated by optogenetic stimulation in these murine models. We have added to the discussion.

In a recent study, Jeon et al (Topographic connectivity and cellular profiling reveal detailed input pathways and functionally distinct cell types in the subthalamic nucleus, 2022, Cell Reports) provided evidence on the topographically graded organization of STN afferents and McElvain et al. (Specific populations of basal ganglia output neurons target distinct brain stem areas while collateralizing throughout the diencephalon, 2021, Neuron) have shown similar topographical resolution for SNr efferents. Can a similar topographical organization of efferents and afferents be derived for the A13/ ZI in total?

The ZI can be subdivided into four subregions in the antero-posterior axis: rostral (ZIr), dorsal (ZId), ventral (ZIv), and caudal (ZIc) regions. The dorsal and ventral ZI is also referred together as central/medial/intermediate ZI. There are topographical gradients in different cell types and connectivity across these subregions (see reviews: (Mitrofanis 2005; Monosov et al. 2022; Ossowska 2019). Recent work by Yang and colleagues (2022) demonstrated a topographical organization among the inputs and outputs of GABAergic (VGAT) populations across four ZI subregions. Given that A13 region encompasses a smaller portion (the medial aspect) of both rostral and medial/central ZI (three of four ZI subregions) and coexpress VGAT, A13 region likely falls under rostral and intermediate medial ZI dataset found in Yang et al. (2022). With our data, we would not be able to capture the breadth of topographical organization shown in Yang et al (2022).

In conclusion, this is an interesting study that can be improved by taking into consideration the points mentioned above.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Figure 2 indeed presents valuable information regarding the effects of A13 region photoactivation. To enhance the comprehensiveness of this figure and gain a deeper understanding of the neurons driving the pro-locomotor effect of stimulation, it would be beneficial to include quantifications of various cell types:

• cFos-Positive Cells/TH-Positive Cells: it can help determine the impact of A13 stimulation on dopaminergic neurons and the associated pro-locomotor effect in the healthy condition and especially in the context of Parkinson's disease (PD) modeling.

• cFos-Positive Cells /TH-Negative Cells: Investigating the number of TH-negative cells activated by stimulation is also important, as it may reveal non-dopaminergic neurons that play a role in locomotor responses. Identifying the location and characteristics of these TH-negative cells can provide insights into their functional significance.

We have completed this analysis. The data is presented in Figure 2F, where we show increased c-fos intensity with photoactivation. We observed an increase in the number of cells activated in the A13 region. However, we did not definitively see increases in TH+ cells, suggesting a heterogeneous set of neurons responsible for the effects—possibly glutamatergic neurons.

Incorporating these quantifications into Figure 2 would enhance the figure's informativeness and provide a more comprehensive view of the neuronal populations involved in the locomotor effects of A13 stimulation.

We have added text and a new graph.

(2) Refer to Figure 3. In the main text (page 5) when describing the animal with 6-OHDA the wrong panels are indicated. It is indicated in Figure 2A-E but it should be replaced with 3A-E.

Please do that.

Done, and we have updated the figure to improve readability, by separating the 6-OHDA findings from sham in all graphs.

Reviewer #2 (Recommendations For The Authors):

Abstract

Page 1: Inhibitory or lesion studies will be necessary to support the claim that the global remodeling of afferent and efferent projections of the A13 region highlights the Zona Incerta's role as a crucial hub for the rapid selection of motor function.

Overall, there is quite a bit of evidence that the zona incerta is a hub for afferent/efferents.

Mitrofanis (2005) and, more recently, Wang et al. (2020) summarize some of the evidence. Yang (2022) illustrates that the zona incerta shows multiple inputs to GABAergic neurons and outputs to diverse regions. Recent work suggests that the zona incerta contributes to various motor functions such as hunting, exploratory locomotion, and integrating multiple modalities (Zhao et al. 2019; Wang et al. 2019; Monosov et al. 2022; Chometton et al. 2017). The introduction has been updated.

Introduction

Page 2, paragraph 2: "However, little attention has been placed on the medial zona incerta (mZI), particularly the A13, the only dopamine-containing region of the rostral ZI" Is the A13 region located in the rostral or medial ZI or both?

It should have been written “rostromedial” ZI. The A13 is located in the medial aspect of rostromedial ZI. Introduction has been updated.

Page 2, para 3: Li et al (2021) used a mini-endoscope to record the GCaMP6 signal. Masini and Kiehn, 2022 transiently blocked the dopaminergic transmission; they never used 6-OHDA.

Please correct through the text.

Corrected.

Page 2, para 4: the A13 connectome encompasses the cerebral cortex,... MLR. The MLR is a functional region, correct this for the CNF and PPN.

Corrected.

Page 3, the last paragraph of the introduction could be clarified by presenting the behavioral data first, followed by the anatomy.

This has been corrected

Figure 1 is nice and clear, and well summarizes the experimental design.

Thank you.

Figure 2 shows an example of the extent of the ChR2-YFP expression and the position of an optical fiber tip above the dopaminergic A13 region from a mouse. Without any quantification, these images could be included in Figure 1. Despite a very small volume (36.8nL) of AAV, the extent of ChR2-YFP expression is quite large and includes dopaminergic and unidentified neurons within the A13 region but also a large population of unidentified neurons outside of it, thus raising questions about the volume and the types of neurons recruited.

This is an important consideration. The issue of viral spread is complex and depends on factors including tissue type, serotype, and promotor of the virus. Li et al. (2021), for example, used different virus serotypes and promotors, injecting 150nL, whereas we used AAV DJ, injecting 36.8nL. AAV-DJ is a hybrid viral type consisting of multiple serotypes. It has a high transduction efficiency, which leads to greater gene delivery than single-serotype AAV viral constructs (Mao et al. 2016). A secondary consideration regarding translation was that AAV-DJ could effectively transduce non-primate neurons (Watanabe et al. 2020). We have addressed the issue of neurons recruited earlier, provided c-Fos quantification, and provided a new supplementary figure showing viral spread (Figure S1).

Anatomical reconstruction of the extent of the ChR2-YFP expression and the location of the tip of the optical fiber will be necessary to confirm that ChR2-YFP expression was restricted to the A13 region.

We will provide additional information regarding viral spread, ferrule tip placement, and c-fos cell counts. This has been done in Figure 2 and we also present a new Figure S1 where we have quantified the viral spread.

Page 5, 1st para: Double-check the references, as not all of them are 6-OHDA injections in the MLF.

Corrected. Removed Kiehn reference.

Page 5, 1st para, 4th line: Replace ferrule with optical canula or fiber.

Done

Page 5, 1st para, 9th line: Replace Figure 2 with Figure 3.

Done

Page 5, 2nd para: About the refractory decrease in traveled distance by sham-ChR2 mice: is this significant?

It was not significant (Figure S1C, 1-way RM ANOVA: F5,25 = 0.486, P \= 0.783). This has been updated in the text.

Figure 3 showing behavioral assessments is nice, but the stats are not always clear. In Fig 3A, are each of the off and on boxes 1 minute long? The figure legend states the test lasts 1 min, but isn't it 4 minutes? In Figure 3B-E and 3J-M, what are the differences? Do the stats identify a significant difference only during the stimulation phase? Fig. 3F-I are nice and could have been presented as primary examples prior to data analysis in Fig. 3B-E. Group labels above the graph would help.

Yes, the off-on boxes are 1 minute long. The error is corrected in the legend. Great suggestion for F-I - they have been moved ahead of the summary figures. We have also updated new Fig 3F-,I, J, L, M) to make the differences between 6-OHDA and sham graphs easier to visualize. The stats do indicate a significant difference during the stimulation phase. We have added group labels, and reorganized the figure, and it is much easier to read now.

Fig. 3L-M, what do PreSur, Post, and Ferrule mean? I assume that Ferrule refers to mice tested with the optical fiber without stimulation, whereas Stim. refers to the stimulation. It would be helpful to standardize the format of stats in Fig. 3B-E and 3-J-M. What are time points a, b, and c referring to?

We have renamed the figure names to be more intuitive. We have standardized the presentation of statistics in the figure, and eliminated the a,b,c nomenclature. We have also updated the caption to provide descriptions of the tests in Fig 3 L-M.

Figure S2A: the higher variability in 6-OHDA-YFP mice in comparison to 6-OHDA-ChR2 mice prior to stimulation suggests that 6-OHDA-YFP mice were less impaired. Why use boxplots only for these data? Would a pairwise comparison be more appropriate?

We have removed these plots from Figure S2. We now present the Baseline to Pre values across the experimental timespan to illustrate the fact that distance travelled returned to baseline values for all trials conducted.

Fig. S2B: add the statistical marker.

We have removed this from Figure S2.

Page 7, para 1, line 8: to add "in comparison to 6-OHDA-YFP and YFP mice" to during photostimulation... (Figure 3E).

Done

Page 7, para 3, line 5: about larger improvement, replace "sham ChR2" with "6-OHDA."

Done

Page 8, para 1, line 4: Perier et al., 2000 reported that 6-OHDA injection increased the firing frequency of the ZI over a month.

Added the timeframe to this sentence.

Page 8, para 2, line 1: Since the results were expected, add some references.

Done.

Page 8, para 3, line 4. Double-check the reference.

Corrected.

Page 8: About large-scale changes in the A13 region, the relevance of correlation matrices is difficult to grasp. Analysis of local connectivity would have been more informative in the context of GABAergic and glutamatergic neurons of the ZI in the vicinity of the A13 region.

We have updated the figures for connectivity throughout the manuscript. Overall, there are new Figures 4 and 5 in the main text. We also provide a revised Supplementary Figure 8. Unfortunately, we could not do that experiment regarding local connectivity. In light of our new work (Sharma et al. 2024), it is clear that this will be critical going forward.

Page 8, para 3, line: given Fig. 2, there is concern about the claim that only the A13 region was targeted. The time of the analysis after 6-OHDA should be mentioned. Some sections of the paragraph could be moved to methods.

We have provided more information about the viral spread in the text and Supplementary Figure 1. The functional and anatomical experiments are separate, which we realize caused confusion. We have mentioned analysis time after 6-OHDA and inserted this into the text.

Fig. 4: The color code helps the reader visualize distribution differences. However, statistical analyses comparing 6-OHDA versus sham should be included. Quantification per region would greatly help readers visualize the data and support the conclusion. The relationship between the type of correlation (positive or negative) and absolute change (increase or decrease) is unknown in the current format, which limits the interpretation of the data. Moreover, examples of raw images of axons and cells should be presented for several brain regions. The experimental design with a timeline, as in Fig. 1, would be helpful. The legend for Fig. 4 is a bit long. Some sections are very descriptive, whereas others are more interpretive.

We have provided a new Figure 5 where we present quantification per region, and the correlation matrices have been updated in Figure 4. We have also focused on motor regions as mentioned earlier. We also provide examples of raw regions in Supplementary Figure 8. Raw values are shared on our data repository.

Page 10, para 1, line 1: add "afferent" to "changes in -afferent and- projection patterns."

Done

Page 10, para 1, line 9: remove the 2nd "compared to sham" in the sentence.

Done

Page 10, para 1, line 10: remove "coordinated" in "several regions showed a coordinated reduction in afferent density." We cannot say anything about the timing of events, as there is only info at 1 month.

Done

Page 10, para 2: the section should be written in the past tense.

Done

Page 13, para 2, the last sentence is overstated. Please remove "cells" and refer to the A13 region instead.

Done

About differential remodelling of the A13 region connectome: Figure 5C and 5G: The proportion of total afferents ipsi- and contralateral to 6-OHDA injection argues that the A13 region primarily receives inputs from the cortical plate and the striatum. Unfortunately, there are no statistics.

Due to the small sample size, we provided descriptive statistics (mean and error bars) in Figure 5A. As mentioned in comments for Reviewers 1 and 2, we have revised Figure 5 to present data focusing on motor-related pathways to provide clarity. In addition, absolute values are shared on our data repository.

Figure 5 D and 5H: Changes in the proportion of total afferents/projections are relatively modest (less than 10% of the whole population for the highest changes). There is no standard deviation for these data and no statistics. Do they reflect real changes or variability from the injection site?

The changes are relatively modest (less than 10%) since a small brain region usually provides a small proportion of total input (McElvain et al. 2021; Yang et al. 2022). The changes in the proportions reflect real differences between average proportions observed in sham and 6-OHDA mice. The variability in the total labelling of neurons and fibers was minimized by normalizing individual regional counts against total counts found in each animal. This figure has been updated as reviewers requested.

Fig 5F and H: The example in F shows a huge decrease in the striatum, but H indicates only a 2% change, which makes the example not very representative. Absolute values would be helpful.

While a 2% change may seem small, it represents a relatively large change in the A13 efferent connectome. To provide further clarity, we have provided absolute values as suggested in our new supplemental table.

Figure 6 is inaccurate and unnecessary.

Figure 6 has been removed.

Discussion

Although interesting, the discussion is too long.

The discussion has been reduced by about three quarters of a page.

Methods

Page 17, para 1: include the stereotaxic coordinates of the optical cannula above the A13 region.

Added.

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eLife Assessment

This important study uses extensive comparative analysis to examine the relationship between plasma glucose levels, albumin glycation levels, and diet and life history, within the framework of the "pace of life syndrome" hypothesis. The evidence that glucose is positively correlated with glycation levels and lifespan is convincing and, although there are some limitations related to data collection, they likely make the statistically significant findings more conservative. As the first extensive comparative analysis of glycation rates, life history, and glucose levels in birds, the study has the potential to be of interest to evolutionary ecologists and the aging research community more broadly.

Reviewer #2 (Public review):

Summary:

In this extensive comparative study, Moreno-Borrallo and colleagues examine the relationships between plasma glucose levels, albumin glycation levels, diet and life-history traits across birds. Their results confirmed the expected positive relationship between plasma blood glucose level and albumin glycation rate but also provided findings that are somewhat surprising or contrast with findings of some previous studies (positive relationships between blood glucose and lifespan, or absent relationships between blood glucose and clutch mass or diet). This is the first extensive comparative analysis of glycation rates and their relationships to plasma glucose levels and life history traits in birds that is based on data collected in a single study, with blood glucose and glycation measured using unified analytical methods (except for blood glucose data for 13 species collected from a database).

Strengths:

This is an emerging topic gaining momentum in evolutionary physiology, which makes this study a timely, novel and important contribution. The study is based on a novel data set collected by the authors from 88 bird species (67 in captivity, 21 in the wild) of 22 orders, except for 13 species, for which data were collected from a database of veterinary and animal care records of zoo animals (ZIMS). This novel data set itself greatly contributes to the pool of available data on avian glycemia, as previous comparative studies either extracted data from various studies or a ZIMS database (therefore potentially containing much more noise due to different methodologies or other unstandardised factors), or only collected data from a single order, namely Passeriformes. The data further represents the first comparative avian data set on albumin glycation obtained using a unified methodology. The authors used LC-MS to determine glycation levels, which does not have problems with specificity and sensitivity that may occur with assays used in previous studies. The data analysis is thorough, and the conclusions are substantiated. Overall, this is an important study representing a substantial contribution to the emerging field evolutionary physiology focused on ecology and evolution of blood/plasma glucose levels and resistance to glycation.

Weaknesses:

Unfortunately, the authors did not record handling time (i.e., time elapsed between capture and blood sampling), which may be an important source of noise because handling-stress-induced increase in blood glucose has previously been reported. Moreover, the authors themselves demonstrate that handling stress increases variance in blood glucose levels. Both effects (elevated mean and variance) are evident in Figure ESM1.2. However, this likely makes their significant findings regarding glucose levels and their associations with lifespan or glycation rate more conservative, as highlighted by the authors.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

Summary

In this extensive comparative study, Moreno-Borrallo and colleagues examine the relationships between plasma glucose levels, albumin glycation levels, diet and lifehistory traits across birds. Their results confirmed the expected positive relationship between plasma blood glucose level and albumin glycation rate but also provided findings that are somewhat surprising or contrast with findings of some previous studies (positive relationships between blood glucose and lifespan, or absent relationships between blood glucose and clutch mass or diet). This is the first extensive comparative analysis of glycation rates and their relationships to plasma glucose levels and life history traits in birds that is based on data collected in a single study, with blood glucose and glycation measured using unified analytical methods (except for blood glucose data for 13 species collected from a database).

Strengths

This is an emerging topic gaining momentum in evolutionary physiology, which makes this study a timely, novel and important contribution. The study is based on a novel data set collected by the authors from 88 bird species (67 in captivity, 21 in the wild) of 22 orders, except for 13 species, for which data were collected from a database of veterinary and animal care records of zoo animals (ZIMS). This novel data set itself greatly contributes to the pool of available data on avian glycemia, as previous comparative studies either extracted data from various studies or a ZIMS database (therefore potentially containing much more noise due to different methodologies or other unstandardised factors), or only collected data from a single order, namely Passeriformes. The data further represents the first comparative avian data set on albumin glycation obtained using a unified methodology. The authors used LC-MS to determine glycation levels, which does not have problems with specificity and sensitivity that may occur with assays used in previous studies. The data analysis is thorough, and the conclusions are substantiated. Overall, this is an important study representing a substantial contribution to the emerging field evolutionary physiology focused on ecology and evolution of blood/plasma glucose levels and resistance to glycation.

Weaknesses

Unfortunately, the authors did not record handling time (i.e., time elapsed between capture and blood sampling), which may be an important source of noise because handling-stress-induced increase in blood glucose has previously been reported. Moreover, the authors themselves demonstrate that handling stress increases variance in blood glucose levels. Both effects (elevated mean and variance) are evident in Figure ESM1.2. However, this likely makes their significant findings regarding glucose levels and their associations with lifespan or glycation rate more conservative, as highlighted by the authors.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I understand that your main objective regarding glycation rate and lifespan, was to analyse the species resistance to glycation with respect to lifespan, while factoring out the species-specific variation in blood glucose level. However, I still believe that the absolute glycation level (i.e., not controlled for blood glucose level) may also be important for the evolution of lifespan. Given that blood glucose is positively related to both glycation and lifespan (although with a plateau in the latter case), lifespan could possibly be positively correlated with absolute glycation levels. If significant, that would be an interesting and counterintuitive finding, which would call for an explanation, thereby potentially stimulating further research. If not significant, it would show that long-lived species do not have higher glycation levels, despite having higher blood glucose levels, thereby strengthening your argument about higher resistance of longlived species to glycation. So, in my opinion, the inclusion of an additional model of glycation level on life-history traits, without controlling for blood glucose, is worth considering.

We include now this model as supplementary material, indicating it in several parts of the text, including some of these issues we discussed here.

Lines 230-231: Please, provide a citation for these GVIF thresholds

We include it now.

Figure 3: I think that showing both glucose and glycation rate on the linear scale, rather than log scale, would better illustrate your conclusion - the slowing rise of glycation rate with increasing glucose levels.

That is a good point, although it may also be confusing for readers to see a graph that represents the data in a different way as the models. Maybe showing both graphs (as 3.A and 3.B) can solve it?

Figure 4. I recommend stating in the caption that the whiskers do not represent interquartile ranges (a standard option in box plots) but credible intervals as mentioned in the current version of the public author response.

Sorry about that, it was missed. Now it is included. Nevertheless, interquartile ranges from the posterior distributions can still be observed here represented with the boxes. Then the whiskers are the credible intervals.

eLife Assessment

This valuable study by Guo and colleagues reports the inhibitory activity of caffeic acid phenethyl ester (CAPE) against TcdB, a key toxin produced by Clostridioides difficile. C. difficile infections are a major public health concern, and this manuscript provides interesting data on toxin inhibition by CAPE, a potentially promising therapeutic alternative for this disease. The strength of the evidence to support the conclusions is solid, with some concerns about the moderate effects on the mouse infection model and direct binding assays of CAPE to the toxin.

Reviewer #1 (Public review):

Summary:

In this manuscript, Guo and colleagues used a cell rounding assay to screen a library of compounds for inhibition of TcdB, an important toxin produced by Clostridioides difficile. Caffeic acid and derivatives were identified as promising leads, and caffeic acid phenethyl ester (CAPE) was further investigated.

Strengths:

Considering the high morbidity rate associated with C. difficile infections (CDI), this manuscript presents valuable research in the investigation of novel therapeutics to combat this pressing issue. Given the rising antibiotic resistance in CDI, the significance of this work is particularly noteworthy. The authors employed a robust set of methods and confirmatory tests, which strengthen the validity of the findings. The explanations provided are clear, and the scientific rationale behind the results is well-articulated. The manuscript is extremely well written and organized. There is a clear flow in the description of the experiments performed. Also, the authors have investigated the effects of CAPE on TcdB in careful detail, and reported compelling evidence that this is a meaningful and potentially useful metabolite for further studies.

Weaknesses:

The authors have made some changes in the revised version. However, many of the changes were superficial, and some concerns still need to be addressed. Important details are still missing from the description of some experiments. Authors should carefully revise the manuscript to ascertain that all details that could affect interpretation of their results are presented clearly. For instance, authors still need to include details of how the metabolomics analyses were performed. Just stating that samples were "frozen for metabolomics analyses" is not enough. Was this mass-spec or NMR-based metabolomics. Assuming it was mass-spec, what kind? How was metabolite identity assigned, etc? These are important details, which need to be included. Even in cases where additional information was included, the authors did not discuss how the specific way in which certain experiments were performed could affect interpretation of their results. One example is the potential for compound carryover in their experiments. Another important one is the fact that CAPE affects bacterial growth and sporulation. Therefore, it is critical that authors acknowledge that they cannot discard the possibility that other factors besides compound interactions with the toxin are involved in their phenotypes. As stated previously, authors should also be careful when drawing conclusions from the analysis of microbiota composition data, and changes to the manuscript should be made to reflect this. Ascribing causality to correlational relationships is a recurring issue in the microbiome field. Again, I suggest authors carefully revise the manuscript and tone down some statements about the impact of CAPE treatment on the gut microbiota.

Reviewer #2 (Public review):

I appreciate the author's responses to my original review. This is a comprehensive analysis of CAPE on C. difficile activity. It seems like this compound affects all aspects of C. difficile, which could make it effective during infection but also make it difficult to understand the mechanism. Even considering the authors responses, I think it is critical for the authors to work on the conclusions regarding the infection model. There is some protection from disease by CAPE but some parameters are not substantially changed. For instance, weight loss is not significantly different in the C. difficile only group versus the C. difficile + CAPE group. Histology analysis still shows a substantial amount of pathology in the C. difficile + CAPE group. This should be discussed more thoroughly using precise language.

Reviewer #3 (Public review):

Summary:

The study is well written, and the results are solid and well demonstrated. It shows a field that can be explored for the treatment of CDI

Strengths:

Results are really good, and the CAPE shows a good and promising alternative for treating CDI.

Weaknesses:

Some references are too old or missing.

Comments on revisions:

I have read your study after comments made by all referees, and I noticed that all questions and suggestions addressed to the authors were answered and well explained. Some of the minor and major issues related to the article were also solved. I am satisfied with all the effort given by the authors to improve their manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Guo and colleagues used a cell rounding assay to screen a library of compounds for inhibition of TcdB, an important toxin produced by Clostridioides difficile. Caffeic acid and derivatives were identified as promising leads, and caffeic acid phenethyl ester (CAPE) was further investigated.

Strengths:

Considering the high morbidity rate associated with C. difficile infections (CDI), this manuscript presents valuable research in the investigation of novel therapeutics to combat this pressing issue. Given the rising antibiotic resistance in CDI, the significance of this work is particularly noteworthy. The authors employed a robust set of methods and confirmatory tests, which strengthened the validity of the findings. The explanations provided are clear, and the scientific rationale behind the results is well-articulated. The manuscript is extremely well-written and organized. There is a clear flow in the description of the experiments performed. Also, the authors have investigated the effects of CAPE on TcdB in careful detail and reported compelling evidence that this is a meaningful and potentially useful metabolite for further studies.

Weaknesses:

This is really a manuscript about CAPE, not caffeic acid, and the title should reflect that. Also, a few details are missing from the description of the experiments. The authors should carefully revise the manuscript to ascertain that all details that could affect the interpretation of their results are presented clearly. Just as an example, the authors state in the results section that TcdB was incubated with compounds and then added to cells. Was there a wash step in between? Could compound carryover affect how the cells reacted independently from TcdB? This is just an example of how the authors should be careful with descriptions of their experimental procedures. Lastly, authors should be careful when drawing conclusions from the analysis of microbiota composition data. Ascribing causality to correlational relationships is a recurring issue in the microbiome field. Therefore, I suggest authors carefully revise the manuscript and tone down some statements about the impact of CAPE treatment on the gut microbiota.

Thanks for your constructive suggestion. We have carefully revised the manuscript, including the description of title, results and methods sections.

Reviewer #2 (Public review):

Summary:

This work is towards the development of nonantibiotic treatment for C. difficile. The authors screened a chemical library for activity against the C. difficile toxin TcdB, and found a group of compounds with antitoxin activity. Caffeic acid derivatives were highly represented within this group of antitoxin compounds, and the remaining portion of this work involves defining the mechanism of action of caffeic acid phenethyl ester (CAPE) and testing CAPE in mouse C. difficile infection model. The authors conclude CAPE attenuates C. difficile disease by limiting toxin activity and increasing microbial diversity during C. difficile infection.

Strengths/ Weaknesses:

The strategy employed by the authors is sound although not necessarily novel. A compound that can target multiple steps in the pathogenies of C. difficile would be an exciting finding. However, the data presented does not convincingly demonstrate that CAPE attenuates C. difficile disease and the mechanism of action of CAPE is not convincingly defined. The following points highlight the rationale for my evaluation.

(1) The toxin exposure in tissue culture seems brief (Figure 1). Do longer incubation times between the toxin and cells still show CAPE prevents toxin activity?

Thanks for your comments. The cytotoxicity assay was employed to directly assess the protective capacity of CAPE against cell death induced by TcdB. Our observations at 1 and 12 h post-TcdB exposure revealed that CAPE effectively mitigated the toxic effects of the TcdB at both time points, demonstrating its potent protective role. Please see Figure S1.

(2) The conclusion that CAPE has antitoxin activity during infection would be strengthened if the mouse was pretreated with CAPE before toxin injections (Figure 1D).

Thanks for your constructive comments. According to your suggestion, we administered TcdB 2 h after pretreatment with CAPE. The outcomes demonstrated that CAPE pretreatment significantly enhanced the survival rate of the intoxicated mice, confirming that CAPE retains its antitoxin efficacy during the infection process. Please see Figure S2.

(3) CAPE does not bind to TcdB with high affinity as shown by SPR (Figure 4). A higher affinity may be necessary to inhibit TcdB during infection. The GTD binds with millimolar affinity and does not show saturable binding. Is the GTD the binding site for CAPE? Auto processing is also affected by CAPE indicating CAPE is binding non-GTD sites on TcdB.

Thanks for your comments. Our findings indicate that the GTD domain is a critical binding site for CAPE. CAPE exerts its protective effects at multiple stages of TcdB-mediated cell death, including inhibiting TcdB's self-cleavage and blocking the activity of GTD, thereby preventing the glycosylation modification of Rac1 by TcdB.

(4) In the infection model, CAPE does not statistically significantly attenuate weight loss during C. difficile infection (Figure 6). I recognize that weight loss is an indirect measure of C. difficile disease but histopathology also does not show substantial disease alleviation (see below).

Thanks for your comments. Our comparative analysis revealed a notable distinction in the body weight of mice on the third day post-infection (Figure 6B). Similarly, the dry/wet stool ratio exhibited a comparable pattern, suggesting that treatment with phenethyl caffeic acid ameliorated Clostridium difficile-induced diarrhea to a significant degree (Figure 6C).

(5) In the infection model (Figure 6), the histopathology analysis shows substantial improvement in edema but limited improvement in cellular infiltration and epithelial damage. Histopathology is probably the most critical parameter in this model and a compound with disease-modifying effects should provide substantial improvements.

Thanks for your comments. Edema, inflammatory factor infiltration, and epithelial damage served as key evaluation metrics. Statistical analysis revealed that the pathological scores of mice treated with CAPE were markedly reduced compared to those in the model group (Figure 6F).

(6) The reduction in C. difficile colonization is interesting. It is unclear if this is due to antitoxin activity and/or due to CAPE modifying the gut microbiota and metabolites (Figure 6). To interpret these data, a control is needed that has CAPE treatment without C. difficile infection or infection with an atoxicogenic strain.

The observed reduction in C. difficile fecal colonization following drug treatment may be attributed to the CAPE's antitoxin properties or its capacity to modify the intestinal microbiota and metabolites. These two mechanisms likely work in tandem to combat CDI. CDI is primarily triggered by the toxins A (TcdA) and B (TcdB) secreted by the bacterium. Certain therapies, including monoclonal antibodies like bezlotoxumab, target CDI by neutralizing these toxins, thereby mitigating gut damage and subsequent C. difficile colonization(1,2). The establishment of C. difficile in the gut is intricately linked to the equilibrium of the intestinal microbiota. Although antibiotic treatments can inhibit C. difficile growth, they may also disrupt the microbial balance, potentially facilitating the overgrowth of other pathogens. Consequently, interventions such as fecal microbiota transplantation (FMT) are designed to reestablish gut flora balance and consequently decrease C. difficile colonization(3,4). Moreover, the administration of probiotics and prebiotics is considered to reduce C. difficile colonization by modifying the gut environment(5,6).

(7) Similar to the CAPE data, the melatonin data does not display potent antitoxin activity and the mouse model experiment shows marginal improvement in the histopathological analysis (Figure 9). Using 100 µg/ml of melatonin (~ 400 micromolar) to inactivate TcdB in cell culture seems high. Can that level be achieved in the gut?

The uptake and dissemination of melatonin within the body varies with the dose administered. For instance, in rats, the bioavailability of melatonin following administration was found to be 53.5%, whereas in dogs, bioavailability was nearly complete (100%) at a dose of 10 mg/kg, yet it decreased to 16.9% at a lower dose of 1 mg/kg(7). This data suggests that the absorption of melatonin differs across various animal species and is influenced by the dose administered. Moreover, it underscores the higher potential bioavailability of melatonin, implying that a dose of 200 mg/kg should be adequate to achieve the desired concentration in the body post-administration.

(8) The following parameters should be considered and would aid in the interpretation of this work. Does CAPE directly affect the growth of C. difficile? Does CAPE affect the secretion of TcdB from C. difficile? Does CAPE alter the sporulation and germination of C. diffcile?

We incorporated CAPE into the MIC assay for detecting C. difficile, as well as for assessing the sporulation capacity of C. difficile and evaluating the secretion level of TcdB. The findings revealed that CAPE markedly repressed tcdB transcription at a concentration of 16 μg/mL and effectively suppressed the growth and sporulation of C. difficile BAA-1870 at a concentration of 32 μg/mL. Please see Figure S3.

References:

(1) Skinner AM, et al. Efficacy of bezlotoxumab to prevent recurrent Clostridioides difficile infection (CDI) in patients with multiple prior recurrent CDI. Anaerobe. 2023 Dec; 84: 102788.

(2) Wilcox MH, et al. Bezlotoxumab for Prevention of Recurrent Clostridium difficile Infection. N Engl J Med. 2017 Jan 26;376(4):305-317.

(3) Khoruts A, Sadowsky MJ. Understanding the mechanisms of faecal microbiota transplantation. Nat Rev Gastroenterol Hepatol. 2016 Sep;13(9):508-16.

(4) Khoruts A, Staley C, Sadowsky MJ. Faecal microbiota transplantation for Clostridioides difficile: mechanisms and pharmacology. Nat Rev Gastroenterol Hepatol. 2021 Jan;18(1):67-80.

(5) Mills JP, Rao K, Young VB. Probiotics for prevention of Clostridium difficile infection. Curr Opin Gastroenterol. 2018 Jan;34(1):3-10.

(6) Lau CS, Chamberlain RS. Probiotics are effective at preventing Clostridium difficile-associated diarrhea: a systematic review and meta-analysis. Int J Gen Med. 2016 Feb 22; 9:27-37.

(7) Yeleswaram K, et al. Pharmacokinetics and oral bioavailability of exogenous melatonin in preclinical animal models and clinical implications. J Pineal Res. 1997 Jan;22(1):45-51.

Reviewer #3 (Public review):

Summary:

The study is well written, and the results are solid and well demonstrated. It shows a field that can be explored for the treatment of CDI.

Strengths:

The results are really good, and the CAPE shows a good and promising alternative for treating CDI. The methodology and results are well presented, with tables and figures that corroborate them. It is solid work and very promising.

Weaknesses:

Some references are too old or missing.

Thanks for your constructive suggestion. We have included and refreshed several references to enhance the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

While the manuscript convincingly demonstrates that CAPE affects the TcdB toxin and reduces its toxicity in vitro, it would be beneficial to include data on the effect of CAPE on the growth of C. difficile. This would help ensure that the observed in vivo effects are not merely due to reduced bacterial growth but rather due to the specific action of CAPE on the toxin.

Thanks for your constructive suggestion. We have augmented our findings with the impact of CAPE on the bacteria themselves, revealing that CAPE not only hampers the growth of the bacterial cells but also suppresses their capacity to produce spores. Please see Figure S3.

(1) Line 41, line 115 - authors should clarify what they mean when mentioning Bacteroides within parentheses.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(2) Line 71 - Is C. difficile really found "in the environment"?

Thanks for your comments. C. difficile is prevalent across various natural settings, including soil and water ecosystems. A study has identified highly diverse strains of this bacterium within environmental samples(1). Moreover, the significant presence of C. difficile in soil and lawn specimens collected near Australian hospitals indicates that the organism is indeed a common inhabitant in the environment(2).

(3) Lines 128-130 - Was there a wash step here? What could be the impact of compound carryover in this experiment?

Thanks for your comments. Following pre-incubation of TcdB with CAPE, remove the compounds that have not bound to TcdB through centrifugation. The persistence of the compound in the culture post-washing could result in an inflated assessment of its efficacy, particularly if it continues to engage with TcdB or the cells beyond the initial 1-hour pre-incubation window. The carryover of the compound might also give rise to misleading positive results, where the compound seems to confer protection or inhibition against TcdB-mediated cell rounding, whereas such effects are actually due to the lingering activity of the compound. This carryover could skew the determination of the compound's minimum effective concentration, as the effective concentration interacting with the cells might be inadvertently elevated. Furthermore, if the compounds possess cytotoxic properties or impact cell viability, carryover could generate artifacts in cell morphology that are unrelated to the direct interaction between TcdB and the compounds.

(4) Lines 133-134 - I suggest authors mention how many caffeic acid derivatives there were in the entire library so that the suggested "enrichment" of them in the group of bioactive compounds can be better judged.

Thanks for your comments. The natural compound library contained eight caffeic acid derivatives, of which methyl caffeic acid and ferulic acid displayed no efficacy. This information has been incorporated into the manuscript.

(5) Line 135 - I recommend the authors add the molarity of the compound solutions used.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(6) Line 247 - I think the term "CAPE mice" is confusing. Please use a full description.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(7) Line 248 - I also think the terms "model mice" and "model group" are confusing. Maybe call them "control mice"?

Thanks for your comments. The terms "model mice" and "model group" are indeed synonymous, and we have subsequently clarified that control mice refer to those that have not been infected with C. difficile.

(8) Line 273 - "most abundant species at the genus level" is incorrect. I think what you mean is "most abundant TAXA".

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(9) Line 278 - Please include your p-value cut-off together with the LDA score.

Thanks for your comments. We have revised the above description to “LDA score > 3.5, p < 0.05”.

(10) Line 292 - Details on how metabolomics was performed should be included here.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(11) Line 299 - 1.5 is a fairly low cut-off. The authors should at a minimum also include the p-value cut-off used.

Response: Thanks for your comments. We have revised the above description to “fold change > 1.5, p < 0.05”.

(12) Line 307 - Purine "degradation" would be better here.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(13) Line 328 onward - The melatonin experiment is a weird one. Although I fully understand the rationale behind testing the effect of melatonin in the mouse model, the idea that just because melatonin levels changed in the gut it would act as a direct inhibitor of TcdB was very far-fetched, even though it ended up working. Authors should explain this in the manuscript.

Thanks for your comments. Furthermore, beyond our murine studies, we have confirmed that melatonin significantly diminishes TcdB-induced cytotoxicity at the cellular level (Figure 9A). Additionally, it has been documented that melatonin, acting as an antimicrobial adjuvant and anti-inflammatory agent, can decrease the recurrence of CDI(3). Consequently, we contend that the aforementioned statement is substantiated.

(14) Lines 429-435 - There are seemingly contradictory pieces of information here. The authors state that adenosine is released from cells upon inflammation and that CAPE treatment caused an increase in adenosine levels. Later in this section, the authors state that adenosine prevents TcdA-mediated damage and inflammation. This should be clarified and better discussed.

Thanks for your comments. Adenosine modulates immune responses and inflammatory cascades by interacting with its receptors, including its capacity to suppress the secretion of specific pro-inflammatory mediators. We have updated this depiction in the manuscript.

(15) Lines 513-514 - How was this phenotype quantified?

Thanks for your comments. Initially, we introduced TcdB at a final concentration of 0.2 ng/mL along with various concentrations of compounds into 1 mL of medium for a 1-h pre-incubation period. Subsequently, unbound compounds were removed through centrifugation, and the resulting mixture was then applied to the cells.

(16) Figure 3 - panels are labeled incorrectly.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(17) Figure 5C - it is unclear what the different colors and labels represent.

Thanks for your comments. In the depicted graph, blue denotes the total binding energy, red signifies the electrostatic interactions, green corresponds to the van der Waals forces, and orange indicates solvation or hydration effects. The horizontal axis represents the mutation of the amino acid residue at the respective position to alanine. As illustrated in Figure 5C, the mutations W520A and GTD exhibit the highest binding energies.

References:

(1) Janezic S, et al. Highly Divergent Clostridium difficile Strains Isolated from the Environment. PLoS One. 2016 Nov 23;11(11): e0167101.

(2) Perumalsamy S, Putsathit P, Riley TV. High prevalence of Clostridium difficile in soil, mulch and lawn samples from the grounds of Western Australian hospitals. Anaerobe. 2019 Dec; 60:102065.

(3) Sutton SS, et al. Melatonin as an Antimicrobial Adjuvant and Anti-Inflammatory for the Management of Recurrent Clostridioides difficile Infection. Antibiotics (Basel). 2022 Oct 25;11(11):1472.

Reviewer #2 (Recommendations for the authors):

Minor comments and questions.

(1) Which form of TcdB is being used in these experiments?

Thanks for your comments. The TcdB proteins used in this study are TcdB1 subtypes.

(2) Why are THP-1 cells being used in these assays?

Thanks for your comments. For the purposes of this study, we employed a diverse array of cell lines, including Vero, HeLa, THP-1, Caco-2, and HEK293T. Each cell line was selected to serve a specific experimental objective. The inclusion of the THP-1 cell line was necessitated by the need to incorporate a macrophage cell line to ensure the comprehensive nature of our experiments, allowing for the testing of both epithelial cells and macrophages. C. difficile is a kind of intestinal pathogenic bacteria, and immune clearance plays a vital role in the process of pathogen infection, so THP-1 cells are used as important immune cells.

(3) Please improve the quality of the microscopy images in Figure 1.

Thanks for your comments. We have improved the quality of the microscopy images in Figure 1.

(4) Does the flow cytometry experiment in Figure 2B show internalization? Surface-bound toxins would provide the same histogram.

Thanks for your comments. Figure 2B was employed to assess the internalization of TcdB, and the findings indicate that CAPE does not influence the internalization process of TcdB.

(5) The sensogram in Figure 4A does not look typical and should be clarified.

Thanks for your comments. Typically, small molecules and proteins engage in a rapid binding and dissociation dynamic. However, as depicted in Figure 4A, the interaction between CAPE and TcdB demonstrates a gradual progression towards equilibrium. This behavior can be primarily explained by the swift occupation of the protein's primary binding sites by the small molecule in the initial stages. Subsequently, CAPE binds to secondary or lower affinity sites, extending the time needed to reach equilibrium. Additionally, the likelihood of CAPE binding to multiple sites on TcdB requires time for the exploration and occupation of these diverse locations before equilibrium is attained, we have incorporated an analysis of this potential scenario into the manuscript.

Reviewer #3 (Recommendations for the authors):

These are my suggestions for the text:

(1) Line 29: high recurrent rates.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(2) Line 32: Where is the caffeic acid identified? I think a line should be included.

Thanks for your comments. Caffeic acid was identified from natural compounds library and we have completed the corresponding modifications according to the suggestions.

(3) Line 39: C. difficile is not italic.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(4) Line 41: Bacteroides spp.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

(5) Line 56: This number of casualties 56.000 is still happening or it was in the past?

Thanks for your comments. The mortality rates reported in the manuscript reflect a downturn in the incidence and fatality of CDI around 2017(1), as the infection gained broader recognition. Nonetheless, a recent study reveals that the mortality rate for CDI cases in Germany can soar to 45.7% within a year, with the overall economic burden amounting to approximately 1.6 billion euros. This underscores the ongoing significance of CDI as a global public health challenge(2).

(6) Line 104: Where did the idea of testing caffeic acid come from? Any previous study of the authors? Any studies with the inhibition of other pathogens?

Thanks for your comments. Initially, we conducted a screen of a compound library comprising 2,076 compounds and identified several potent inhibitors, which, upon structural analysis, were revealed to be caffeic acid derivatives. Prior to our investigation, no studies had explored the potential of CAPE in this context.

(7) Line 115: Bacteroides spp.

Thanks for your comments. We have completed the corresponding modifications according to the suggestions.

Results section

(8) Did the authors try the caffeic acid with the TcdA or binary toxin? I know this is not the purpose of the study, but TcdA toxin has a high identity structure with TcdB and generates inflammation in the gut via neutrophils. Negative strains for the major toxins and positive for the binary toxin also cause severe cases of CDI.

Thanks for your comments. Although we acknowledge the significance of TcdA and binary toxins in CDI, we did not investigate the impact of CAPE on these toxins. Our focus was exclusively on the effect of CAPE against TcdB, as it is the primary virulence factor in C. difficile pathogenesis. Since TcdA and TcdB are highly similar in structure, we will analyze the neutralization effect of CAPE on TcdA in later studies.

(9) Does caffeic acid have any effect on C. difficle? Or does it only gain the toxins? That would be ideal.

Thanks for your comments. We have included additional related assays in our study. Beyond directly neutralizing TcdB, CAPE also demonstrates the capacity to inhibit the growth and spore formation of C. difficile.

(10) Line 230: C. difficile BAA-1870 is a clinical strain? There are no details about it in the paper.

Thanks for your comments. C. difficile BAA-1870 (RT027/ST1), a highly virulent isolate frequently employed in research(3-6), was kindly donated by Professor Aiwu Wu. We have meticulously noted the PCR ribotype in our manuscript.

(11) Line 236: Did the mice fully recover from CDI after the administration of the CAPE? Was one dose enough?

Thanks for your comments. CAPE was administered orally at 24 h intervals, commencing with the initial dose on Day 0. By the time a significant difference was observed on Day 3, the treatment had been administered a total of three times.

Methodology

(12) Most of the methods do not have a reference.

Thanks for your comments. We have added several references to the methods.

Discussion section

(13) The first two paragraphs of the discussion should be summarized. Those details were already explained in the introduction.

Thanks for your comments. The discussion section and the introduction address slightly different focal points; therefore, we aim to retain the first two paragraphs to maintain continuity and context.

(14) Line 382: Bezolotoxumab was approved by the FDA in 2016. It is not recent.

Thanks for your comments. We have revised the above description.

(15) Line 410: "Despite the high 410 cure rate and increasing popularity of FMT, its safety remains controversial. Although this is true, recently (2022) the FDA approved the Rebyota, which was later cited by the authors.

Thanks for your comments. We have revised the above description.

(16) Lines 415-416: "the abundance of Bacteroides, a critical gut microbiota component that is required for C. difficile resistance". There is only one reference cited by the authors. I suppose that if it is true, more studies should be mentioned. Why are probiotics with Bacteroides spp. not available in the market?

Thanks for your comments. We have supplemented additional references. The scarcity of probiotic products containing Bacteroides spp. on the market is primarily attributable to the stringent requirements of their survival conditions. As most Bacteroides spp. are anaerobic, they thrive in oxygen-deprived environments. This unique survival trait poses challenges in maintaining their viability during product preservation and distribution, which in turn escalates production costs and complexity. Furthermore, despite the significant role of Bacteroides in gut health, research into its potential probiotic benefits and safety is comparatively underexplored.

References:

(1) Guh AY, et al. Emerging Infections Program Clostridioides difficile Infection Working Group. Trends in U.S. Burden of Clostridioides difficile Infection and Outcomes. N Engl J Med. 2020 Apr 2;382(14):1320-1330.

(2) Schley K, et al. Costs and Outcomes of Clostridioides difficile Infections in Germany: A Retrospective Health Claims Data Analysis. Infect Dis Ther. 2024 Nov 20.

(3) Saito R, et al. Hypervirulent clade 2, ribotype 019/sequence type 67 Clostridioides difficile strain from Japan. Gut Pathog. 2019 Nov 4; 11:54.

(4) Pellissery AJ, Vinayamohan PG, Venkitanarayanan K. In vitro antivirulence activity of baicalin against Clostridioides difficile. J Med Microbiol. 2020 Apr;69(4):631-639.

(5) Shao X, et al. Chemical Space Exploration around Thieno[3,2-d]pyrimidin-4(3H)-one Scaffold Led to a Novel Class of Highly Active Clostridium difficile Inhibitors. J Med Chem. 2019 Nov 14;62(21):9772-9791.

(6) Mooyottu S, Flock G, Venkitanarayanan K. Carvacrol reduces Clostridium difficile sporulation and spore outgrowth in vitro. J Med Microbiol. 2017 Aug;66(8):1229-1234.

eLife Assessment

The manuscript provides an important assessment of the number and distribution of different retrovirus env genes present in primate genomes in the form of ancient endogenous retroviruses (ERV loci) and the potential role that viral recombination played in the diversification of retrovirus env genes and their propagation in the primate germline over millions of years. The paper convincingly describes how intermixing/recombination occurs with this viruses, representing a conceptual advance with potentially broad implications.

Reviewer #3 (Public review):

Summary:

Retroviruses have been endogenized into the genome of all vertebrate animals. The envelope protein of the virus is not well conserved and acquires many mutations hence can be used to monitor viral evolution. Since they are incorporated into the host genome, they also reflect the evolution of the hosts. In this manuscript the authors have focused their analyses to the env genes of endogenous retroviruses in primates. Important observations made include the extensive recombination events between these retroviruses that were previously unknown and the discovery of HML species in genomes prior to the splitting of old and new world monkeys.

Strengths:

They explored a number of databases and made phylogenetic trees to look at the distribution of retroviral species in primates. The authors provide a strong rationale for their study design, they provide a clear description of the techniques and the bioinformatics tools used.

Weaknesses:

The manuscript is based on bioinformatics analyses only. The reference genomes do not reflect the polymorphisms in humans or other primate species. The analyses thus likely under estimate the amount of diversity in the retroviruses. Further experimental verification will be needed to confirm the observations.

Not sure which databases were used, but if not already analyzed, ERVmap.com and repeatmesker are ones that have many ERVs that are not present in the reference genomes. Also long range sequencing of the human genome has recently become available which may also be worth studying for this purpose.

Comments on revisions:

All comments have been adequately addressed.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary

Chabukswar et al analysed endogenous retrovirus (ERV) Env variation in a set of primate genomes using consensus Env sequences from ERVs known to be present in hominoids using a Blast homology search with the aim of characterising env gene changes over time. The retrieved sequences were analysed phylogenetically, and showed that some of the integrations are LTR-env recombinants.

Strengths

The strength of the manuscript is that such an analysis has not been performed yet for the subset of ERV Env genes selected and most of the publicly available primate genomes.

Weaknesses

Unfortunately, the weaknesses of the manuscript outnumber its strengths. Especially the methods section does not contain sufficient information to appreciate or interpret the results. The results section contains methodological information that should be moved, while the presentation of the data is often substandard. For instance, the long lists of genomes in which a certain Env was found could better be shown in tables. Furthermore, there is no overview of the primate genomes Saili how did you answer to this?, or accession numbers, used. It is unclear whether the analyses, such as the phylogenetic trees, are based on nucleotide or amino acid sequences since this is not stated. tBLASTn was used in the homology searches, so one would suppose aa are retrieved. In the Discussion, both env (nt?) and Env (aa?) are used.

For the non-hominoids, genome assembly of publicly available sequences is not always optimal, and this may require Blasting a second genome from a species. Which should for instance be done for the HML2 sequences found in the Saimiri boliviensis genome, but not in the related Callithrix jacchus genome. Finally, the authors propose to analyse recombination in Env sequences but only retrieve env-LTR recombinant Envs, which should likely not have passed the quality check.

Since the Methods section does not contain sufficient information to understand or reproduce the results, while the Results are described in a messy way, it is unclear whether or not the aims have been achieved. I believe not, as characterisation of env gene changes over time is only shown for a few aberrant integrations containing part of the LTR in the env ORF.

We thank the reviewer for the critiques of the manuscript and their constructive suggestions to improve the clarity, methodological rigor, and data presentation.

(1) The concern regarding the insufficient data in the methods has been resolved in the revised manuscript by adding a supplementary file that contains the genome assemblies that  were used to perform the tBLAStn analysis using the reconstructed Env sequences. The requested accession numbers are available for all sequences in the supplementary phylogenetic figures.

(2) We have also modified the manuscript by moving a portion of the results section in the methods section, in particular all the methodological description of the reconstruction of Env part (Line 197-231).

(3) As suggested, the long list of genomes mentioned in the results section in which the Env tBLASTn hits were obtained are now provided in the table form (Table 2) as an overall summary of the distribution of ERV Env in the genomes and the genome assemblies are mentioned in Supplementary file 2.

(4) As for the point regarding the tBLASTn usage in the homology searches, we first performed tBLASTn analysis using the reconstructed Env amino acid sequences as query and performed tBLASTn similarity search in the primate genomes. The tBLASTn algorithm uses the amino acid sequences to compare with the translated nucleotide database in all six frames and hence the hits obtained are nucleotide sequences (Line 381-383). These nt sequences were used for all the further analysis such as sequence alignment, phylogenetic analysis and recombination analysis. For better clarity, we have specified the use of env nt alignments in the methods section to avoid the raised confusion in the discussion.

(5) For the HML supergroup characterization in squirrel monkey genome (Saimiri boliviensis), we used the tBLASTn hits obtained in the S. boliviensis from the initial analysis to perform the comparative genomics in two Platyrrhini genomes available on UCSC Genome browser. In particular, this analysis was performed to confirm the presence of specific members of HML supergroup in squirrel monkey genomes that has not been previously reported. We used the available genome assemblies because of the annotations available on Genome browser, and especially the possibility to use the repeatmasker tracks and the comparative genomics tools in order to use the human genome as a reference. We reported the coordinates for the members of HML supergroup that were retrieved through the comparative genomic assemblies by applying the repeat masker custom track, that have many ERVS that are not present in NCBI reference genomes.

(6) The concern regarding only retrieving env-LTR recombinant Envs has been addressed in the revised results section (Lines 747-758). As also mentioned in the methods section, the RDP software detects the recombinant sequences and a breakpoint position for the recombinant signals and hence we confirmed only those sequences that were predicted as potential recombinant sequences by the RDP software through comparative genomics. All the sequences predicted by the software were env-LTR recombinant and hence we confirmed and reported only those recombinant sequences in the manuscript.

Reviewer #1 (Recommendations for the authors):

The paper could be strengthened by:

- a rigorous rewriting and shortening of the manuscript, thereby eliminating all textbook-like paragraphs, and all biological misinterpretations and confusions. Distinguish between retroviral replication as an exogenous virus, and host genome remodeling affecting ERVs. Rewrite the sections on template switching by RT being the basis for the observed recombinations, while host genome recombinations are far more likely. ERVs with such aberrant env/LTR gene recombination are unlikely to be fit for cross-species transmission. Likely, such a recombinant was generated in a common ancestor. Also, host RNA polymerase II transcribes retroviral RNA (line 79), not RT.

- check lines 89-90 as pro is part of the pol gene in gamma- and lentiviruses.

We thank the reviewer for the suggestion, we have revised the manuscript by shortening the introduction section and eliminating the textbook like paragraphs and also clarifying the recombination mechanism. We have revised the introduction section at Lines 102-111, and the clarification for the recombination mechanism is provided at lines 1668-1675

- adding much more information to the Methods section. Such as which genomes were searched, were nt or aa have been retrieved and analysed, were multiple genomes of a species searched, a list of databases used ('various databases' in line 164 does not suffice), etc.

We thank the reviewer for the observation. As mentioned above, in the revised manuscript we have provided more detailed methods by including a supplementary file for the genome assemblies used for tBLASTn analysis and comparative genomics. For the sequence alignment, phylogenetic analysis and recombination analysis we used nt sequences, as it is also mentioned in the revised version. Lastly, all the databases that were used and are mentioned in the methods section.

- more information is needed on the alignments and phylogenetic trees. For instance, how were indels treated? How long were the alignments on average regarding informative sites?

We thank the reviewer for the questions, to answer them we have added a paragraph (Lines 359-362) describing the reconstruction process in more details.

- confirm the findings about the presence or absence of an ERV, such as for the squirrel monkey genome, using additional genomes of the species

As mentioned above, we only used the genome assemblies available on the genome browser because of the annotations available on Genome browser, blasting the second NCBI RefSeq genome using the BLAST algorithm does not provide accurate information and annotations compared to that of Genome browser and hence we reported the coordinates for the members of HML supergroup that were retrieved through the comparative genomic assemblies by applying the repeat masker custom track, that have many ERVS that are not present in NCBI reference genomes.

- present the lists of findings in primate genomes on pages 9 and 10 in tables

We thank the reviewer for the suggestion, we have provided a new table (Table 2) in the revised version summarizing the ERV Env distribution results.

- a significant limitation of the study is that only env ERVs found in hominoids have been searched in OWM and NWM, not ones specific for monkeys. This should be mentioned somewhere.

As the reviewer pointed out, the study was designed to explore ERVs’ Env  sequences in hominoids which were then searched in the OWM and NWM genomes, this is now better stated in the introduction at Lines 57-60.

- define abbreviations at first use (e.g. HML in abstract)

We thank the reviewer for the suggestion, we have mentioned the abbreviations in the abstract, where we mentioned HML first (Line 65)

- explain 'pathological domestication' (line 42). Domestication implies usefulness to the host. And over time, deleterious insertions would have been likely purged from a population.

We thank the reviewer for the observation, we have modified the sentence and provided a clearer explanation for the pathological and physiological consequences of ERVs’ env (lines 52-57).

Furthermore:

- why begin the discussion with a lengthy description of domestication and syncytins, which is not part of the current study?

We thank the reviewer for the critique. Accordingly, we have now modified the discussion section by shortening the part about domestication of syncytins, and just mentioned them as an example at lines 942-944.

- how can 96 hits have been retrieved for spuma-like envs (line 506), while it was earlier reported (line 333), that the most hits were gamma-like?

We thank the reviewer for the observation, we have clarified and explained how 96 hits have been retrieved for spuma-like envs in lines 670-677 of the discussion section.

English grammar should be improved throughout the manuscript.

And I could not open half of the supplementary files

As suggested we have revised English and checked that all files were correctly open.

Reviewer #2 (Public Review):

Summary:

The manuscript by Chabukswar et al. describes a comprehensive attempt to identify and describe the diversity of retroviral envelope (env) gene sequences present in primate genomes in the form of ancient endogenous retrovirus (ERV) sequences.

Strengths:

The focus on env can be justified because of the role the Env proteins likely played in determining viral tropism and host range of the viruses that gave rise to the ERV insertions, and to a lesser extent, because of the potential for env ORFs to be coopted for cellular functions (in the rare cases where the ORF is still intact and capable of encoding a functional Env protein). In particular, these analyses can reveal the potential roles of recombination in giving rise to novel combinations of env sequences. The authors began by compiling env sequences from the human genome (from human endogenous retrovirus loci, or "HERVs") to build consensus Env protein sequences, and then they use these as queries to screen other primate genomes for group-specific envs by tBLASTn. The "groups" referred to here are previously described, as unofficial classifications of endogenous retrovirus sequences into three very broad categories - Class I, Class II and Class III. These are not yet formally recognized in retroviral taxonomy, but they each comprise representatives of multiple genera, and so would fall somewhere between the Family and Genus levels. The retrieved sequences are subject to various analyses, most notably they are screened for evidence of recombination. The recombinant forms appear to include cases that were probably viral dead-ends (i.e. inactivating the env gene) even if they were propagated in the germline.

The availability of the consensus sequences (supplement) is also potentially useful to others working in this area.

Weaknesses:

The weaknesses are largely in presentation. Discussions of ERVs are always complicated by the lack of a formal and consistent nomenclature and the confusion between ERVs as loci and ERVs as indirect information about the viruses that produced them. For this reason, additional attention needs to be paid to precise wording in the text and/or the use of illustrative figures.

We thank the reviewer for the general observation. We put additional attention to the wording in text/figures, and hope to have improved the manuscript clarity.

Reviewer #2 (Recommendations for the authors):

Reviewing the manuscript was a challenge because figures were difficult to read. As provided, the fonts were sometimes too small to read in a standard layout and had to be expanded on screen.

The tree in Figure 3 could also be made easier to read, for example if the authors collapsed related branches and gave the clusters a single, clear label (this is not necessary, just a suggestion) - especially if the supplementary trees have all the labelled branches for any readers who want specific details.

I also recommend asking a third party (perhaps a scientific colleague) with fluency in English grammar and familiarity with English scientific idiom to provide some editorial feedback on the text.

Figure 4 legend is confusing. From the description it sounds like the tree in 4B is a host phylogeny, but it's not clearly stated. And if so, how was the tree generated? Is it based on entire genomes? Include at least enough methodological detail or citations that someone could recreate it, if necessary. The details and how it was done should be briefly mentioned here and in detail in the Methods section.

We thank the reviewer for the observation. As for Figure 4 we have modified its legend and more clearly stated how the phylogenetic tree of the primate genomes was generated using TimeTree. We have also provided further details in the methods section (Lines 475-489).

As suggested we have revised English.

Line 42 - what is "pathological domestication"? It sounds like a contradiction in terms.

We thank the reviewer for the observation. We have modifies the sentence and provided clearer explanation for the pathological and physiological consequences of ERVs’ env (lines 52-57).

Lines 166-167 - the authors use the word "classes" but then use a list of terms that correspond to genera within the Retroviridae. The authors should be cautious here, as "class" and "genus" are both official taxonomic terms with different meanings. Do they mean genus? Or, if a more informal term is needed, perhaps "group"?

Thank you for the observation, the ERVs have been classified into three classes (Class I, II and III) based on the relatedness to the exogenous retroviruses Gammaretrovirus, Betaretrovirus and Spumaretrovirus genera respectively and hence have been mentioned in the manuscript as per the nomenclature proposed by Gifford et al., 2018 which has been cited at Lines 122-125.

Line 221- "defferent" should be "different"

Corrected

Lines 233-234 - what is meant by "canonical" and "non-canonical" forms? Can the authors please define these two terms?

Thank you for the question, canonical refers to sequences that are well-preserved and match the structural and functional features of complete env genes, and non-canonical refers to sequences with significant structural alterations or truncations that deviate from this typical form. This explanation has been mentioned in the revised version at Lines 475-479.

Line 252 - if/is

Corrected

Lines 274-276 needs a citation to the paper(s) that reported this.

Corrected

Line 283-285 - this was confusing. How could the authors have noted distinct occurrences and clusters of these if they were excluded from the BLAST analysis? It says the consensus sequences were effectively representing these, but doesn't this raise the possibility that the consensus sequences are not specific enough? Could this also then lead to false identification? Perhaps a few more words to explain should be added.

We thank the reviewer for the observation. While performing the tBlastn search we did obtain the hits for HERV15, HERVR, ERVV1, ERVV2 and PABL, and we have mentioned the detailed explanation about this observation in the revised manuscript at lines 619-627.

Line 298 - missing comma

Corrected

Lines 348-351- this list is not a list of recombination mechanisms. Template switching is a mechanism of recombination, but "acquisition" is simply a generic term, "degradation" is not a mechanism, and "cross-species transmission" might be a driver or a result of recombination, but it is not a mechanism of recombination.

We thank the reviewer for the observation. We have revised the explanation for the recombination events in the discussion section, as some parts of the results have been moved to discussion section (Lines 1058-1065)

Lines 369-372. It's not clear why this means the event was a "very recent occurrence". Do the authors mean that there were shared integration sites between some of the species, and that these sites lacked the insertions in other species (e.g. gibbon, orangutan, monkeys)?

For the long section on recombination events involving an env sequence with an LTR in it, can the authors explain how they know when it's a recombination event versus integration of one provirus into another one, followed by recombination between LTRs to generate a solo-LTR?

We thank the reviewer for the observation. Regarding the very recent occurrence of the recombination event, we have explained it in revised manuscript at lines 769-824 writing “In fact, the recombinant sequences were shared only between 4 species of Catarrhini parvorder and were absent in more distantly related primates (such as gibbons, orangutans, etc.). This with the presence of shared recombination sites suggests that the insertion occurred after the divergence of these species, while its absence in others indicate that it is a recombination event.”

For the observation regarding the env-LTR recombination events, the recombinants were first detected by the RDP software and were further validated through the BLAT search in the genomes available on genome browser. The explanation on how we obtained these env-LTR recombination events is now provided in lines 746-763 of the revised manuscript.

Methods Lines 151-168 and Figure 1 legend Lines 689-690 - how did the authors distinguish between "translated regions" corresponding to the actual Env protein sequence from translation of the other two reading frames? That is, there must have been substantial "translatable" stretches of sequence in the two incorrect reading frames as well as the reading frame corresponding to Env, so the question is how were the correct ones identified for the reconstruction?

We thank the reviewer for the observation. We have provided the detailed explanation to the observation in the methods section (Lines 335-359).

Line 495 - "previously reported" should include citation(s) of the prior report(s).

We thank the reviewer for the observation, we have provided appropriate citations.

Line 525 - the authors propose that the mechanism "is the co-packaging of different ERVs in a virus particle". First, I assume they meant to say that RNA from different ERVs is co-packaged. Second, isn't it also possible or likely that these could arise from co-packaging of exogenous retrovirus RNAs and recombination, especially if the related exogenous forms were still circulating at the time these things arose?

We thank the reviewer for the observation. We have modified in the revised manuscript a proposed mechanism that includes also the possibility of co-packaging of exogenous retrovirus RNAs and recombination, at lines 1082-1099

Line 686 - env should either be italicized (gene) or capitalized (protein), depending on what the authors intended here.

We thank the reviewer for the observation. We have corrected the typological error in the new version of manuscript.

Reviewer #3 (Public review):

Summary:

Retroviruses have been endogenized into the genome of all vertebrate animals. The envelope protein of the virus is not well conserved and acquires many mutations hence can be used to monitor viral evolution. Since they are incorporated into the host genome, they also reflect the evolution of the hosts. In this manuscript the authors have focused their analyses on the env genes of endogenous retroviruses in primates. Important observations made include the extensive recombination events between these retroviruses that were previously unknown and the discovery of HML species in genomes prior to the splitting of old and new world monkeys.

Strengths:

They explored a number of databases and made phylogenetic trees to look at the distribution of retroviral species in primates. The authors provide a strong rationale for their study design, they provide a clear description of the techniques and the bioinformatics tools used.

Weaknesses:

The manuscript is based on bioinformatics analyses only. The reference genomes do not reflect the polymorphisms in humans or other primate species. The analyses thus likely underestimates the amount of diversity in the retroviruses. Further experimental verification will be needed to confirm the observations.

Not sure which databases were used, but if not already analyzed, ERVmap.com and repeatmesker are ones that have many ERVs that are not present in the reference genomes. Also, long range sequencing of the human genome has recently become available which may also be worth studying for this purpose.

We thank the reviewer for the observations and comments. We would like to clarify that the intent of the work was to perform bioinformatics analysis and so a wet lab experimental verification of the observations are out of the scope of the present manuscript. For the aim of the manuscript, we have used the NCBI reference genomes, while for the report of the coordinates of HML supergroup in the squirrel monkey genome and the coordinates of the recombination events through BLAT search we have used genomes assemblies available on Genome browser with repeat masker custom track, since it has well represented ERV annotations.

The suggestion regarding using long range sequencing of human genome is an interesting perspective and hence in the future work we will try to implement it in our analysis as well as perform an experimental verification, since, again, the focus of the present work does not include wet experimental part.

Reviewer #3 (Recommendations for the authors):

In a few places the term HERV has been used when describing ERVs in non-human primates. This needs to be corrected.

We thank the reviewer for the observation. We have checked and accordingly modified the terms in the manuscript wherever necessary.

eLife Assessment

This study provides a valuable contribution to understanding how negative affect influences food-choice decision making in bulimia nervosa, using a mechanistic approach with a drift diffusion model (DDM) to examine the weighting of tastiness and healthiness attributes. The solid evidence is supported by a robust crossover design and rigorous statistical methods, although concerns about low trial counts, possible overfitting, and the absence of temporally aligned binge-eating measures limit the strength of causal claims. Addressing modeling transparency, sample size limitations, and the specificity of mood induction effects, would enhance the study's impact and generalizability to broader populations.

Reviewer #1 (Public review):

Summary:

Using a computational modeling approach based on the drift diffusion model (DDM) introduced by Ratcliff and McKoon in 2008, the article by Shevlin and colleagues investigates whether there are differences between neutral and negative emotional states in:

(1) The timings of the integration in food choices of the perceived healthiness and tastiness of food options between individuals with bulimia nervosa (BN) and healthy participants.

(2) The weighting of the perceived healthiness and tastiness of these options.

Strengths:

By looking at the mechanistic part of the decision process, the approach has the potential to improve the understanding of pathological food choices. The article is based on secondary research data.

Weaknesses:

I have two major concerns and a major improvement point.

The major concerns deal with the reliability of the results of the DDM (first two sections of the Results, pages 6 and 7), which are central to the manuscript, and the consistency of the results with regards to the identification of mechanisms related to binge eating in BN patients (i.e. last section of the results, page 7).

(1) Ratcliff and McKoon in 2008 used tasks involving around 1000 trials per participant. The Chen et al. experiment the authors refer to involves around 400 trials per participant. On the other hand, Shevlin and colleagues ask each participant to make two sets of 42 choices with two times fewer participants than in the Chen et al. experiment. Shevlin and colleagues also fit a DDM with additional parameters (e.g. a drift rate that varies according to subjective rating of the options) as compared to the initial version of Ratcliff and McKoon. With regards to the number of parameters estimated in the DDM within each group of participants and each emotional condition, the 5- to 10-fold ratio in the number of trials between the Shevlin and colleagues' experiment and the experiments they refer to (Ratcliff and McKoon, 2008; Chen et al. 2022) raises serious concerns about a potential overfitting of the data by the DDM. This point is not highlighted in the Discussion. Robustness and sensitivity analyses are critical in this case.

The authors compare different DDMs to show that the DDM they used to report statistical results in the main text is the best according to the WAIC criterion. This may be viewed as a robustness analysis. However, the other DDM models (i.e. M0, M1, M2 in the supplementary materials) they used to make the comparison have fewer parameters to estimate than the one they used in the main text. Fits are usually expected to follow the rule that the more there are parameters to estimate in a model, the better it fits the data. Additionally, a quick plot of the data in supplementary table S12 (i.e. WAIC as a function of the number of parameters varying by food type in the model - i.e. 0 for M0, 2 for M1, 1 for M2 and 3 for M3) suggests that models M1 and potentially M2 may be also suitable: there is a break in the improvement of WAIC between model M0 and the three other models. I would thus suggest checking how the results reported in the main text differ when using models M1 and M2 instead of M3 (for the taste and health weights when comparing M3 with M1, for τS when comparing M3 with M2). If the differences are important, the results currently reported in the main text are not very reliable.

(2) The second main concern deals with the association reported between the DDM parameters and binge eating episodes (i.e. last paragraph of the results section, page 7). The authors claim that the DDM parameters "predict" binge eating episodes (in the Abstract among other places) while the binge eating frequency does not seem to have been collected prospectively. Besides this methodological issue, the interpretation of this association is exaggerated: during the task, BN patients did not make binge-related food choices in the negative emotional state. Therefore, it is impossible to draw clear conclusions about binge eating, as other explanations seem equally plausible. For example, the results the authors report with the DDM may be a marker of a strategy of the patients to cope with food tastiness in order to make restrictive-like food choices. A comparison of the authors' results with restrictive AN patients would be of interest. Moreover, correlating results of a nearly instantaneous behavior (i.e. a couple of minutes to perform the task with the 42 food choices) with an observation made over several months (i.e. binge eating frequency collected over three months) is questionable: the negative emotional state of patients varies across the day without systematically leading patients to engage in a binge eating episode in such states.

I would suggest in such an experiment to collect the binge craving elicited by each food and the overall binge craving of patients immediately before and after the task. Correlating the DDM results with these ratings would provide more compelling results. Without these data, I would suggest removing the last paragraph of the Results.

(3) My major improvement point is to tone down as much as possible any claim of a link with binge eating across the entire manuscript and to focus more on the restrictive behavior of BN patients in between binge eating episodes (see my second major concern about the methods). Additionally, since this article is a secondary research paper and since some of the authors have already used the task with AN patients, if possible I would run the same analyses with AN patients to test whether there are differences between AN (provided they were of the restrictive subtype) and BN.

Reviewer #2 (Public review):

Summary:

Binge eating is often preceded by heightened negative affect, but the specific processes underlying this link are not well understood. The purpose of this manuscript was to examine whether affect state (neutral or negative mood) impacts food choice decision-making processes that may increase the likelihood of binge eating in individuals with bulimia nervosa (BN). The researchers used a randomized crossover design in women with BN (n=25) and controls (n=21), in which participants underwent a negative or neutral mood induction prior to completing a food-choice task. The researchers found that despite no differences in food choices in the negative and neutral conditions, women with BN demonstrated a stronger bias toward considering the 'tastiness' before the 'healthiness' of the food after the negative mood induction.

Strengths:

The topic is important and clinically relevant and methods are sound. The use of computational modeling to understand nuances in decision-making processes and how that might relate to eating disorder symptom severity is a strength of the study.

Weaknesses:

The sample size was relatively small and may have been underpowered to find differences in outcomes (i.e., food choice behaviors). Participants were all women with BN, which limits the generalizability of findings to the larger population of individuals who engage in binge eating. It is likely that the negative affect manipulation was weak and may not have been potent enough to change behavior. Moreover, it is unclear how long the negative affect persisted during the actual task. It is possible that any increases in negative affect would have dissipated by the time participants were engaged in the decision-making task.

Reviewer #3 (Public review):

Summary:

The study uses the food choice task, a well-established method in eating disorder research, particularly in anorexia nervosa. However, it introduces a novel analytical approach - the diffusion decision model - to deconstruct food choices and assess the influence of negative affect on how and when tastiness and healthiness are considered in decision-making among individuals with bulimia nervosa and healthy controls.

Strengths:

The introduction provides a comprehensive review of the literature, and the study design appears robust. It incorporates separate sessions for neutral and negative affect conditions and counterbalances tastiness and healthiness ratings. The statistical methods are rigorous, employing multiple testing corrections.

A key finding - that negative affect induction biases individuals with bulimia nervosa toward prioritizing tastiness over healthiness - offers an intriguing perspective on how negative affect may drive binge eating behaviors.

Weaknesses:

A notable limitation is the absence of a sample size calculation, which, combined with the relatively small sample, may have contributed to null findings. Additionally, while the affect induction method is validated, it is less effective than alternatives such as image or film-based stimuli (Dana et al., 2020), potentially influencing the results.

Another concern is the lack of clarity regarding which specific negative emotions were elicited. This is crucial, as research suggests that certain emotions, such as guilt, are more strongly linked to binge eating than others. Furthermore, recent studies indicate that negative affect can lead to both restriction and binge eating, depending on factors like negative urgency and craving (Leenaerts et al., 2023; Wonderlich et al., 2024). The study does not address this, though it could explain why, despite the observed bias toward tastiness, negative affect did not significantly impact food choices.

Author response:

eLife Assessment

This study provides a valuable contribution to understanding how negative affect influences food-choice decision making in bulimia nervosa, using a mechanistic approach with a drift diffusion model (DDM) to examine the weighting of tastiness and healthiness attributes. The solid evidence is supported by a robust crossover design and rigorous statistical methods, although concerns about low trial counts, possible overfitting, and the absence of temporally aligned binge-eating measures limit the strength of causal claims. Addressing modeling transparency, sample size limitations, and the specificity of mood induction effects, would enhance the study's impact and generalizability to broader populations.

We thank the Editor and Reviewers for their summary of the strengths of our study, and for their thoughtful review and feedback on our manuscript. We apologize for the confusion in how we described the multiple steps performed and hierarchical methods used to ensure that the model we report in the main text was the best fit to the data while not overfitting. We are not certain about what is meant by “[a]ddressing model transparency,” but as described in our response to Reviewer 1 below, we have now more clearly explained (with references) that the use of hierarchical estimation procedures allows for information sharing across participants, which improves the reliability and stability of parameter estimates—even when the number of trials per individual is small. We have clarified for the less familiar reader how our Bayesian model selection criterion penalizes models with more parameters (more complex models). Although details about model diagnostics, recoverability, and posterior predictive checks are all provided in the Supplementary Materials, we have clarified for the less familiar reader how each of these steps ensures that the parameters we estimate are not only identifiable and interpretable, but also ensure that the model can reproduce key patterns in the data, supporting the validity of the model. Additionally, we have provided all scripts for estimating the models by linking to our public Github repository. Furthermore, we have edited language throughout to eliminate any implication of causal claims and acknowledged the limitation of the small sample size.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Using a computational modeling approach based on the drift diffusion model (DDM) introduced by Ratcliff and McKoon in 2008, the article by Shevlin and colleagues investigates whether there are differences between neutral and negative emotional states in:

(1) The timings of the integration in food choices of the perceived healthiness and tastiness of food options between individuals with bulimia nervosa (BN) and healthy participants.

(2) The weighting of the perceived healthiness and tastiness of these options.

Strengths:

By looking at the mechanistic part of the decision process, the approach has the potential to improve the understanding of pathological food choices. The article is based on secondary research data.

Weaknesses:

I have two major concerns and a major improvement point.

The major concerns deal with the reliability of the results of the DDM (first two sections of the Results, pages 6 and 7), which are central to the manuscript, and the consistency of the results with regards to the identification of mechanisms related to binge eating in BN patients (i.e. last section of the results, page 7).

(1) Ratcliff and McKoon in 2008 used tasks involving around 1000 trials per participant. The Chen et al. experiment the authors refer to involves around 400 trials per participant. On the other hand, Shevlin and colleagues ask each participant to make two sets of 42 choices with two times fewer participants than in the Chen et al. experiment. Shevlin and colleagues also fit a DDM with additional parameters (e.g. a drift rate that varies according to subjective rating of the options) as compared to the initial version of Ratcliff and McKoon. With regards to the number of parameters estimated in the DDM within each group of participants and each emotional condition, the 5- to 10-fold ratio in the number of trials between the Shevlin and colleagues' experiment and the experiments they refer to (Ratcliff and McKoon, 2008; Chen et al. 2022) raises serious concerns about a potential overfitting of the data by the DDM. This point is not highlighted in the Discussion. Robustness and sensitivity analyses are critical in this case.

We thank the Reviewer for their thoughtful critique. We agree that a limited number of trials can forestall reliable estimation, which we acknowledge in the Discussion section. However, we used a hierarchical estimation approach which leverages group information to constrain individual-level estimates. This use of group-level parameters to inform individual-level estimates reduces overfitting and noise that can arise when trial counts are low, and the regularization inherent in hierarchical fitting prevents extreme parameter estimates that could arise from noisy or limited data (Rouder & Lu, 2005). As a result, hierarchical estimation has been repeatedly shown to work well in settings with low trial counts, including as few as 40 trials per condition (Ratcliff & Childers, 2015; Wiecki et al., 2013), and previous applications of the time-varying DDM to food choice task data has included experiments with as few as 60 trials per condition (Maier et al., 2020). We have added references to these more recent approaches and specifically note their advantages for the modeling of tasks with fewer trials. Additionally, our successful parameter recovery described in the Supplementary Materials supports the robustness of the estimation procedure and the reliability of our results.

The authors compare different DDMs to show that the DDM they used to report statistical results in the main text is the best according to the WAIC criterion. This may be viewed as a robustness analysis. However, the other DDM models (i.e. M0, M1, M2 in the supplementary materials) they used to make the comparison have fewer parameters to estimate than the one they used in the main text. Fits are usually expected to follow the rule that the more there are parameters to estimate in a model, the better it fits the data. Additionally, a quick plot of the data in supplementary table S12 (i.e. WAIC as a function of the number of parameters varying by food type in the model - i.e. 0 for M0, 2 for M1, 1 for M2 and 3 for M3) suggests that models M1 and potentially M2 may be also suitable: there is a break in the improvement of WAIC between model M0 and the three other models. I would thus suggest checking how the results reported in the main text differ when using models M1 and M2 instead of M3 (for the taste and health weights when comparing M3 with M1, for τS when comparing M3 with M2). If the differences are important, the results currently reported in the main text are not very reliable.

We thank the Reviewer for highlighting that it would be helpful for the paper to explicitly note that we specifically selected WAIC as one of two methods to assess model fit because it penalizes for model complexity. We now explicitly state that, in addition to being more robust than other metrics like AIC or BIC when comparing hierarchical Bayesian models like those in the current study, model fit metrics like WAIC penalize for model complexity based on the number of parameters (Watanabe, 2010). Therefore, it is not the case that more complex models (i.e., having additional parameters) would automatically have lower WAICs. Additionally, we note that our second method to assess model fit, posterior predictive checks demonstrate that only model M3 can reproduce key behavioral patterns present in the empirical data. As described in the Supplementary Materials, M1 and M2 miss those patterns in the data. In summary, we used best practices to assess model fit and reliability (Wilson & Collins, 2019): results from the WAIC comparison (which in fact penalizes models with more parameters) and results from posterior predictive checks align in showing that M3 best fit to our data. We have added a sentence to the manuscript to state this explicitly.

(2) The second main concern deals with the association reported between the DDM parameters and binge eating episodes (i.e. last paragraph of the results section, page 7). The authors claim that the DDM parameters "predict" binge eating episodes (in the Abstract among other places) while the binge eating frequency does not seem to have been collected prospectively. Besides this methodological issue, the interpretation of this association is exaggerated: during the task, BN patients did not make binge-related food choices in the negative emotional state. Therefore, it is impossible to draw clear conclusions about binge eating, as other explanations seem equally plausible. For example, the results the authors report with the DDM may be a marker of a strategy of the patients to cope with food tastiness in order to make restrictive-like food choices. A comparison of the authors' results with restrictive AN patients would be of interest. Moreover, correlating results of a nearly instantaneous behavior (i.e. a couple of minutes to perform the task with the 42 food choices) with an observation made over several months (i.e. binge eating frequency collected over three months) is questionable: the negative emotional state of patients varies across the day without systematically leading patients to engage in a binge eating episode in such states.

I would suggest in such an experiment to collect the binge craving elicited by each food and the overall binge craving of patients immediately before and after the task. Correlating the DDM results with these ratings would provide more compelling results. Without these data, I would suggest removing the last paragraph of the Results.

We thank the Reviewer for these interesting suggestions and appreciate the opportunity to clarify that we agree that claims about causal connections between our decision parameters and symptom severity metrics would be inappropriate. Per the Reviewer’s suggestions, we have eliminated the use of the word “predict” to describe the tested association with symptom metrics.  We also agree that more time-locked associations with craving ratings and near-instantaneous behavior would be useful, and we have added this as an important direction for future research in the discussion. However, associating task-based behavior with validated self-report measures that assess symptom severity over long periods of time that precede the task visit (e.g., over the past 2 weeks in depression, over the past month in eating disorders) is common practice in computational psychiatry, psychiatric neuroimaging, and clinical cognitive neuroscience (Hauser et al., 2022; Huys et al., 2021; Wise et al., 2023), and this approach has been used several times specifically with food choice tasks (Dalton et al., 2020; Steinglass et al., 2015). We have revised the language throughout the manuscript to clarify: the results suggest that individuals whose task behavior is more reactive to negative affect tend to be the most symptomatic, but the results do not allow us to determine whether this reactivity causes the symptoms.

In response to this Reviewer’s important point about negative affect not always producing loss-of-control eating in individuals with BN, we also now explicitly note that while several studies employing ecological momentary assessments (EMA) have repeatedly shown that increases in negative affect significantly increase the likelihood of subsequent loss-of-control eating (Alpers & Tuschen-Caffier, 2001; Berg et al., 2013; Haedt-Matt & Keel, 2011; Hilbert & Tuschen-Caffier, 2007; Smyth et al., 2007), not all loss-of-control eating occurs in the context of negative affect, and that future studies should integrate food choice task data pre and post-affect inductions with measures that capture the specific frequency of loss of control eating episodes that occur during states of high negative affect.

(3) My major improvement point is to tone down as much as possible any claim of a link with binge eating across the entire manuscript and to focus more on the restrictive behavior of BN patients in between binge eating episodes (see my second major concern about the methods). Additionally, since this article is a secondary research paper and since some of the authors have already used the task with AN patients, if possible I would run the same analyses with AN patients to test whether there are differences between AN (provided they were of the restrictive subtype) and BN.

We appreciate the Reviewer’s perspective and suggestions. We have adjusted our language linking loss-of-control eating frequency with decision parameters, and we have added additional sentences focusing on the implications for the restrictive behavior of patients with BN between binge eating episodes. In the Supplementary Materials. We have added an analysis of the restraint subscale of the EDE-Q and confirmed no relationship with parameters of interest. While we agree additional analyses with AN patients would be of interest, this is outside the scope of the paper. Our team have collected data from individuals with AN using this task, but not with any affect induction or measure of affect. Therefore, we have added this important direction for future research to the discussion.

Reviewer #2 (Public review):

Summary:

Binge eating is often preceded by heightened negative affect, but the specific processes underlying this link are not well understood. The purpose of this manuscript was to examine whether affect state (neutral or negative mood) impacts food choice decision-making processes that may increase the likelihood of binge eating in individuals with bulimia nervosa (BN). The researchers used a randomized crossover design in women with BN (n=25) and controls (n=21), in which participants underwent a negative or neutral mood induction prior to completing a food-choice task. The researchers found that despite no differences in food choices in the negative and neutral conditions, women with BN demonstrated a stronger bias toward considering the 'tastiness' before the 'healthiness' of the food after the negative mood induction.

Strengths:

The topic is important and clinically relevant and methods are sound. The use of computational modeling to understand nuances in decision-making processes and how that might relate to eating disorder symptom severity is a strength of the study.

Weaknesses:

The sample size was relatively small and may have been underpowered to find differences in outcomes (i.e., food choice behaviors). Participants were all women with BN, which limits the generalizability of findings to the larger population of individuals who engage in binge eating. It is likely that the negative affect manipulation was weak and may not have been potent enough to change behavior. Moreover, it is unclear how long the negative affect persisted during the actual task. It is possible that any increases in negative affect would have dissipated by the time participants were engaged in the decision-making task.

We thank the Reviewer for their comments on the strengths of the paper, and for highlighting these important considerations regarding the sample demographics and the negative affect induction. As in the original paper that focused only on ultimate food choice behaviors, we now specifically acknowledge that the study was only powered to detect small to medium group differences in the effect of negative emotion on these final choice behaviors. Regarding the sample demographics, we agree that the study’s inclusion of only female participants is a limitation.  Although the original decision for this sampling strategy was informed by data suggesting that bulimia nervosa is roughly six times more prevalent among females than males (Udo & Grilo, 2018), we now note in the discussion that our female-only sample limits the generalizability of the findings.

We also agree with the Reviewer’s noted limitations of the negative mood induction, and based on the reviewer’s suggestions, we have added to our original description of these limitations in the Discussion. Specifically, we now note that although the task was completed immediately after the affect induction, the study did not include intermittent mood assessments throughout the choice task, so it is unclear how long the negative affect persisted during the actual task.

Reviewer #3 (Public review):

Summary:

The study uses the food choice task, a well-established method in eating disorder research, particularly in anorexia nervosa. However, it introduces a novel analytical approach - the diffusion decision model - to deconstruct food choices and assess the influence of negative affect on how and when tastiness and healthiness are considered in decision-making among individuals with bulimia nervosa and healthy controls.

Strengths:

The introduction provides a comprehensive review of the literature, and the study design appears robust. It incorporates separate sessions for neutral and negative affect conditions and counterbalances tastiness and healthiness ratings. The statistical methods are rigorous, employing multiple testing corrections.

A key finding - that negative affect induction biases individuals with bulimia nervosa toward prioritizing tastiness over healthiness - offers an intriguing perspective on how negative affect may drive binge eating behaviors.

Weaknesses:

A notable limitation is the absence of a sample size calculation, which, combined with the relatively small sample, may have contributed to null findings. Additionally, while the affect induction method is validated, it is less effective than alternatives such as image or film-based stimuli (Dana et al., 2020), potentially influencing the results.

We agree that the small sample size and specific affect induction method may have contributed to the null model-agnostic behavioral findings. Based on this Reviewer’s and Reviewer 2’s comments, we have added these factors to our original acknowledgements of limitations in the Discussion.

Another concern is the lack of clarity regarding which specific negative emotions were elicited. This is crucial, as research suggests that certain emotions, such as guilt, are more strongly linked to binge eating than others. Furthermore, recent studies indicate that negative affect can lead to both restriction and binge eating, depending on factors like negative urgency and craving (Leenaerts et al., 2023; Wonderlich et al., 2024). The study does not address this, though it could explain why, despite the observed bias toward tastiness, negative affect did not significantly impact food choices.

We thank the Reviewer for raising these important points and possibilities. In the supplementary materials, we have added an additional analysis of the specific POMS subscales that comprise the total negative affect calculation that was reported in the original paper (Gianini et al., 2019), and which we now report in the main text. Ultimately, we found that, across both groups, the negative affect induction increased responses related to anger, confusion, depression, and tension while reducing vigor.

We agree with the Reviewer that factors like negative urgency and cravings are relevant here. The study did not collect any measures of craving, and in response to Reviewer 1 and this Reviewer, we now note in the discussion that replication studies including momentary craving assessments will be important. While we don’t have any measurements of cravings, we did measure negative urgency. Despite these prior findings, the original paper (Gianini et al., 2019) did not find that negative urgency was related to restrictive food choices. We have now repeated those analyses, and we also were unable to find any meaningful patterns. Nonetheless, we have added an analysis of negative urgency scores and decision parameters to the supplementary materials.      

References

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Berg, K. C., Crosby, R. D., Cao, L., Peterson, C. B., Engel, S. G., Mitchell, J. E., & Wonderlich, S. A. (2013). Facets of negative affect prior to and following binge-only, purge-only, and binge/purge events in women with bulimia nervosa. Journal of Abnormal Psychology, 122(1), 111–118. https://doi.org/10.1037/a0029703

Dalton, B., Foerde, K., Bartholdy, S., McClelland, J., Kekic, M., Grycuk, L., Campbell, I. C., Schmidt, U., & Steinglass, J. E. (2020). The effect of repetitive transcranial magnetic stimulation on food choice-related self-control in patients with severe, enduring anorexia nervosa. International Journal of Eating Disorders, 53(8), 1326–1336. https://doi.org/10.1002/eat.23267

Gianini, L., Foerde, K., Walsh, B. T., Riegel, M., Broft, A., & Steinglass, J. E. (2019). Negative affect, dietary restriction, and food choice in bulimia nervosa. Eating Behaviors, 33, 49–54. https://doi.org/10.1016/j.eatbeh.2019.03.003

Haedt-Matt, A. A., & Keel, P. K. (2011). Revisiting the affect regulation model of binge eating: A meta-analysis of studies using ecological momentary assessment. Psychological Bulletin, 137(4), 660–681. https://doi.org/10.1037/a0023660

Hauser, T. U., Skvortsova, V., Choudhury, M. D., & Koutsouleris, N. (2022). The promise of a model-based psychiatry: Building computational models of mental ill health. The Lancet Digital Health, 4(11), e816–e828. https://doi.org/10.1016/S2589-7500(22)00152-2

Hilbert, A., & Tuschen-Caffier, B. (2007). Maintenance of binge eating through negative mood: A naturalistic comparison of binge eating disorder and bulimia nervosa. International Journal of Eating Disorders, 40(6), 521–530. https://doi.org/10.1002/eat.20401

Huys, Q. J. M., Browning, M., Paulus, M. P., & Frank, M. J. (2021). Advances in the computational understanding of mental illness. Neuropsychopharmacology, 46(1), 3–19. https://doi.org/10.1038/s41386-020-0746-4

Maier, S. U., Raja Beharelle, A., Polanía, R., Ruff, C. C., & Hare, T. A. (2020). Dissociable mechanisms govern when and how strongly reward attributes affect decisions. Nature Human Behaviour, 4(9), Article 9. https://doi.org/10.1038/s41562-020-0893-y

Ratcliff, R., & Childers, R. (2015). Individual differences and fitting methods for the two-choice diffusion model of decision making. Decision, 2(4), 237–279. https://doi.org/10.1037/dec0000030

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eLife Assessment

This study dissects the function of 3 outputs of a specific population of modulatory neurons, dorsal raphe dopamine neurons, in social and affective behavior. It provides valuable information that both confirms prior results and provides new insights. The strength of the evidence is convincing, based on cutting-edge approaches and analysis. This study will be of interest to behavioral and systems neuroscientists, especially those interested in social and emotional behavior.

Reviewer #1 (Public review):

Summary:

The authors had previously found that brief social isolation could increase the activity of these neurons, and that manipulation of these neurons could alter social behavior in a social rank-dependent fashion. This manuscript explored which of the outputs were responsible for this, identifying the central nucleus of the amygdala as the key output region. The authors identified some discrete behavior changes associated with these outputs, and found that during photostimulation of these outputs, neuronal activity appeared altered in 'social response' neurons.

Strengths:

Rigorous analysis of the anatomy. Careful examination of the heterogenous effects on cell activity due to stimulation, linking the physiology with the behavior via photostimulation during recording in vivo.

Weaknesses:

(1) There are some clear imbalances in the sample size across the different regions parsed. The CeA has a larger sample size, likely in part to the previous work suggesting differential effects depending on social rank/dominance. Given the potential variance, it may be hard to draw conclusions about the impact of stimulation across different social ranks for other groups.

(2) It is somewhat unclear why only the 'social object ratio' was used to assess the effects versus more direct measurements of social behavior.

(3) Somewhat related, while it is statistically significant, it is unclear if the change seen in face investigation of biologically significant, on average, it looks like a few-seconds difference and that was not modulated by social rank.

(4) There are several papers studying these neurons that have explored behaviors examined here, as well as the physiological connectivity that are not cited that would provide important context for this work. In particular, multiple groups have found a dopamine-mediated IPSP in the BNST, in contrast to this work. There are technical differences that may drive these differences, but not addressing them is a major weakness.

(5) The inclusion of some markers for receptors for some of these outputs is interesting, and the authors suggest that this may be important, but this is somewhat disconnected from the rest of the work performed.

Reviewer #2 (Public review):

Summary:

The authors perform a series of studies to follow up on their previous work, which established a role for dorsal raphe dopamine neurons (DRN) in the regulation of social-isolation-induced rebound in mice. In the present study, Lee et. al, use a combination of modern circuit tools to investigate putatively distinct roles of DRN dopamine transporting containing (DAT) projections to the bed nucleus of the stria terminalis (BNST), central amygdala (CeA), and posterior basolateral amygdala (BLP). Notably, they reveal that optogenetic stimulation of distinct pathways confers specific behavioral states, with DRNDAT-BLP driving aversion, DRNDAT-BNST regulating non-social exploratory behavior, and DRNDAT-CeA promoting social ability. A combination of electrophysiological studies and in situ hybridization studies reveal heterogenous dopamine and neuropeptide expression and different firing properties, providing further evidence of pathway-specific neural properties. Lastly, the authors combine optogenetics and calcium imaging to resolve social encoding properties in the DRNDAT-CeA pathway, which correlates observed social behavior to socially engaged neural ensembles.

Collectively, these studies provide an interesting way of dissecting out separable features of a complex multifaceted social-emotional state that accompanies social isolation and the perception of 'loneliness.' The main conclusions of the paper provide an important and interesting set of findings that increase our understanding of these distinct DRN projections and their role in a range of social (e.g., prosocial, dominance), non-social, and emotional behaviors. However, as noted below, the examination of these circuits within a homeostatic framework is limited given that a number of the datasets did not include an isolated condition. The DRNDAT-CeA pathway was investigated with respect to social homeostatic states in the present study for some of the datasets.

Strengths:

(1) The authors perform a comprehensive and elegant dissection of the anatomical, behavioral, molecular, and physiological properties of distinct DRN projections relevant to social, non-social, and emotional behavior, to address multifaceted and complex features of social state.

(2) This work builds on prior findings of isolation-induced changes in DRN neurons and provides a working framework for broader circuit elements that can be addressed across the social homeostatic state.

(3) This work characterizes a broader circuit implicated in social isolation and provides a number of downstream targets to explore, setting a nice foundation for future investigation.

(4) The studies account for social rank and anxiety-like behavior in several of the datasets, which are an important consideration to the interpretation of social motivation states, especially in male mice with respect to dominance behavior.

Weaknesses:

(1) The conceptual framework of the study is based on the premise of social isolation and perceived 'loneliness' under the framework of social homeostasis, analogous to hunger. In this framework, social isolation should provoke an aversive state and compensatory social contact behavior. In the authors' prior work, they demonstrate synaptic changes in DRN neurons and social rebound following acute social isolation. Thus, the prediction would be that downstream projections also would show state-dependent changes as a function of social housing conditions (e.g., grouped vs. isolated). In the current paper, a social isolation condition was not included for the majority of the studies conducted (e.g., Figures 1-6 do not include an isolated condition, Figures 7-8 do include an isolated condition). Thus, while Figure 1-6 adds a very interesting and compelling set of data that is of high value to the social behavior field with respect to social and emotional processing and general circuit characterization, these studies do not directly investigate the impacts of dynamic social homeostatic state. The main claim of the paper, including the title (e.g., separable DRN projections mediate facets of loneliness-like state), abstract, intro, and discussion presents the claim of this work under the framework of dynamic social homeostatic states, which should be interpreted with caution, as the majority of the work in the paper did not include a social isolation comparison.

(2) In Figure 1, the authors confirm co-laterals in the BNST and CeA via anatomical tracing studies. The goal of the optogenetic studies is to dissociate the functional/behavioral roles of distinct projections. However, one limitation of optogenetic projection targeting is the possibility of back-propagating action potentials (stimulation of terminals in one region may back-propagate to activate cell bodies, and then afferent projections to other regions), and/or stimulation of fibers of passage. Therefore, one limitation in the dataset for the optogenetic stimulation studies is the possibility of non-specific unintended activation of projections other than those intended (e.g., DRNDAT-CeA). This can be dealt with by administering lidocaine to prevent back-propagating action potentials.

(3) It is unclear from the test, but in the subjects' section of the methods, it appears that only male animals were included in the study, with no mention of female subjects. It should be clear to the reader that this was conducted in males only if that is the case, with consideration or discussion, about female subjects and sex as a biological variable.

(4) Averaged data are generally reported throughout the study in the form of bar graphs, across most figures. Individual data points would increase the transparency of the data.

Reviewer #3 (Public review):

Summary:

The authors investigated the role of dopaminergic neurons (dopamine transporter expressing, DAT) in the dorsal raphe nucleus (DRN) in regulating social and affective behavior through projections to the central nucleus of the amygdala (CeA), bed nucleus of the stria terminalis (BNST), and the posterior subdivision of the basolateral amygdala. The largest effect observed was in the DRN-DAT projections to the CeA. Augmenting previously published results from this group (Matthews et al., 2016), the comprehensive behavioral analysis relative to social dominance, gene expression analysis, electrophysiological profiling, and in vivo imaging provides novel insights into how DRN-DAT projections to the CeA influence the engagement of social behavior in the contexts of group-housed and socially isolated mice.

Strengths:

Correlational analysis with social dominance is a nice addition to the study. The overall computational analyses performed are well-designed and rigorous.

Weaknesses:

(1) Analysis of dopamine receptor expression did not include Drd3, Drd4, or Drd5 which may provide more insights into how dopamine modulates downstream targets. This is particularly relevant to the BNST projection in which the densest innervation did not robustly co-localize with the expression of either Drd1 or Drd2. It is also possible that dopamine release from DRN-DAT neurons in any or all of these structures modulates neurotransmitter release from inputs to these regions that contain D2 receptors on their terminals.

(2) Although not the focus of this study, without pharmacological blockade of dopamine receptors, it is not possible to assess what the contribution of dopamine is to the behavioral outcomes. Given the co-release of glutamate and GABA from these neurons, it is possible that dopamine plays only a marginal role in the functional connectivity of DRN-DAT neurons. (

(3) Photostimulation parameters used during the behavioral studies (8 pulses of light delivered at 30 Hz for several minutes) could lead to confounding results limiting data interpretation. As shown in Figure 6J, 8 pulses of light delivered at 30 Hz result in a significant attenuation of the EPSC amplitude in the BLP and CeA projection. Thus, prolonged stimulation could lead to significant synaptic rundown resulting in an overall suppression of connectivity in the later stages of the behavioral analyses.

eLife Assessment

This study thoroughly assesses tactile acuity on women's breasts, for which no dependable data currently exists. The study provides two important contributions, by convincingly showing that tactile acuity on the breast is poor in comparison to other body parts, and that acuity is worst in larger breasts, indicating that the number of tactile sensors is fixed. However, further arguments concerning the role of the nipple in spatial localisation are not well supported by the current evidence. This study will be of interest to the broader community of touch, as well as those interested in breast reconstruction and sexual function.

Reviewer #1 (Public review):

The authors investigated tactile spatial perception on the breast through discrimination, categorization, and direct localization tasks. They reach three main conclusions:

(1) The breast has poor tactile spatial resolution.<br /> This conclusion is based on comparing just noticeable differences, a marker of tactile spatial resolution, across four body regions, two on the breast. The data compellingly support the conclusion; the study outshines other studies on tactile spatial resolution that tend to use problematic measures of tactile resolution such as two-point-discrimination thresholds. The result will interest researchers in the field and possibly in other fields due to the intriguing tension between the finding and the sexually arousing function of touching the breast.

(2) Larger breasts are associated with lower tactile spatial resolution<br /> This conclusion is based on a strong correlation between participants' JNDs and the size of their breasts. The correlation convincingly supports the conclusion. It is of interest to the field, as it aligns with the hypothesis that nerve fibers are more sparsely distributed across larger body parts.

(3) The nipple is a landmark: perceptually a unit and an attractor for tactile percepts<br /> The data do not support these conclusions. The conclusion that the nipple is perceived as a unit is based on poor performance in tactile categorization for touches on the nipple. This categorization performance may simply mirror the breast's low tactile spatial resolution with JNDs about the size of a nipple.

The conclusion that tactile percepts are drawn towards the nipple is based on tactile localization biases towards the nipple for tactile stimuli on the breast compared to localization biases for tactile stimuli on the back. Currently, the statistical analysis of the data does not match the field, psychophysics, standards. Moreover, any bias towards the nipple could simply be another instance of regression to the mean of the stimulus distribution, given that the tested locations were centered on the nipple. This confound can only be experimentally solved by shifting the distribution of the tested locations. Finally, given that participants indicated the locations on a 3D model of the body part, further experimentation would be required to determine whether there is a perceptual bias towards the nipple or whether the authors merely find a response bias.

Further comments:

- Given that later analyses require regression models, the authors might consider using them throughout.

- The stability of the JND differences between body parts across subjects is already captured in the analysis of the JNDs; the ANOVA and the post-hoc testing would not be significant if the order were not relatively stable across participants. Thus, it is unclear why this is being evaluated again with reduced power due to improper statistics.

- The null hypothesis of an ANOVA is that at least one of the mean values is different from the others; adding participants as a factor does not provide evidence for similarity.

- The pairwise correlations between body parts seem to be exploratory in nature. Like all exploratory analyses, the question arises of how much potential extra insights outweigh the risk of false positives. It would be hard to generate data with significant differences between several conditions and not find any correlations between pairs of conditions. Thus, the a priori chance of finding a significant correlation is much higher than what a correction accounts for.

- If the JND at mid breast (measured with locations centered at the nipple) is roughly the same size as the nipple, it is not surprising that participants have difficulty with the categorical localization task on the nipple but perform better than chance on the significantly larger areola.

- To justify the conclusion that the nipple is a unit, additional data would be required. 1) One could compare psychometric curves with the nipple as the center and psychometric curves with a nearby point on the areola as the center. 2) Performance in the quadrant task could be compared for the nipple and an equally sized portion of the areola. Otherwise, the task "only" provides confirmatory evidence for a low tactile resolution in the midbreast area.

- A localization bias toward the nipple in this context does not show that the nipple is the anchor of the breast's tactile coordinate system. The result might simply be an instance of regression to the mean of the stimulus distribution (also known as experimental prior). To convincingly show localization biases towards the nipple, the tested locations should be centered at another location on the breast.

- Another problem is the visual salience of the nipple, even though Blender models were uniformly grey. With this type of direct localization, it is very difficult to distinguish perceptual from response biases even if the regression to the mean problem is solved. There are two solutions to this problem: 1) Varying the uncertainty of the tactile spatial information, for example, by using a pen that exerts lighter pressure. A perceptual bias should be stronger for more uncertain sensory information; a response bias should be the same across conditions. 2) Measure bias with a 2IFC procedure by taking advantage of the fact that sensory information is noisier if the test is presented before the standard.

- Neither signed nor absolute localization error can be compared to the results of the previous experiments. The JND should be roughly proportional to the variance of the errors.

- The statistically adequate way of testing the biases is a hierarchical regression model (LMM) with a distance of the physical location from the nipple as a predictor, and a distance of the reported location from the nipple as a dependent variable. Either variable can be unsigned or signed for greater power, for example, coding the lateral breast as negative and the medial breast as positive. The bias will show in regression coefficients smaller than 1.

- It does not matter whether distances are calculated based on skin or 3D coordinates, as Euclidean distances or based on polar coordinates. However, there should only be one consistent distance in the text across both independent and dependent variables. Calculating various versions of these measures can create issues in Frequentist Statistics. For transparency, it is good practice to report the results of other methods for calculating the distance in the supplement.

- The body part could be added as a predictor to the LMM, with differences in bias between the body parts showing a significant interaction between the two predictors. The figures suggest such an effect. However, the interpretation should take into account that 1) response biases are more likely to arise at the breast and 2) it might be harder to learn the range of locations on the back given that stimulation is not restricted to an anatomically defined region as it is the case for the breast.

Reviewer #2 (Public review):

The authors tested tactile acuity on the breast of females using several tasks and reported overall low acuity compared to the back, which is typically considered to have the worst acuity of all body parts. Moreover, there was evidence that acuity is worse the larger the breast; this finding mirrors similar findings for the hand and therefore suggests that the number of tactile sensors is fixed and must be distributed across a larger extent of skin when a body part is larger, thus resulting in comparably lower tactile acuity.

Strengths:

I find this an interesting paper with results that are relevant to the tactile community. The authors apply several tasks allowing them to link the paper with previous results. The methodology and psychophysical analysis are sound.

Weaknesses:

The analysis of localization error direction, with the result that the nipple area may be a landmark for tactile localization, is interesting and aligns the paper with some other recent papers that have suggested that such landmarks should exist. However, there are major issues with methodology and statistics, so that currently the conclusions are not supported.

In the following, line numbers refer to the re-formatted manuscript provided by the authors upon request and are mentioned for them to find the relevant passages faster.

(1) Comments on analysis of tactile acuity:

- I had a hard time understanding some parts of the report. What is meant by "broadly no relationship" in line 137?

- It is suggested that spatial expansion (which is correlated with body part size) is related between medial breast and hand - is this to say that women with large hands have large medial breast size? Nipple size was measured, but hand size was not measured, is this correct?

- It is furthermore unclear how the authors differentiate medial breast and NAC. The sentence in lines 140-141 seems to imply the two terms are considered the same, as a conclusion about NAC is drawn from a result about the medial breast. This requires clarification.

- Finally, given that the authors suspect that overall localization ability (or attention) may be overshadowed by a size effect, would not an analysis be adequate that integrates both, e.g. a regression with multiple predictors?

(2) Comments on analysis of "The nipple is a unit":

- Statistics in this section are not adequately described and may be partly false.

- In the paragraph about testing quadrants of the nipple, it is stated that only 3 of 10 participants barely outperformed chance with a p < 0.01. It is unclear how a significant t-test is an indication of "barely above chance".

- The final part of the paragraph on nipple quadrants (starting line 176) explains that there was a trend (4 of 10 participants) for lower tactile acuity being related to the inability to differentiate quadrants. It seems to me that such a result would not be expected: The stated hypothesis is that all participants have the same number of tactile sensors in their nipple and areola, independent of NAC size. In this section, participants determine the quadrant of a single touch. Theoretically, all participants should be equally able to perform this task, because they all have the same number of receptors in each quadrant of nipple and areola. Thus, the result in Figure 2C is curious.

(3) Comments on analysis of "Absolute localization on the breast is anchored to the nipple"

- Again, there are things that are unclear with the statistics and description of the analysis.

- This section reports an Anova (line 193/194) with a factor "participant". This doesn't appear sensible. Please clarify. The factor distance is also unclear; is this a categorical or a continuous variable? Line 400 implies a 6-level factor, but Anovas and their factors, respectively, are not described in methods (nor are any of the other statistical approaches).

- The analysis on imprecision using mean pairwise error (line 199) is unclear: does pairwise refer to x/y or to touch vs. center of the nipple?

- p8, upper text, what is meant by "relative over-representation of the depth axis"? Does this refer to the breast having depth but the equivalent area on the back not having depth? What are the horizontal planes (probably meant to be singular?) - do you simply mean that depth was ignored for the calculation of errors? This seems to be implied in Figure 3AB.

- Lines 232-241, I cannot follow the conclusions drawn here. First, it is not clear to a reader what the aim of the presented analyses is: what are you looking for when you analyze the vectors? Second, "vector strength" should be briefly explained in the main text. Third, it is not clear how the final conclusion is drawn. If there is a bias of all locations towards the nipple, then a point closer to the nipple cannot exhibit a large bias, because the nipple is close-by. Therefore, one would expect that points close to the nipple exhibit smaller errors, but this would not imply higher acuity - just less space for localizing anything. The higher acuity conclusion is at odds with the remaining results, isn't it: acuity is low on the outer breast, but even lower at the NAC, so why would it be high in between the two?

(4) Comments on the Discussion:

The discussion makes some concrete suggestions for sensors in implants (line 283). It is not clear how the stated numbers were computed. Also, why should 4 sensors nipple quadrants receive individual sensors if the result here was that participants cannot distinguish these quadrants?

Additional comments:

I would find it interesting to know whether participants with small breast measurement delta had breast acuity comparable to the back. Alternatively, it would be interesting to know whether breast and back acuity are comparable in men. Such a result would imply that the torso has uniform acuity overall, but any spatial extension of the breast is unaccounted for. The lowest single participant data points in Figure 1B appear similar, which might support this idea.

eLife Assessment

This study proposes a valuable and interpretable approach for predicting hematoma expansion in patients with spontaneous intracerebral hemorrhage from non-contrast computed tomography. The predictive performance of the proposed method is solid through external validation using two datasets. The work will be of interest to medical biologists working on stroke and neuroimaging.

Reviewer #1 (Public review):

Summary:

The study explores the use of Transport-based morphometry (TBM) to predict hematoma expansion and growth 24 hours post-event, leveraging Non-Contrast Computed Tomography (NCCT) scans combined with clinical and location-based information. The research holds significant clinical potential, as it could enable early intervention for patients at high risk of hematoma expansion, thereby improving outcomes. The study is well-structured, with detailed methodological descriptions and a clear presentation of results. However, the practical utility of the predictive tool requires further validation, as the current findings are based on retrospective data. Additionally, the impact of this tool on clinical decision-making and patient outcomes needs to be further investigated.

Strengths

(1) Clinical Relevance: The study addresses a critical need in clinical practice by providing a tool that could enhance diagnostic accuracy and guide early interventions, potentially improving patient outcomes.

(2) Feature Visualization: The visualization and interpretation of features associated with hematoma expansion risk are highly valuable for clinicians, aiding in the understanding of model-derived insights and facilitating clinical application.

(3) Methodological Rigor: The study provides a thorough description of methods, results, and discussions, ensuring transparency and reproducibility.

Weaknesses:

(1) The limited sample size in this study raises concerns about potential model overfitting. While the reported AUCROC of 0.71 may be acceptable for clinical use, the robustness of the model could be further enhanced by employing techniques such as k-fold cross-validation. This approach, which aggregates predictive results across multiple folds, mimics the consensus of diagnoses from multiple clinicians and could improve the model's reliability for clinical application. Additionally, in clinical practice, the utility of the model may depend on specific conditions, such as achieving high specificity to identify patients at risk of hematoma expansion, thereby enabling timely interventions. Consequently, while AUC is a commonly used metric, it may not fully capture the model's clinical applicability. The authors should consider discussing alternative performance metrics, such as specificity and sensitivity, which are more aligned with clinical needs. Furthermore, evaluating the model's performance in real-world clinical scenarios would provide valuable insights into its practical utility and potential impact on patient outcomes.

(2) The authors compared the performance of TBM with clinical and location-based information, as well as other machine learning methods. While this comparison highlights the relative strengths of TBM, the study would benefit from providing concrete evidence on how this tool could enhance clinicians' ability to assess hematoma expansion in practice. For instance, it remains unclear whether integrating the model's output with a clinician's own assessment would lead to improved diagnostic accuracy or decision-making. Investigating this aspect-such as through studies evaluating the combined performance of clinician judgment and model predictions-could significantly enhance the tool's practical value.

Reviewer #2 (Public review):

Summary:

The author presents a transport-based morphometry (TBM) approach for the discovery of non-contrast computed tomography (NCCT) markers of hematoma expansion risk in spontaneous intracerebral hemorrhage (ICH) patients. The findings demonstrate that TBM can quantify hematoma morphological features and outperforms existing clinical scoring systems in predicting 24-hour hematoma expansion. In addition, the inversion model can visualize features, which makes it interpretable. In conclusion, this research has clinical potential for ICH risk stratification, improving the precision of early interventions.

Strengths:

TBM quantifies hematoma morphological changes using the Wasserstein distance, which has a well-defined physical meaning. It identifies features that are difficult to detect through conventional visual inspection (such as peripheral density distribution and density heterogeneity), which provides evidence supporting the "avalanche effect" hypothesis in hematoma expansion pathophysiology.

Weaknesses:

(1) As a methodology-focused study, the description of the methods section somewhat lacks depth and focus, which may make it challenging for readers to fully grasp the overall structure and workflow of the approach. For instance, the manuscript lacks a systematic overview of the entire process, from NCCT image input to the final prediction output. A potential improvement would be to include a workflow figure at the beginning of the manuscript, summarizing the proposed method and subsequent analytical procedures. This would help readers better understand the mechanism of the model.

(2) The description of the comparison algorithms could be more detailed. Since TBM directly utilizes NCCT images as input for prediction, while SVM and K-means are not inherently designed to process raw imaging data, it would be beneficial to clarify which specific features or input data were used for these comparison models. This would better highlight the effectiveness and advantages of the TBM method.

(3) The relatively small training and testing dataset may limit the model's performance and generalizability. Notably, while the study mentions that 1,066 patients from the ERICH dataset met the inclusion criteria, only 170 were randomly selected for the test set. Leveraging the full 1,066 ERICH cases for model training and internal validation might potentially enhance the model's robustness and performance.

(4) Some minor textual issues need to be checked and corrected, such as line 16 in the abstract "Incorporating these traits into a v achieved an AUROC of 0.71 ...".

(5) Some figures need to be reformatted (e.g., the x-axis in Figure 2 a is blocked).

eLife Assessment

This study provides fundamental insights into the regulation of a retained intron in the mRNA coding for OGT, a process known to be regulated by the O-GlcNAc cycling system, and highlights the functional role of the splicing regulator SFSWAP. The evidence supporting the claims of the authors is convincing; the authors performed an elegant state-of-the-art CRISPR knockout strategy and sophisticated bioinformatic analysis to identify SFSWAP as a negative regulator of alternative splicing. The work will be of interest to researchers in the fields of splicing and glycobiology.

Reviewer #1 (Public review):

Summary:

Govindan and Conrad use a genome-wide CRISPR screen to identify genes regulating retention of intron 4 in OGT, leveraging an intron retention reporter system previously described (PMID: 35895270). Their OGT intron 4 reporter reliably responds to O-GlcNAc levels, mirroring the endogenous splicing event. Through a genome-wide CRISPR knockout library, they uncover a range of splicing-related genes, including multiple core spliceosome components, acting as negative regulators of OGT intron 4 retention. They choose to follow up on SFSWAP, a largely understudied splicing regulator shown to undergo rapid phosphorylation in response to O-GlcNAc level changes (PMID: 32329777). RNA-sequencing reveals that SFSWAP depletion not only promotes OGT intron 4 splicing but also broadly induces exon inclusion and intron splicing, affecting decoy exon usage. While this study offers interesting insights into intron retention regulation and O-GlcNAc signaling, the RNA-Sequencing experiments lack essential controls needed to provide full confidence to the authors' conclusions.

Strengths:

(1) This study presents an elegant genetic screening approach to identify regulators of intron retention, uncovering core spliceosome genes as unexpected positive regulators of intron retention.<br /> (2) The work proposes a novel functional role for SFSWAP in splicing regulation, suggesting that it acts as a negative regulator of splicing and cassette exon inclusion, which contrasts with expected SR-related protein functions.<br /> (3) The authors suggest an intriguing model where SFSWAP, along with other spliceosome proteins, promotes intron retention by associating with decoy exons.

Weaknesses:

(1) The conclusions regarding SFSWAP's impact on alternative splicing rely on cells treated with a single pool of two siRNAs for five days. The absence of independent siRNA treatments raises concerns about potential off-target effects, which may reduce confidence in the observed SFSWAP-dependent splicing changes. Rescue experiments or using additional independent siRNA treatments would strengthen the conclusions.<br /> (2) The mechanistic role of SFSWAP in splicing would benefit from further exploration, though this may be more appropriate for future studies.

Comments on revisions:

The authors have addressed all my previous recommendations.

Reviewer #2 (Public review):

Summary:

The paper describes an effort to identify the factors responsible for intron retention and alternate exon splicing in a complex system known to be regulated by the O-GlcNAc cycling system. The CRISPR/Cas9 system was used to identify potential factors. The bioinformatic analysis is sophisticated and compelling. The conclusions are of general interest and advance the field significantly.

Strengths:

- Exhaustive analysis of potential splicing factors in an unbiased screen.<br /> - Extensive genome wide bioinformatic analysis.<br /> - Thoughtful discussion and literature survey

Weaknesses:

- No firm evidence linking SFSWA to an O-GlcNAc specific mechanism.<br /> - Resulting model leaves many unanswered questions.

Comments on revisions:

I think the authors have adequately dealt with the overall reviewer's comments.

Reviewer #3 (Public review):

Summary:

The major novel finding in this study is that SFSWAP, a splicing factor containing an RS domain but no canonical RNA binding domain, functions as a negative regulator of splicing. More specifically, it promotes retention of specific introns in a wide variety of transcripts including transcripts from the OGT gene previously studied by the Conrad lab. The balance between OGT intron retention and OGT complete splicing is an important regulator of O-GlcNAc expression levels in cells.

Strengths:

An elegant CRISPR knockout screen employed a GFP reporter, in which GFP is efficiently expressed only when the OGT retained intron is removed (so that the transcript will be exported from the nucleus to allow for translation of GFP). Factors whose CRISPR knockdown cause decreased intron retention therefore increase GFP, and these can be identified by sequencing RNA of GFP-sorted cells. SFSWAP was thus convincingly identified as a negative regulator of OGT retained intron splicing. More focused studies of OGT intron retention indicate that it may function by regulating a decoy exon previously identified in the intron, and that this may extend to other transcripts with decoy exons.

Weaknesses:<br /> The mechanism by which SFSWAP represses retained introns is unclear, although some data suggests it can operate (in OGT) at the level of a recently reported decoy exon within that intron. Interesting / appropriate speculation about possible mechanism are provided and will likely be the subject of future studies.

Overall the study is well done and carefully described.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

Govindan and Conrad use a genome-wide CRISPR screen to identify genes regulating retention of intron 4 in OGT, leveraging an intron retention reporter system previously described (PMID: 35895270). Their OGT intron 4 reporter reliably responds to O-GlcNAc levels, mirroring the endogenous splicing event. Through a genome-wide CRISPR knockout library, they uncover a range of splicing-related genes, including multiple core spliceosome components, acting as negative regulators of OGT intron 4 retention. They choose to follow up on SFSWAP, a largely understudied splicing regulator shown to undergo rapid phosphorylation in response to O-GlcNAc level changes (PMID: 32329777). RNA-sequencing reveals that SFSWAP depletion not only promotes OGT intron 4 splicing but also broadly induces exon inclusion and intron splicing, affecting decoy exon usage. While this study offers interesting insights into intron retention and O-GlcNAc signaling regulation, the RNA sequencing experiments lack the essential controls needed to provide full confidence to the authors' conclusions. 

Strengths: 

(1) This study presents an elegant genetic screening approach to identify regulators of intron retention, uncovering core spliceosome genes as unexpected positive regulators of intron retention. 

(2) The work proposes a novel functional role for SFSWAP in splicing regulation, suggesting that it acts as a negative regulator of splicing and cassette exon inclusion, which contrasts with expected SR-related protein functions. 

(3) The authors suggest an intriguing model where SFSWAP, along with other spliceosome proteins, promotes intron retention by associating with decoy exons. 

We thank the reviewer for recognizing and detailing the strengths of our manuscript. 

Weaknesses: 

(1) The conclusions on SFSWAP impact on alternative splicing are based on cells treated with two pooled siRNAs for five days. This extended incubation time without independent siRNA treatments raises concerns about off-target effects and indirect effects from secondary gene expression changes, potentially limiting confidence in direct SFSWAP-dependent splicing regulation. Rescue experiments and shorter siRNA-treatment incubation times could address these issues. 

We repeated our SFSWAP knockdown analysis and analyzed both OGT e4-e5 junction splicing and SFSWAP transcript levels by RT-qPCR (now included in Sup. Fig. S4) from day 2 to day 5 post siRNA treatment. We observed that the time point at which OGT intron 4 removal increases (day 2) coincides with the time at which SFSWAP transcript levels start decrease, consistent with a direct effect of SFSWAP knockdown on OGT intron 4 splicing. Moreover, the effect of SFSWAP knockdown on OGT intron 4 splicing peaks between day 4-5, supporting our use of these longer time points to cast a wide net for SFSWAP targets.

(2) The mechanistic role of SFSWAP in splicing would benefit from further exploration. Key questions remain, such as whether SFSWAP directly binds RNA, specifically the introns and exons (including the decoy exons) it appears to regulate. Furthermore, given that SFSWAP phosphorylation is influenced by changes in O-GlcNAc signaling, it would be interesting to investigate this relationship further. While generating specific phosphomutants may not yield definitive insights due to redundancy and also beyond the scope of the study, the authors could examine whether distinct SFSWAP domains, such as the SR and SURP domains, which likely overlap with phosphorylation sites, are necessary for regulating OGT intron 4 splicing. 

We absolutely agree with the reviewer that the current work stops short of a detailed mechanistic study, and we have made every attempt to be circumspect in our interpretations to reflect that limitation. In addition, we are very interested in delving more deeply into the mechanistic aspects of this regulation. In fact, we have initiated many of the experiments suggested by the reviewer (and more), but in each case, rigorous interpretable results will require a minimum another year’s time. 

For example, we have used crosslinking and biotin labeling techniques (using previously available reagents from Eclipsebio) to test whether SFSWAP binds RNA. The results were negative, but the lack of strong SFSWAP antibodies required that we use a transiently expressed myc-tagged SFSWAP. Therefore, this negative result could be an artifact of the exogenous expression and/or tagging. Given the difficulties of “proving the negative”, considerably more work will be required to substantiate this finding. As another example, we intend to develop a complementation assay as suggested. For an essential gene, the ideal complementation system employs a degron system, and we have spent months attempting to generate a homozygous AID-tagged SFSWAP. Unfortunately, we so far have only found heterozygotes. Of course, this could be because the tag interferes with function, the insert was not efficiently incorporated by homologous repair, or that we simply haven’t yet screened a sufficient number of clones. We’re confident that these technical issues that can be addressed, but they will take a significant amount of time to resolve. While we would ideally define a mechanism, we think that the data reported here outlining functions for SFSWAP in splicing represent a body of work sufficient for publication. 

(3) Data presentation could be improved (specific suggestions are included in the recommendations section). Furthermore, Excel tables with gene expression and splicing analysis results should be provided as supplementary datasheets. Finally, a more detailed explanation of statistical analyses is necessary in certain sections. 

We have addressed all specific suggestions as detailed in the recommendations below.

Reviewer #2 (Public review): 

Summary: 

The paper describes an effort to identify the factors responsible for intron retention and alternate exon splicing in a complex system known to be regulated by the O-GlcNAc cycling system. The CRISPR/Cas9 system was used to identify potential factors. The bioinformatic analysis is sophisticated and compelling. The conclusions are of general interest and advance the field significantly. 

Strengths: 

(1) Exhaustive analysis of potential splicing factors in an unbiased screen. 

(2) Extensive genome wide bioinformatic analysis. 

(3) Thoughtful discussion and literature survey. 

We thank the reviewer for recognizing and detailing the strengths of our manuscript. 

Weaknesses: 

(1) No firm evidence linking SFSWAP to an O-GlcNAc specific mechanism. 

We couldn’t agree more with this critique. Indeed, our intention at the outset for the screen was to find an O-GlcNAc sensor linking OGT splicing with O-GlcNAc levels. As often occurs with high-throughput screens, we didn’t find exactly what we were looking for, but the screen nonetheless pointed us to interesting biology. Prompted by our screen, we describe new insights into the function of SFSWAP a relatively uncharacterized essential gene. Currently, we are testing other candidates from our screen, and we are performing additional studies to identify potential O-GlcNAc sensors.  

(2) Resulting model leaves many unanswered questions. 

We agree (see Reviewer 1, point 2 response).  

Reviewer #3 (Public review): 

Summary: 

The major novel finding in this study is that SFSWAP, a splicing factor containing an RS domain but no canonical RNA binding domain, functions as a negative regulator of splicing. More specifically, it promotes retention of specific introns in a wide variety of transcripts including transcripts from the OGT gene previously studied by the Conrad lab. The balance between OGT intron retention and OGT complete splicing is an important regulator of O-GlcNAc expression levels in cells. 

Strengths: 

An elegant CRISPR knockout screen employed a GFP reporter, in which GFP is efficiently expressed only when the OGT retained intron is removed (so that the transcript will be exported from the nucleus to allow for translation of GFP). Factors whose CRISPR knockdown causes decreased intron retention therefore increase GFP, and can be identified by sequencing RNA of GFP-sorted cells. SFSWAP was thus convincingly identified as a negative regulator of OGT retained intron splicing. More focused studies of OGT intron retention indicate that it may function by regulating a decoy exon previously identified in the intron, and that this may extend to other transcripts with decoy exons. 

We thank the reviewer for recognizing the strengths of our manuscript. 

Weaknesses: 

The mechanism by which SFSWAP represses retained introns is unclear, although some data suggests it can operate (in OGT) at the level of a recently reported decoy exon within that intron.

Interesting/appropriate speculation about possible mechanisms are provided and will likely be the subject of future studies. 

We completely agree that this is a limitation of the current study (see above). Now that we have a better understanding of SFSWAP functions, we will continue to explore SFSWAP mechanisms as suggested. 

Overall the study is well done and carefully described but some figures and some experiments should be described in more detail. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) Clarify and add missing statistical details across the figures. For example, Figure S2 lacks statistical comparisons, and in Figures 4A and 4C the tests applied should be specified in the legend. 

We have added appropriate statistical analysis wherever missing and edited figure legends to specify the tests used.

(2) The authors are strongly encouraged to provide detailed tables of gene expression and alternative splicing analyses from RNA-Seq experiments (e.g., edgeR, rMATS, Whippet, and MAJIQ), as this would enhance transparency and facilitate data interpretation. 

We have added tables for gene expression and alternate splicing analysis as suggested (Suppl. tables 3-

6).

(3) Although the legend sometimes indicates differently (e.g., Figure 3b, 5a, 5c, etc), the volcano plots showing the splicing changes do not contain a cutoff for marginally differential percent spliced in or intron retention values. 

The legends have been edited to reflect the correct statistical and/or PSI cutoffs.

(4) For consistency, use a consistent volcano plot format across all relevant figures (Figures 3b, 5a-c, S3, S4, S7, and S8), including cutoffs for differential splicing and the total count of up- and down-regulated events. 

Due to different statistical frameworks and calculations employed by different alternate splicing pipelines, we could not use the same cutoffs for different pipelines.  However, we have now indicated the number of up- and down-regulated events for consistency among the volcano plots.

(5) What is the overlap of differentially regulated events between the different analytical methodologies applied? 

We analyzed the degree of overlap between the three pipelines used in the paper using a Venn diagram (added to Suppl. Fig. S7). However, as widely reported in literature (e.g., Olofsson et al., 2023; Biochem Biophys Res Commun. 2023; doi: 10.1016/j.bbrc.2023.02.053.), the degree of overlap between pipelines is quite low.

(6) To further substantiate your conclusions, additional validations of RNA-Seq splicing data, ideally visualized on an agarose gel, would be valuable, especially for exons and introns regulated by SFSWAP, and particularly for OGT decoy exons in Figure 4c. 

We have not included these experiments as we focused on other critiques for this resubmission. Because the RNA-seq, RT-PCR and RT-qPCR data all align, we are confident that the products we are seeing are correctly identified and orthogonally validated (Figs 2d, 4a, 4b, and 4c).  

(7) It would be more informative if the CRISPR screen data were presented in a format where both the adjusted p-value and LFC values of the hits are presented. Perhaps a volcano plot? 

We have now included these graphs in revised Supplementary Figure S2. 

(8) In Figure 2d, a cartoon showing primer binding sites for each panel could aid interpretation, particularly in explaining the unexpected simultaneous increase in OGT mRNA and intron retention upon SFSWAP knockdown. 

We have added a cartoon showing primer binding sites similar to that shown in Fig. 4a.

(9) Page 9, line 1, states that SFSWAP autoregulates its expression by controlling intron retention. Including a Sashimi plot would provide visual support for this claim. 

The data suggesting that SFSWAP autoregulates its own transcript abundance were reported in Zachar et al. (1994), not from our own studies. Validation of those data with our RNA-seq data is confounded by the fact that we are using siRNAs to knockdown the SFSWAP RNA at the transcript level (Fig. S15). 

(10) In the legend of Figure S2 the authors state that negative results are inconclusive because RNA knockdowns are not verified by western blotting or qRT-PCR. This is correct, but the reviewer would also argue that the positive results are also inconclusive as they are not supported by a rescue experiment to confirm that the effect is not due to off-target effects. 

This is a fair point with respect to the siRNA experiments on their own. However, the CRISPR screen was performed with sgRNAs, and MAGeCK RRA scores are high only for those genes that have multiple sgRNAs that up-regulate the gene. Examination of the SFSWAP sgRNAs individually shows that three of four SFSWAP sgRNAs had false discovery rates ≤10^-42 for GFP upregulation. Thus, the siRNAs provide an additional orthogonal approach. It seems unlikely that the siRNAs, and three independent sgRNAs will have the same off-target results. Thus, these combined observations support the conclusion that SFSWAP loss leads to decreased OGT intron retention.  

(11) For clarity in Figure 3a, consider using differential % spliced in or intron retention bar plots with directionality (positive and negative axis) and labeling siSFSWAP as the primary condition. 

(12) Consider presenting Figure 5D as a box plot with a Wilcoxon test for statistical comparison. 

For both points 11 and 12, we have tried the graphs as the reviewer suggested. While these were good suggestions, in both cases we felt that the original plots ended up presenting a clearer presentation of the data (see Author response image 1).

Author response image 1.

(13) Please expand the Methods section to detail the Whippet and MAJIQ analyses. 

We have expanded the methods section to include additional details of the alternate splicing analysis.

(14) Include coordinates for the four possible OGT decoy exon combinations analyzed in the Methods section. 

We have added the coordinates of all four decoy forms in the methods section.  

(15) A section on SFSWAP mass spectrometry is listed in Methods but is missing from the manuscript. 

This section has now been removed.

Reviewer #2 (Recommendations for the authors): 

This is an excellent contribution. The paper describes an effort to identify the factors responsible for intron retention and alternate exon splicing in a complex system known to be regulated by the O-GlcNAc cycling system. The CRISPR/Cas9 system was used to identify potential factors. The bioinformatic analysis is sophisticated and compelling. The conclusions are of general interest and advance the field significantly. 

Some specific recommendations. 

(1) The plots in Figure 3 describing SI and ES events are confusing to this reader. Perhaps the violin plot is not the best way to visualize these events. The same holds true for the histograms in the lower panel of Figure 3. Not sure what to make of these plots. 

For Figure 3b, we include both scatter and violin plots to represent the same data in two distinct ways. For Figure 3d, we agree that these are not the simplest plots to understand, and we have spent significant time trying to come up with a better way of displaying these trends in GC content as they relate to SE and RI events. Unfortunately, we were unable to identify a clearer way to present these data. 

(2) The model (Figure 6) is very useful but confusing. The legend and the Figure itself are somewhat inconsistent. The bottom line of the figure is apparent but I fear that the authors are trying to convey a more complete model than is apparent from this figure. Please revise. 

We have simplified the figure from the previous submission. As mentioned above, we admit that mechanistic details remain unknown. However, we have tried to generate a model that reflects our data, adds some speculative elements to be tested in the future, but remains as simple as possible. We are not quite sure what the reviewer was referring to as “somewhat inconsistent”, but we have attempted to clarify the model in the revised Discussion and Figure legend.  

(3) It is unclear how normalization of the RNA seq experiments was performed (eg. Figure S5 and 6).  

The normalization differences in Fig. S5 and S6 (now Fig S8 and S9) were due to scaling differences during the use of rmats2sashimiplot software. We have now replaced Fig. S5 to reflect correctly scaled images.

I am enthusiastic about the manuscript and feel that with some clarification it will be an important contribution. 

Thank you for these positive comments about our study!

Reviewer #3 (Recommendations for the authors): 

(1) In Figure 1f, it is clear that siRNA-mediated knockdown of OGT greatly increases spliced RNA as the cells attempt to compensate by more efficient intron removal (three left lanes). However, there is no discussion of the various treatments with TG or OSMI. Might quantitation of these lanes not also show the desired effects of TG and OSMI on spliced transcript levels? 

The strong effect of OGT knockdown masks the (comparatively modest) effects of subsequent inhibitor treatments on the reporter RNA. We have edited the results section to clarify this.

(2) In Figure 2c, why is the size difference between spliced RNA and intron-retained RNA so different in the GFP-probed gel (right) compared with the OGT-probed gel (left)? Even recognizing that the GFP probe is directed against reporter transcripts, and the OGT probe (I think) is directed against endogenous OGT transcripts, shouldn't the difference between spliced and unspliced bands be the same, i.e., +/- the intron 4 sequence. Also, why does the GFP probe detect the unspliced transcript so poorly? 

The fully spliced endogenous OGT mRNA is ~5.5 kb while the fully spliced reporter is only ~1.6kb, so the difference in size (the apparent shift relative to the mRNA) is quite different. Moreover, the two panels in Fig 2c are not precisely scaled to one another, so direct comparisons cannot be made. 

The intron retained isoform does not accumulate to high levels in this reporter, a phenotype that we also observed with our GFP reporter designed to probe the regulation of the MAT2A retained intron (Scarborough et al., 2021). We are not certain about the reason for these observations, but suspect that the reporter RNA’s retained intron isoforms are less stable in the nucleus than their endogenous counterparts. Alternatively, the lack of splicing may affect 3´ processing of the transcripts so that they do not accumulate to the high levels observed for the wild-type genes. 

(3) Please provide more information about the RNA-seq experiments. How many replicates were performed under each of the various conditions? The methods section says three replicates were performed for the UPF1/TG experiments; was this also true for the SFSWAP experiments?  

All RNA-seq experiments were performed in biological triplicates. We have edited the methods section to clarify this.

(4) Relatedly, the several IGV screenshots shown in Figure 3C presumably represent the triplicate RNA seq experiments. In part D, how many experiments does the data represent? Is it a compilation of three experiments? 

Fig. 3d is derived from alternate splicing analysis performed on three biological replicates. We have added the number of replicates (n=3) on the figure to clarify this. We have also noted that the three IGV tracks represent biological replicates in the Figure legend for 3c.  

(5) Please provide more details regarding the qRT-PCR experiments. 

We have provided the positions of primer sets used for RT-qPCR analysis and cartoon depictions of target sites below the data wherever appropriate.

(6) In the discussion of decoy exon function (in the Discussion section), several relevant observations are cited to support a model in which decoy exons promote assembly of splicing factors. One might also cite the finding that eCLIP profiling has found enriched binding of U2AF1 and U2AF2 at the 5' splice site region of decoy exons (reference 16). 

Excellent point. This has now been added to the Discussion. 

Minor corrections / clarifications: 

(1) In the Figure 2A legend, CRISPR is misspelled. 

Corrected.

(2) In the discussion, the phrase "indirectly inhibits splicing of exons 4 and 5, but promoting stable unproductive assembly of the spliceosome", the word "but" should probably be "by". 

Corrected.

eLife Assessment

The role of ACVR2A is potentially of importance to both the biology of trophoblast cells and to the pathogenesis of preeclampsia. In this manuscript, the authors have taken a useful first step towards better understanding this protein using a loss of function model in trophoblast cell lines and then examining invasion, proliferation, and transcription in these cells. The study is solid and further in vivo evidence on how target factors participate in the occurrence of placental structural disorders and diseases through potential downstream pathways will be invaluable in the future.

Reviewer #1 (Public review):

Summary:

This study has preliminarily revealed the role of ACVR2A in trophoblast cell function, including its effects on migration, invasion, proliferation, and clonal formation, as well as its downstream signaling pathways.

Strengths:

The use of multiple experimental techniques, such as CRISPR/Cas9-mediated gene knockout, RNA-seq, and functional assays (e.g., Transwell, colony formation, and scratch assays), is commendable and demonstrates the authors' effort to elucidate the molecular mechanisms underlying ACVR2A's regulation of trophoblast function. The RNA-seq analysis and subsequent GSEA findings offer valuable insights into the pathways affected by ACVR2A knockout, particularly the Wnt and TCF7/c-JUN signaling pathways.

Weaknesses:

The current findings provide valuable insights into the role of ACVR2A in trophoblast cell function and its involvement in the regulation of migration, invasion, and proliferation, further validation in both in vitro and in vivo models would strengthen the conclusions. Additional techniques, such as animal models and more advanced clinical sample analyses, would help strengthen the conclusions and provide a more comprehensive understanding of the molecular pathways involved.

Reviewer #2 (Public review):

Summary:

ACVR2A is one of a handful of genes for which significant correlations between associated SNPs and the incidences of preeclampsia have been found in multiple populations. It is one of the TGFB family receptors, and multiple ligands of ACVR2A, as well as its coreceptors and related inhibitors, have been implicated in placental development, trophoblast invasion, and embryo implantation. This useful study builds on this knowledge by showing that ACVR2A knockout in trophoblast-related cell lines reduces trophoblast invasion, which could tie together many of these observations. The implication of cross-talk between the WNT and ACRV2A/SMAD2 pathways is an important contribution to the understanding of the regulation of trophoblast function.

Strengths:

(1) ACVR2A is one of very few genes implicated in preeclampsia in multiple human populations, yet its role in pathogenesis is not very well studied and this study begins to address that hole in our knowledge.

(2) ACVR2A is also indirectly implicated in trophoblast invasion and trophoblast development via its connections to many ligands, inhibitors, and coreceptors, suggesting its potential importance.

(3) The authors have used multiple cell lines to verify their most important observations.

Editors' note: Following the first round of peer review, the original reviewers were not available to review the revised manuscript. As several specific weakness detailed by the reviewers were largely addressed in the revised manuscript, they are not included here.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study has preliminarily revealed the role of ACVR2A in trophoblast cell function, including its effects on migration, invasion, proliferation, and clonal formation, as well as its downstream signaling pathways.

Strengths:

The use of multiple experimental techniques, such as CRISPR/Cas9-mediated gene knockout, RNA-seq, and functional assays (e.g., Transwell, colony formation, and scratch assays), is commendable and demonstrates the authors' effort to elucidate the molecular mechanisms underlying ACVR2A's regulation of trophoblast function. The RNA-seq analysis and subsequent GSEA findings offer valuable insights into the pathways affected by ACVR2A knockout, particularly the Wnt and TCF7/c-JUN signaling pathways.

Weaknesses:

The molecular mechanisms underlying this study require further exploration through additional experiments. While the current findings provide valuable insights into the role of ACVR2A in trophoblast cell function and its involvement in the regulation of migration, invasion, and proliferation, further validation in both in vitro and in vivo models is needed. Additionally, more experiments are required to establish the functional relevance of the TCF7/c-JUN pathway and its clinical significance, particularly in relation to pre-eclampsia. Additional techniques, such as animal models and more advanced clinical sample analyses, would help strengthen the conclusions and provide a more comprehensive understanding of the molecular pathways involved.

Reviewer #2 (Public review):

Summary:

ACVR2A is one of a handful of genes for which significant correlations between associated SNPs and the incidences of preeclampsia have been found in multiple populations. It is one of the TGFB family receptors, and multiple ligands of ACVR2A, as well as its coreceptors and related inhibitors, have been implicated in placental development, trophoblast invasion, and embryo implantation. This useful study builds on this knowledge by showing that ACVR2A knockout in trophoblast-related cell lines reduces trophoblast invasion, which could tie together many of these observations. Support for this finding is incomplete, as reduced proliferation may be influencing the invasion results. The implication of cross-talk between the WNT and ACRV2A/SMAD2 pathways is an important contribution to the understanding of the regulation of trophoblast function.

Strengths:

(1) ACVR2A is one of very few genes implicated in preeclampsia in multiple human populations, yet its role in pathogenesis is not very well studied and this study begins to address that hole in our knowledge.

(2) ACVR2A is also indirectly implicated in trophoblast invasion and trophoblast development via its connections to many ligands, inhibitors, and coreceptors, suggesting its potential importance.

(3) The authors have used multiple cell lines to verify their most important observations.

Weaknesses:

(1) There are a number of claims made in the introduction without attribution. For example, there are no citations for the claims that family history is a significant risk factor for PE, that inadequate trophoblast invasion of spiral arteries is a key factor, and that immune responses, and reninangiotensin activity are involved.

Thank you for pointing out the lack of citations in some parts of the introduction. We have revised the manuscript to include appropriate references for the claims regarding family history as a risk factor for PE, the role of inadequate trophoblast invasion in spiral arteries, and the involvement of immune responses and the renin-angiotensin system. The revised text now includes citations to well-established studies in the field (Salonen Ros et al., 2000; Chappell LC et al., 2021; Brosens et al., 2002; Knofler et al., 2019; Redman CWG et al., 1999; LaMarca B et al., 2008). We believe these additions improve the scientific rigor of the manuscript.

(2) The introduction states "As a receptor for activin A, ACVR2A..." It's important to acknowledge that ACVR2A is also the receptor for other TGFB family members, with varying affinities and coreceptors. Several TGFB family members are known to regulate trophoblast differentiation and invasion. For example, BMP2 likely stimulates trophoblast invasion at least in part via ACVR2A (PMID 29846546).

Thank you for highlighting the broader role of ACVR2A as a receptor for multiple members of the TGF-β superfamily. We have revised the introduction to acknowledge that ACVR2A is not only the receptor for activin A but also interacts with other ligands, such as BMP2, which likely stimulates trophoblast invasion via ACVR2A (PMID: 29846546). This addition provides a more comprehensive view of ACVR2A's function in trophoblast biology. While the focus of our current study is on activin A, we agree that ACVR2A's role in mediating the effects of other TGF-β family members is an important topic for future research.

(3) An alternative hypothesis for the potential role of ACVR2A in preeclampsia is its functions in the endometrium. In the mouse ACVR2A knockout in the uterus (and other progesterone receptorexpressing cells) leads to embryo implantation failure.

Thank you for bringing up the potential role of ACVR2A in the endometrium as an alternative hypothesis. We have revised the discussion to acknowledge this possibility and cited relevant studies showing that uterine-specific knockout of ACVR2A in mice leads to embryo implantation failure (Monsivais et al., 2021). This suggests that ACVR2A may play a critical role in uterine receptivity and embryo implantation, which could influence placental development and preeclampsia pathogenesis. While our current study focuses on trophoblast-related functions of ACVR2A, we agree that investigating its role in the uterine environment is an important direction for future research.

(4) In the description of the patient population for placental sample collections, preeclampsia is defined only by hypertension, and this is described as being in accordance with ACOG guidelines. ACOG requires a finding of hypertension in combination with either proteinuria or one of the following: thrombocytopenia, elevated creatinine, elevated liver enzymes, pulmonary, edema, and new onset unresponsive headache.

We appreciate the reviewer’s detailed observation regarding the definition of preeclampsia.

We have reviewed and clarified our description of the diagnostic criteria based on the American College of Obstetricians and Gynecologists (ACOG) guidelines. Specifically, we have revised the definition in the Materials and Methods section under "Collection of Placenta and Decidua Specimens," as follows: In accordance with the guidelines from the American College of Obstetricians and Gynecologists (ACOG, 2023), preeclampsia (PE) is diagnosed as hypertension (systolic blood pressure ≥140 mmHg or diastolic blood pressure ≥90 mmHg on at least two occasions) in combination with one or more of the following: proteinuria (≥300 mg/24-hour urine collection or protein/creatinine ratio ≥0.3), thrombocytopenia, elevated serum creatinine, elevated liver enzymes, pulmonary edema, or new-onset headache unresponsive to treatment.

(5) I believe that Figures 1a and 1b are data from a previously published RNAseq dataset, though it is not entirely clear in the text. The methods section does not include a description of the analysis of these data undertaken here. It would be helpful to include at least a brief description of the study these data are taken from - how many samples, how were the PE/control groups defined, gestational age range, where is it from, etc. For the heatmap presented in B, what is the significance of the other genes/ why are they being shown? If the purpose of these two panels is to show differential expression specifically of ACVR2A in this dataset, that could be shown more directly.

Clarification of RNAseq dataset: The Methods section has been revised to specify the dataset source (GEO accession number: GSE114691), which includes 20 PE and 21 control placental samples with gestational ages ranging from 34 to 38 weeks. PE and control groups were defined using clinical criteria such as hypertension and proteinuria, and these details have also been added to the Results section. RNAseq analysis description: We have included details of the differential gene expression analysis in the Methods section. Specifically, the DESeq2 R package was used, with thresholds of FDR < 0.05 and |log2(fold change) | ≥ 1. The selection of WNT pathwayrelated genes in Figure 1B is based on these analyses. Significance of the heatmap genes: The genes displayed in Figure 1B were selected based on their significant differential expression and enrichment in pathways relevant to PE pathogenesis, such as the WNT signaling pathway. We have clarified this in the Results section and updated the figure legend to explain their biological relevance. Purpose of Figures 1A and 1B: Figure 1A emphasizes the downregulation of ACVR2A in PE placentas, while Figure 1B complements this by presenting differentially expressed genes associated with the WNT pathway. These figures collectively highlight the role of ACVR2A in PE and its connection to broader molecular pathways. Text descriptions have been updated to improve clarity and focus.

(6) More information is needed in the methods section to understand how the immunohistochemistry was quantified. "Quantitation was performed" is all that is provided. Was staining quantified across the whole image or only in anchoring villous areas? How were HRP & hematoxylin signals distinguished in ImageJ? How was the overall level of HRP/DAB development kept constant between the NC and PE groups?

Thank you for pointing out the need for more details regarding the quantification of immunohistochemistry (IHC). We have now clarified and expanded the description of the IHC quantification process in the Methods section as follows: Quantification Across the Entire Section: IHC staining was assessed across the entire tissue section to account for global expression patterns. For quantitative analysis, representative regions from the anchoring villous areas, where ACVR2A expression is most prominent, were selected for comparison between NC and PE groups. This ensured that the analysis focused on biologically relevant regions. ImageJ Analysis:

Images of stained sections were captured under identical magnifications and lighting conditions. Hematoxylin (blue, nuclear staining) and DAB/HRP (brown, protein-specific signal) were distinguished using ImageJ's color deconvolution plugin. The DAB/HRP signal was isolated and quantified based on the integrated optical density (IOD) within the selected regions. Consistency in HRP/DAB Development: To maintain consistency between NC and PE groups, all tissue samples were processed under identical experimental conditions, including the same antibody dilution, incubation times, and DAB/HRP development durations. Negative controls (without primary antibody) were included to monitor background staining, and the DAB reaction was stopped simultaneously across all samples to avoid overdevelopment. Statistical Analysis: The quantified DAB signal intensity was normalized to the area of the selected regions, and comparisons between NC and PE groups were performed using statistical tests (e.g., Student’s ttest). Results are reported as mean ± SD. We hope this additional detail addresses your concerns.

(7) In Figure 1E it is not immediately obvious to many readers where the EVT are. It is probably worth circling or putting an arrow to the little region of ACVR2A+ EVT that is shown in the higher magnification image in Figure 1E. These are actually easier to see in the pictures provided in the supplement Figure 1. Of note, the STB is also staining positive. This is worth pointing out in the results text.

Thank you for your suggestion regarding Figure 1E. To make the location of the ACVR2A+ extravillous trophoblasts (EVTs) more apparent, we have updated Figure 1E by adding arrows to indicate the regions of EVTs in the higher magnification image. Additionally, we have included annotations in the supplemental Figure S1 to further aid visualization. We appreciate your observation that syncytiotrophoblasts (STBs) also show positive staining for ACVR2A. We have revised the Results section to explicitly mention this finding and its potential significance.

(8) It is not possible to judge whether the IF images in 1F actually depict anchoring villi. The DAPI is really faint, and it's high magnification, so there isn't a lot of context. Would it be possible to include a lower magnification image that shows where these cells are located within a placental section? It is also somewhat surprising that this receptor is expressed in the cytoplasm rather than at the cell surface. How do the authors explain this?

Thank you for your suggestion to provide more context for the immunofluorescence (IF) images in Figure 1F. To address this, we have included lower magnification images in Supplementary Figure S2, showing the overall structure of the placental section and the location of the anchoring villi. These images help to contextualize the regions analyzed in Figure 1F, which were selected to clearly illustrate ACVR2A expression in extravillous trophoblasts (EVTs). In Figure 1F, we have focused on higher magnification images for better visualization of ACVR2A staining patterns in EVTs. Regarding the subcellular localization of ACVR2A, the receptor is predominantly expressed on the cell surface, as shown in our images. However, some intracellular staining is also observed, which may reflect receptor trafficking or recycling processes, consistent with the behavior of other activin receptors under physiological or pathological conditions. We have clarified these points in the Results and Discussion sections.

(9) The results text makes it sound like the data in Figure 2A are from NCBI & Protein atlas, but the legend says it is qPCR from this lab. The methods do not detail how these various cell lines were grown; only HTR-SVNeo cell culture is described. Similarly, JAR cells are used for several experiments and their culture is not described.

Thank you for pointing out the need for clarification regarding Figure 2A and cell culture methods. The data in Figure 2A were generated using RT-qPCR conducted in our laboratory, not solely based on data from NCBI or the Human Protein Atlas. We have revised the Results section to reflect this more accurately. Regarding the culture conditions, we acknowledge that the methods for other cell lines were not explicitly detailed. For this study, all cell lines, including JAR and other cancer cell lines, were cultured following standard protocols provided by the suppliers. Specifically, JAR cells and other cell lines were purchased from Wuhan Punosei Life Technology and were maintained in RPMI-1640 medium supplemented with 10% fetal bovine serum (FBS) and 1% penicillin/streptomycin under standard conditions (37°C, 5% CO₂). This information has been added to the Methods section for clarity.

(10) Under RT-qPCR methods, the phrase "cDNA reverse transcription cell RNA was isolated..." does not make any sense.

Thank you for pointing out the unclear phrasing in the RT-qPCR methods section. We agree that the original description was not precise. To address this, we have revised the relevant section to improve clarity and accuracy. Specifically, the methods now explicitly describe the two key steps: RNA isolation and cDNA synthesis. The revised text reads: Total RNA was isolated from cells using a Total RNA Extraction Kit (TIANGEN, China) following the manufacturer’s instructions. The extracted RNA was reverse-transcribed into complementary DNA (cDNA) using a cDNA Synthesis Kit (Takara, Japan) according to the protocol provided by the manufacturer.

(11) The paragraph beginning "Consequently, a potential association..." is quite confusing. It mentions analyzing ACVR2A expression in placentas, but then doesn't point to any results of this kind and repeats describing the results in Figure 2a, from various cell lines.

Thank you for your comment regarding the paragraph beginning with "Consequently, a potential association...". We understand that the current wording may create confusion. The primary aim of this section is to compare ACVR2A expression levels across various cell lines, including trophoblast-derived and non-trophoblast cell lines, to highlight the relevance of ACVR2A in trophoblast function, particularly in invasion and migration. To address your concerns, we have revised the paragraph for clarity and logical flow. The updated text explicitly focuses on the comparison of ACVR2A expression across cell lines (Figure 2A) and how this supports the hypothesis that ACVR2A plays a key role in trophoblast invasion and migration. Additionally, the discussion of placental samples has been separated to avoid confusion with cell line results. We hope this revision resolves the issue.

(12) The authors should acknowledge that the effect of the ACVR2A knockout on proliferation makes it difficult to draw any conclusions from the trophoblast invasion assays. That is, there might be fewer migrating or invading cells in the knockout lines because there are fewer cells, not because the cells that are there are less invasive. Since this is a central conclusion of the study, it is a major drawback.

Thank you for highlighting this important point. We agree that the reduced proliferation observed in ACVR2A knockout cells could influence the results of the invasion assays, as fewer cells may inherently lead to reduced invasion. To minimize this effect, we conducted the invasion and migration assays under low-serum conditions (1–2% serum) to limit cell proliferation during the experimental timeframe. This approach was based on optimization trials and existing literature, as serum-free conditions were found to negatively impact cell viability and experimental reproducibility. While these efforts helped to mitigate the impact of proliferation on the results, we acknowledge this as a limitation of our study and have added this discussion to the manuscript. Future studies could incorporate approaches such as normalizing cell numbers or using additional proliferation-independent methods to confirm the findings. We hope this clarification and the steps taken address your concerns.

(13) The legend and the methods section do not agree on how many fields were selected for counting in the transwell invasion assays in Figure 3C. The methods section and the graph do not match the number of replicate experiments in Figure 3D (the number of replicate experiments isn't described for 3C).

Thank you for pointing out the inconsistencies regarding the number of fields counted and the number of replicates in the Transwell invasion assays (Figure 3C) and colony formation assays (Figure 3D). We apologize for the lack of clarity in the Methods section and figure legend. To address this, we have revised both the figure legends and the Methods section for consistency and added detailed descriptions. For Figure 3C, cell invasion was quantified by randomly selecting 5 fields of view per sample under 300× magnification. Images shown in the figure were taken at lower magnification to provide a better visual comparison between experimental and control groups. For Figure 3D, each experiment was independently repeated at least 10 times to ensure robust and reproducible results. These clarifications have been incorporated into the revised manuscript. We appreciate your feedback and believe this revision improves the clarity and transparency of our methods.

(14) Discussion says "Transcriptome sequencing analysis revealed low ACVR2A expression in placental samples from PE patients, consistent with GWAS results across diverse populations." The authors should explain this briefly. Why would SNPs in ACVR2A necessarily affect levels of the transcript?

Thank you for raising this important point. We acknowledge that our study did not directly investigate how SNPs in the ACVR2A gene affect transcript levels. However, prior studies have suggested that SNPs can influence gene expression through various mechanisms. For example, SNPs in regulatory regions (e.g., promoters, enhancers, or untranslated regions) may affect transcription factor binding, RNA stability, or splicing efficiency, ultimately altering transcript levels. While we did not directly assess the functional consequences of ACVR2A SNPs in this study, the observed downregulation of ACVR2A in PE placentas aligns with the potential regulatory impact of SNPs previously identified in GWAS studies. To address this, we have revised the Discussion section to clarify the relationship between SNPs and transcript levels and acknowledge this limitation.  

(15) "The expression levels of ACVR2A mRNA were comparable to those of tumor cells such as A549. This discovery suggested a potential pivotal role of ACVR2A in the biological functions of trophoblast cells, especially in the nurturing layer." Alternatively, ACVR2A expression resembles that of tumors because the cell lines used here are tumor cells (JAR) or immortalized cells (HTR8). These lines are widely used to study trophoblast properties, but the discussion should at least acknowledge the possibility that the behavior of these cells does not always resemble normal trophoblasts.

Thank you for pointing out this important limitation. We agree that the JAR and HTR8/SVneo cell lines, being tumor-derived or immortalized, may not fully replicate the behavior of normal trophoblast cells. While these cell lines are widely used as models for studying trophoblast properties due to their ease of culture and invasive behavior, their gene expression and signaling pathways could partially reflect their tumorigenic or immortalized origins. We have revised the Discussion section to acknowledge this limitation and clarify the interpretation of ACVR2A expression levels in these cells.

(16) The authors should discuss some of what is known about the relationship between the TCF7/c-JUN pathway and the major signaling pathway activated by ACVR2A, Smad 2/3/4. The Wnt and TGFB family cross-talk is quite complex and it has been studied in other systems.

Thank you for highlighting the relationship between the TCF7/c-JUN pathway and Smad2/3/4 signaling. In our study, we chose to focus on Smad1/5 due to its strong association with ACVR2A in placental development, as demonstrated in a recent study（DOI: 10.1038/s41467-021-23571-5). This study showed that the BMP signaling pathway, mediated through ACVR2A-Smad1/5, is essential for endometrial receptivity and embryo implantation. While Smad2/3/4 are wellestablished mediators of TGF-β signaling, Smad1/5 activation is more directly linked to ACVR2A in the context of reproductive biology.

In PE placentas, we observed a significant downregulation of Smad1/5 expression, which supports the hypothesis that ACVR2A-mediated Smad signaling is disrupted in this condition. Although we did not directly assess Smad2/3/4 in this study, prior research has shown that Smad2/3 can interact with TCF/LEF transcription factors to regulate Wnt-related target genes, suggesting potential cross-talk between these pathways. We have now clarified this rationale and included a discussion of these interactions in the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Several points need to be addressed to improve the clarity and robustness of the presented findings:

(1) From a clinical perspective, several concerns arise regarding the interpretation of these findings. First, the small sample size of 20 patients may not be representative of the broader population, limiting the generalizability of the results. Additionally, although no significant differences in age and pre-pregnancy BMI were observed between the PE and normal control groups, other clinical variables, such as hypertension or gestational diabetes, may also influence ACVR2A expression and contribute to PE development. Furthermore, while the study suggests a correlation between reduced ACVR2A expression and PE, it remains unclear whether this association holds true across different subtypes of PE or whether there are other underlying clinical factors that could account for these changes in gene expression. These factors need to be considered in future studies to better understand the clinical relevance of ACVR2A in PE.

Thank you for raising these insightful concerns about the clinical interpretation of our findings. We agree that the small sample size of 20 patients may limit the generalizability of our results. To address this, we are actively expanding our cohort by collecting additional clinical samples from PE patients and normotensive controls. This effort aims to strengthen the robustness of our findings and provide stronger evidence for the role of ACVR2A in PE. We would also like to clarify that, during the initial sample collection, we specifically included only PE patients without comorbidities such as gestational diabetes, chronic hypertension, or other pregnancy-related complications. This strict selection criterion was implemented to minimize the potential influence of confounding clinical variables and ensure that our findings specifically reflect the association between ACVR2A expression and PE. While our study provides important initial insights, we recognize the need for larger-scale studies to validate these findings. The ongoing collection of clinical samples will allow us to address this limitation and enhance the translational relevance of our research. We have revised the manuscript to reflect these points and highlight our plans to strengthen the study by increasing the sample size.

(2) The section "Precision Genome Surgery: ACVR2A Knockout via CRISPR/Cas9" in the results contains some issues with expression details. The results section should be more structured, with data presented in a more detailed and clear manner, ensuring that there is a clear connection between each experimental step and its corresponding result. For example, the sentence "Following multiple rounds of monoclonal culture, genotype identification, RT-qPCR and Western blotting (WB) analysis for screening, specific double-knockout monoclonal cell lines were distinctly chosen" contains redundant phrasing and unnecessary details, which affect the flow of the text.

Thank you for your constructive feedback on the “Precision Genome Surgery: ACVR2A Knockout via CRISPR/Cas9” section. We agree that this section can be better structured to present the data in a more detailed and coherent manner. To address this, we have reorganized the results into distinct steps, ensuring a clear connection between each experimental step and its corresponding result. Redundant phrasing has been removed to improve the flow and readability of the text. The revised section emphasizes the purpose of each step, the screening process, and the specific results obtained.

(3) The figure legends and panel labels in Figure 3 should be revised to ensure clarity and consistency. The figure legend should specify the exact panels (e.g., Figure 3A, 3B, 3C, etc.) and clearly describe the experimental conditions and results shown in each part.

Thank you for pointing out the need for improved clarity and consistency in the figure legends and panel labels for Figure 3. We have revised the figure legend to specify each panel (e.g., Figure 3A, 3B, 3C, etc.) and included detailed descriptions of the experimental conditions and results displayed in each part. These updates aim to ensure better understanding and alignment between the figure legend and the panels.

(4) Lack of In Vivo Validation of ACVR2A Knockout: The study does not include in vivo experiments to validate the effects of ACVR2A knockout. It would be important to investigate whether similar regulatory effects of ACVR2A on trophoblast cell migration and invasion can be observed in animal models or in larger clinical studies. The lack of in vivo data raises questions about the translational relevance of the findings.

Thank you for highlighting the importance of in vivo validation to assess the translational relevance of our findings. While we acknowledge that in vivo experiments could provide additional insights into the role of ACVR2A in trophoblast migration and invasion, this study was primarily designed as an in vitro investigation to explore the molecular mechanisms underlying ACVR2A function in trophoblast cells. The choice of an in vitro model allowed us to perform precise and controlled mechanistic analyses, which are critical for establishing a foundation for future research. We agree that in vivo studies using animal models or larger clinical cohorts are important next steps to validate the regulatory effects of ACVR2A on trophoblast function and its contribution to PE pathogenesis. These directions will be pursued in future research to further establish the translational potential of our findings. We have included this perspective in the revised Discussion section.

(5) TCF7/c-JUN Pathway in Clinical Samples: In the study of the TCF7/c-JUN pathway, the authors mention assessing protein expression in clinical samples through immunohistochemistry (IHC). However, the manuscript does not provide a clear explanation of how the findings from laboratory cell models (such as HTR8/SVneo and JAR) relate to the clinical samples. Specifically, while ACVR2A knockout is shown to affect these proteins at the cellular level, it is unclear whether this effect is observed in clinical samples. Therefore, further validation of the TCF7/c-JUN pathway in the cell models and exploration of its relationship with protein expression in clinical samples is necessary. Additional experiments, such as immunofluorescence staining or mass spectrometry, could further confirm the role of the TCF7/c-JUN pathway in cells and provide a more direct comparison with clinical data.

Thank you for highlighting the need to connect findings from cell models to clinical samples, particularly with respect to the TCF7/c-JUN pathway. In response to your comment, we conducted additional experiments using Western blot analysis to evaluate the expression of ACVR2A, SMAD1/5, SMAD4, pSMAD1/5/9, and TCF7L1/TCF7L2 in PE placental tissues compared to normotensive controls (Figure 7A). The results demonstrated significantly reduced expression of these proteins in PE placentas, providing evidence that disruptions in the ACVR2A-SMAD and TCF7/c-JUN signaling pathways observed in vitro are also present in clinical samples.

These findings strengthen the translational relevance of our study by directly linking the molecular mechanisms identified in cell models to clinical observations. We have updated the Results and Discussion sections to incorporate these new data, and we believe this addition addresses your concern about the relationship between in vitro and clinical findings.

eLife Assessment

This important study highlights the key role of the gut-liver axis mediated by LPS in causing hepatic steatosis. The authors provide solid evidence, in vivo, in vitro, and in silico, for the role of acyloxyacyl hydrolase in mediating this effect using KO mice subjected to MASD-inducing diets. The findings are significant for the liver research community and others interested in the gut-liver axis.

Reviewer #1 (Public review):

Lu et. al. proposed here a direct role of LPS in inducing hepatic fat accumulation and that metabolism of LPS therefore can mitigate fatty liver injury. With an Acyloxyacyl hydrolase whole-body KO mice, they demonstrated that Acyloxyacyl hydrolase deletion resulted in higher hepatic fat accumulation over 7 months of high glucose/high fructose diet. Previous literature has found that hepatocyte TLR4 (which is a main receptor for binding LPS) KO reduced fatty liver in MAFLD model, and this paper complement this by showing that degradation/metabolism of LPS can also reduce fatty liver. Using clodronate-liposomes to deplete KC, the authors went on to show that AOAH level decreased significantly with increased SREBP1 level, suggesting that KCs were the major source of AOAH in the liver. To explain the mechanism of LPS induced lipogenesis, the authors demostrated in vitro that LPS alone without KC can induce SREBP1 level in primary hepatocytes via mTOR activation. This result proposed a very interesting mechanism, and the translational implications of utilizing Acyloxyacyl hydrolase to decrease LPS exposure is intriguing.

The strengths of the present study include that they raised a very simplistic mechanism with LPS that is of interest in many diseases. The phenotype shown in the study is strong. The mechanism proposed by the findings are generally well supported. Manuscript significantly improved with revision. Overall, this work adds to the current understanding of the gut-liver axis and development of MAFLD, and will be of interest to many readers.

Reviewer #2 (Public review):

The authors of this article investigated the impact of the host enzyme AOAH on the progression of MASLD in mice. To achieve this, they utilized whole-body Aoah-/- mice. The authors demonstrated that AOAH reduced LPS-induced lipid accumulation in the liver, probably by decreasing the expression and activation of SREBP1. In addition, AOAH reduced hepatic inflammation and minimized tissue damage.

The authors have effectively addressed some key questions I raised. However, I still have some lingering concerns regarding the mechanisms underlying AOAH's effects.

(1) AOAH is expressed in the intestine, where it may inactivate LPS before it enters systemic circulation. In Fig. 3F, fecal LPS is significantly higher in Aoah⁻/⁻ mice compared to Aoah⁺/⁺ mice, indicating that AOAH in the intestine reduces bioactive LPS levels at the source. This implies that differences in hepatic LPS levels are already influenced by the gut environment, raising doubts about how much Kupffer cells contribute to inactivating LPS in the liver.

(2) The reliance on Kupffer cell depletion with clodronate-liposomes may overestimate the role of Kupffer cells because clodronate does not exclusively target hepatic Kupffer cells. Clodronate liposomes are taken up by macrophages systemically, potentially depleting macrophages in other organs, including the intestine and circulation. This means observed effects could also be due to loss of AOAH activity in non-hepatic macrophages.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Lu et. al. proposed here a direct role of LPS in inducing hepatic fat accumulation and that the metabolism of LPS therefore can mitigate fatty liver injury. With an Acyloxyacyl hydrolase whole-body KO mice, they demonstrated that Acyloxyacyl hydrolase deletion resulted in higher hepatic fat accumulation over 8 months of high glucose/high fructose diet. Previous literature has found that hepatocyte TLR4 (which is a main receptor for binding LPS) KO reduced fatty liver in the MAFLD model, and this paper complements this by showing that degradation/metabolism of LPS can also reduce fatty liver. This result proposed a very interesting mechanism and the translational implications of utilizing Acyloxyacyl hydrolase to decrease LPS exposure are intriguing.

The strengths of the present study include that they raised a very simplistic mechanism with LPS that is of interest in many diseases. The phenotype shown in the study is strong. The mechanism proposed by the findings is generally well supported.

There are also several shortcomings in the findings of this study. As AOAH is a whole-body KO, the source production of AOAH in MAFLD is unclear. Although the authors used published single-cell RNA-seq data and flow-isolated liver cells, physiologically LPS degradation could occur in the blood or the liver. The authors linked LPS to hepatocyte fatty acid oxidation via SREBP1. The mechanism is not explored in great depth. Is this signaling TLR4? In this model, LPS could activate macrophages and mediate the worsening of hepatocyte fatty liver injury via the paracrine effect instead of directly signaling to hepatocytes, thus it is not clear that this is a strictly hepatocyte LPS effect. It would also be very interesting to see if administration of the AOAH enzyme orally could mitigate MAFLD injury. Overall, this work will add to the current understanding of the gut-liver axis and development of MAFLD and will be of interest to many readers.

We thank the reviewers for their important questions and comments.

In previous studies we found that AOAH is expressed in Kupffer cells and dendritic cells cells (Shao et al., 2007). Single-cell RNAseq analysis of mouse livers by others has found AOAH in Kupffer cells, monocytes, NK cells and ILC1 cells (Remmerie et al.,2020). We also analyzed human liver single-cell RNAseq data and found that AOAH is expressed in monocytes, macrophages, resident and circulating NK cells, and some T cells (Ramachandran et al., 2019) (Please see new Figure 3E). Using clodronate-liposomes to deplete Kupffer cells we found that hepatic AOAH mRNA diminished and nSREBP1 increased (Please see new Figure 5D). These results suggest that Kupffer cells are the major source of AOAH in the liver and that LPS needs to be inactivated in the liver to prevent hepatocyte lipid accumulation.

Using primary hepatocyte culture, we found that LPS can stimulate hepatocytes directly to induce mTOR activation and SREBP1 activation (new Figure 6E). Adding purified Kupffer cells to the hepatocyte culture did not further increase SREBP1 activation. These results suggest that LPS may directly stimulate hepatocyte to accumulate fat, at least in vitro.

Both TLR4 and caspase 11 are reported to play important roles in MASLD development (Sharifnia et al., 2015; Zhu et al., 2021). We have crossed Aoah^-/- mice with TLR4^-/- mice and found that Aoah^-/-TLR4^-/- and Aoah^-/- mice had similarly severe MASLD. This is probably because TLR4 is required for gut homeostasis (Rakoff-Nahoum et al., 2004); in TLR4 whole-body KO mice compromised gut homeostasis may result in more severe MASLD. By specifically deleting TLR4 on hepatocytes, Yu et al found that NASH-induced fibrosis was mitigated (Yu et al., 2021). In future studies we therefore would need to specifically delete TLR4 in hepatocytes to test whether excessive gut-derived LPS in Aoah^-/- mice stimulates hepatic TLR4 to induce more severe MASLD. We would also test whether Caspase 11 is required for hepatic fat accumulation in Aoah^-/- mice.

It is intriguing to test whether providing exogenous AOAH may mitigate MASLD. We will use an AAV expressing AOAH to test this idea.

Reviewer #2 (Public review):

The authors of this article investigated the impact of the host enzyme AOAH on the progression of MASLD in mice. To achieve this, they utilized whole-body Aoah^-/- mice. The authors demonstrated that AOAH reduced LPS-induced lipid accumulation in the liver, probably by decreasing the expression and activation of SREBP1. In addition, AOAH reduced hepatic inflammation and minimized tissue damage.

However, this paper is descriptive without a clear mechanistic study. Another major limitation is the use of whole-body KO mice so the cellular source of the enzyme remains undefined. Moreover, since LPS-mediated SREBP1 regulation or LPS-mediated MASLD progression is already documented, the role of AOAH in SREBP1-dependent lipid accumulation and MASLD progression is largely expected.

Specific comments:

(1) The overall human relevance of the current study remains unclear.

It is a good point. We have studied human relevance and show the results in Figure 3E. AOAH expression increased in the hepatic macrophages and monocytes of MASLD patients.

(2) Is AOAH secreted from macrophages or other immune cells? Are there any other functions of AOAH within the cells?

AOAH can be secreted from kidney proximal tubule cells and the released AOAH can be taken up by cells that do not express AOAH (Feulner et al., 2004). AOAH can also deacylate oxidized phospholipids, DAMP molecules (Zou et al., 2021).

(3) Due to using whole-body KO mice, the role of AOAH in specific cell types was unclear in this study, which is one of the major limitations of this study. The authors should at least conduct in vitro experiments using a co-culture system of hepatocytes and Kupffer cells (or other immune cells) isolated from WT or Aoah^-/- mice.

Thanks for the suggestion.

Using clodronate-liposomes, we depleted Kupffer cells and found that hepatic AOAH mRNA diminished and nSREBP1 increased in the liver (Please see new Figure 5D). These results confirm that Kupffer cells are the major source of AOAH in the liver and LPS needs to be inactivated in the liver to prevent hepatocyte lipid accumulation.  Using primary hepatocyte culture, we found that LPS can stimulate hepatocytes directly to induce mTOR activation and SREBP1 activation (new Figure 6E).  These results suggest that LPS may directly stimulate hepatocytes to accumulate fat, at least in vitro.

(4) It has been well-known that intestinal tight junction permeability is increased by LPS or inflammatory cytokines. However, in Figure 3E, intestinal permeability is comparable between the groups in both diet groups. The authors should discuss more about this result. In addition, intestinal junctional protein should be determined by Western blot and IHC (or IF) to further confirm this finding.

We have stained ZO-1 (Please see Author response image 1, ZO-1- green fluorescence) in Aoah^+/+ and Aoah^-/- mouse colonic sections. We did not see a big difference between the two strains of mice.

Author response image 1.

Feeding a high fat diet in our mouse facility for 28 weeks has led to increased gut permeability, but there was no difference between Aoah^+/+ and Aoah^-/-mice. Thus, the more severe MASLD in Aoah^-/- mice is mainly caused by elevated bioactive LPS instead of increased LPS translocation from the intestine to the liver.

(5) In Figure 6, the LPS i.g. Aoah^-/- group is missing. This group should be included to better interpret the results.

Please see new Figure 6. When we orally gavaged Aoah^-/- mice with LPS, fecal LPS levels did not increase further. Their liver SREBP1 did not increase further while the SREBP1 target gene expression increased when compared with Aoah^-/- mice i.g. PBS.

(6) The term NAFLD has been suggested to be changed to MASLD as the novel nomenclature according to the guidelines of AASLD and EASL.

Thanks for the suggestion. We have changed NAFLD to MASLD.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Consider using MAFLD rather than NAFLD.

Thanks for the suggestion. We have changed NAFLD to MASLD.

References

Feulner, J.A., M. Lu, J.M. Shelton, M. Zhang, J.A. Richardson, and R.S. Munford. 2004. Identification of acyloxyacyl hydrolase, a lipopolysaccharide-detoxifying enzyme, in the murine urinary tract. Infection and immunity 72:3171-3178.

Zou, B., M. Goodwin, D. Saleem, W. Jiang, J. Tang, Y. Chu, R.S. Munford, and M. Lu. 2021. A highly conserved host lipase deacylates oxidized phospholipids and ameliorates acute lung injury in mice. eLife 10:

eLife Assessment

This valuable work investigates the social interactions of mice living together in a system of multiple connected cages. It provides solid evidence for a statistical approach capturing changes in social interactions after manipulating prefrontal cortical plasticity. This research will be of broad interest to researchers studying animal social behavior.

Reviewer #3 (Public review):

Summary:

Chen et al. present a thorough statistical analysis of social interactions, more precisely, co-occupying the same chamber in the Eco-HAB measurement system. They also test the effect of manipulating the prelimbic cortex by using TIMP-1 that inhibits the MMP-9 matrix metalloproteinase. They conclude that altering neural plasticity in the prelimbic cortex does not eliminate social interactions, but it strongly impacts social information transmission.

Strengths:

The quantitative approach to analyzing social interactions is laudable and the study is interesting. It demonstrates that the Eco-HAB can be used for high throughput, standardized and automated tests of the effects of brain manipulations on social structure in large groups of mice.

Weaknesses:

A demonstration of TIMP-1 impairing neural plasticity specifically in the prelimbic cortex of the treated animals would greatly strengthen the biological conclusions. The Eco-HAB provides coarser spatial information compared to some other approaches, which may influence the conclusions.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

The authors have constructively responded to previous referee comments and I believe that the manuscript is a useful addition to the literature. I particularly appreciate the quantitative approach to social behavior, but have two cautionary comments.

(1) Conceptually it is important to further justify why this particular maximum entropy model is appropriate. Maximum entropy models have been applied across a dizzying array of biological systems, including genes, neurons, the immune system, as well as animal behavior, so would seem quite beneficial to explain the particular benefits here, for mouse social behavior as coarse-grained through the eco-hab chamber occupancy. This would be an excellent chance to amplify what the models can offer for biological understanding, particularly in the realm of social behavior

We thank the reviewer for this comment. Maximum entropy models, along with other statistical inference methods that learn interaction patterns from simultaneously-measured degrees of freedom, help distinguish various types of interactions, e.g. direct vs. indirect interactions among animals, individual preference to food vs. social interaction with pairs. As research on social behavior expands from focusing on pairs of animals to studying groups in (semi-)naturalistic environments, maximum entropy models serve as a crucial link between high-throughput data and the need to identify and distinguish interaction rules. Specifically, among all possible maximum entropy models, the pairwise maximum entropy model is one of the simplest that can describe interactions among individuals, which serves as an excellent starting point to understand collective and social behavior in animals.

Although the Eco-HAB setup currently records spatially coarse-grained data, it still provides more spatial information compared to the traditional three-chamber tests used to assess sociability for rodents. By showing that the maximum entropy model can effectively analyze Eco-HAB data, we hope to highlight its potential in research of social behavior in animals.

To amplify what the models can offer for biological understanding particularly in the realm of social behavior, We have updated the Introduction to add a more logical structure to the need of using maximum entropy models to identify interactions among mice. Additionally, we updated the first paragraph of the Discussion to make it specific that it is the use of maximum entropy models that identifies interaction patterns from the high-throughput data. Finally, we have also added in the Discussion (line 422-425) arguments supporting the specific use of pairwise maximum entropy models to study social behaviors.

(2) Maximum entropy models of even intermediate size systems involve a large number of parameters. The authors are transparent about that limitation here, but I still worry that the conclusion of the sufficiency of pairwise interactions is simply not general, and this may also relate to the differences from previous work. If, as the authors suggest in the discussion, this difference is one of a choice of variables, then that point could be emphasized. The suggestion of a follow up study with a smaller number of mice is excellent.

We thank the reviewer for raising the issue and agree that the caveat of how general pairwise interactions can describe social behavior of animals needs to be discussed. We have added a sentence in the Discussion to point out this important caveat. “More generally, this discrepancy when looking at different choices of variables raises the issue that when studying social behavior of animals in a group, it is important to test and compare interaction models with different complexity (e.g. pairwise or with higher-order interactions).” We have also toned down our conclusion to limit our results of pairwise interactions describing mice co-localization patterns to the data collected in Eco-HAB (also see Reviewer 3 Major Point 2).

Reviewer #3 (Public review):

Summary:

Chen et al. present a thorough statistical analysis of social interactions, more precisely, co-occupying the same chamber in the Eco-HAB measurement system. They also test the effect of manipulating the prelimbic cortex by using TIMP-1 that inhibits the MMP-9 matrix metalloproteinase. They conclude that altering neural plasticity in the prelimbic cortex does not eliminate social interactions, but it strongly impacts social information transmission.

Strengths:

The quantitative approach to analyzing social interactions is laudable and the study is interesting. It demonstrates that the Eco-HAB can be used for high throughput, standardized and automated tests of the effects of brain manipulations on social structure in large groups of mice.

Weaknesses:

A demonstration of TIMP-1 impairing neural plasticity specifically in the prelimbic cortex of the treated animals would greatly strengthen the biological conclusions. The Eco-HAB provides coarser spatial information compared to some other approaches, which may influence the conclusions.

Recommendations for the authors:  

Reviewer #3 (Recommendations for the authors):

Major points

(1) Do the Authors have evidence that TIMP-1 was effective, as well as specific to the prelimbic cortex?

We refer to the literature for the effectiveness and specificity of TIMP-1 to the prelimbic cortex.

Specifically, the study by Okulski et al. (Biol. Psychiatry 2007) provides clear evidence that TIMP1 plays a role in synaptic plasticity in the prefrontal cortex. They showed that TIMP-1 is induced in the medial prefrontal cortex (mPFC) following stimulation that triggers late long-term potentiation (LTP), a key model of synaptic plasticity. Overexpression of TIMP-1 in the mPFC blocked the activity of matrix metalloproteinases (MMPs) and prevented the induction of late LTP in vivo. Similar effects were observed with pharmacological inhibition of MMP-9 in vitro, reinforcing the idea that TIMP-1 regulates extracellular proteolysis as part of the plasticity mechanism in the prefrontal cortex. These findings confirm that TIMP-1 is both effective and active in this specific brain region.

Further evidence comes from Puścian et al. (Mol. Psychiatry 2022), who used TIMP-1-loaded nanoparticles to influence neuronal plasticity in the amygdala. They found that TIMP-1 affected MMP expression, LTP, and dendritic morphology, showing its impact on synaptic modifications. More directly relevant, Winiarski et al. (Sci. Adv. 2025) demonstrated that injecting TIMP-1-loaded nanoparticles into the prelimbic cortex altered responses to social stimuli, further supporting the idea that TIMP-1 has region-specific effects on behavioral processes.

We have also updated the main text (page 8, 1st paragraph of “Effect of impairing neuronal plasticity in the PL on subterritory preferences and sociability”) of the manuscript to include the above references.

(2) The Authors seem to suggest that one main reason for the different results compared to Shemesh et al. 2013 was the coarseness of the Eco-HAB data. In this case, I think this conclusion should be toned down because of this significant caveat.

We thank the reviewer for pointing this out, and agree that this caveat and difference should be emphasized. To tone down the conclusion, we have

(1) added details about the Eco-HAB (it being coarse-grained, etc.) in the abstract to tone down the conclusion.

(2) added to the results summary in the Discussion (top of page 12) that the results are “within in the setup of the semi-naturalistic Eco-HAB experiments”

(3) added to the Discussion (page 13) that the different results compared to Shemesh et al 2013 means that general studies of social behavior need to compare models with different levels of complexity (e.g. pairwise vs. higher-order interactions). (Also see Reviewer 2 Comment 2.)

Minor points

(1) Please explain what is measured in Fig. 1C (what is on the y axis?).

Figure 1C shows the activity of the mice as measured by the rate of transitions, i.e. the number of times the mice switch boxes during each hour of the day, averaged over all N = 15 mice and T = 10 days (cohort M1). The error bars represent variability of activities across individuals or across days. For mouse-to-mouse variability (blue), we first compute for each mouse its number of transitions averaged over the same hour for all 10 days, then we compute its standard deviation across all 15 mice and plot it as error bars. For day-to-day variability (orange), we first compute for each day the number of transitions for each hour averaged over all mice, then compute its standard deviation across all 10 days as the errorbar. We have added the detailed explanation in the caption of Figure 1C.

(2) In Fig. 3, it would be better to present the control group also in the main figure instead of the supplementary.

We have merged Figure 3 and Figure 3 Supplementary 1 to present the control group also in the main figure.

(3) In Fig. 3 and corresponding supplements, there seems to be a large difference between males and females. I think this would deserve some more discussion.

While not being the main focus of this paper, we agree with the reviewer that the difference between male and female is important and deserves attention in the discussion and also future study. Thus we have added a paragraph in the Discussion (line 394-399, bottom of page 12).

eLife Assessment

This manuscript provides potentially important findings examining in 2D and 3D models in MYC liver cancer cells changes in DNA repair genes and programs in response to hypoxia. The authors use convincing methodology in most cases, but there is some concern that the analysis is incomplete.

Reviewer #1 (Public review):

Summary:

In this report, the authors made use of a murine cell line derived from a MYC-driven liver cancer to investigate the gene expression changes that accompany the switch from normoxic to hypoxia conditions during 2D growth and the switch from 2D monolayer to 3D organoid growth under normoxic conditions. They find a significant (ca. 40-50%) overlap among the genes that are dysregulated in response to hypoxia in 2D cultures and in response to spheroid formation. Unsurprisingly, hypoxia-related genes were among the most prominently deregulated under both sets of conditions. Many other pathways pertaining to metabolism, splicing, mitochondrial electron transport chain structure and function, DNA damage recognition/repair and lipid biosynthesis were also identified.

Comments on the revised manuscript:

In my original review of this manuscript, I raised 11 points that I thought needed to be addressed and/or clarified by the authors. In response, they have provided an adequate answer to only one of these (point 6), which is little more than a more thorough description of how spheroids were generated. The remaining points that I raised, which would have provided more mechanistic insight into their study were addressed by the authors with the following such comments:

- It is not the focus of this study (Points 1 and 4)

- It is worthy of further validation (Point 2)

- We apologize for not being able to validate everything (Point 3)

- This reviewer has raised an interesting question. We are investigating this hypothesis and hopefully we can give a clear answer in the future (Point 5)

- This is an excellent idea that we certainly will do it in our future experiments (Point 7)

As to responses that the authors made to the other two reviewers' comments: Most pertained to cosmetic alterations involving clarification of methods, inclusion of a new figure or rearrangement of old figures. These were generally answered. However, in response to the last point raised by Rev. 3 to compare "sgRNA abundances at the earliest harvesting time with the distribution in the library...to see whether and to what extent selection has already taken place before the three culture conditions were established", the authors responded with the comment: "This is great point. Unfortunately, we did not perform such an analysis."

I understand that it is often impossible to address all points raised by the reviewers. This can be for a variety of reasons and many times the omissions can be overlooked and accepted if the reviewer can be convinced that a good faith attempt has otherwise been made to address the other deficiencies. However, no such effort has been made here and the study remains deficient and largely descriptive as I pointed out in my original review.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this report, the authors made use of a murine cell life derived from a MYC-driven liver cancer to investigate the gene expression changes that accompany the switch from normoxic to hypoxia conditions during 2D growth and the switch from 2D monolayer to 3D organoid growth under normoxic conditions. They find a significant (ca. 40-50%) overlap among the genes that are dysregulated in response to hypoxia in 2D cultures and in response to spheroid formation. Unsurprisingly, hypoxia-related genes were among the most prominently deregulated under both sets of conditions. Many other pathways pertaining to metabolism, splicing, mitochondrial electron transport chain structure and function, DNA damage recognition/repair, and lipid biosynthesis were also identified.

We thank this reviewer for his/her time and efforts, and the insightful comments.

Major comments:

(1) Lines 239-240: The authors state that genes involved in DNA repair were identified as being necessary to maintain survival of both 2D and 3D cultures (Figure S6A). Hypoxia is a strong inducer of ROS. Thus, the ROS-specific DNA damage/recognition/repair pathways might be particularly important. The authors should look more carefully at the various subgroups of the many genes that are involved in DNA repair. They should also obtain at least a qualitative assessment of ROS and ROS-mediated DNA damage by staining for total and mitochondrial-specific ROS using dyes such as CM-H2-DCFDA and MitoSox. Actual direct oxidative damage could be assessed by immunostaining for 8-oxo-dG and related to the sub-types of DNA damage-repair genes that are induced. The centrality of DNA damage genes also raises the question as to whether the previously noted prominence of the TP53 pathway (see point 5 below) might represent a response to ROS-induced DNA damage.

We thank this reviewer for the insightful comments, and agreed that ROS induced by hypoxia could play a role in modulating DNA repair and consequently cellular essentiality. Although pathway enrichment in Figure S6A (now as Figure 2-figure supplement 4A) showed that DNA repair pathway was essential to cell survival in hypoxia and 3D cultures, the genes associated with this pathway (Ddb1;Brf2;Gtf3c5;Guk1;Taf6) are not typical DNA repair genes. They are more likely involved in gene transcription. However, it will be interesting to see if they are specifically involved in DNA damage in response to ROS, which is out of focus of this study.

(2) Because most of the pathway differences that distinguish the various cell states from one another are described only in terms of their transcriptome variations, it is not always possible to understand what the functional consequences of these changes actually are. For example, the authors report that hypoxia alters the expression of genes involved in PDH regulation but this is quite vague and not backed up with any functional or empirical analyses. PDH activity is complex and regulated primarily via phosphorylation/dephosphorylation (usually mediated by PDK1 and PDP2, respectively), which in turn are regulated by prevailing levels of ATP and ADP. Functionally, one might expect that hypoxia would lead to the down-regulation of PDH activity (i.e. increased PDH-pSer392) as respiration changes from oxidative to non-oxidative. This would not be appreciated simply by looking at PDH transcript levels. This notion could be tested by looking at total and phospho-PDH by western blotting and/or by measuring actual PDH activity as it converts pyruvate to AcCoA.

We agreed with this reviewer that PDH activity regulation could be affected by multi-factors, and it is worthy of further validation by other approaches.

(3) Line 439: Related to the above point: the authors state: "It is likely that blockade of acetyl-CoA production by PDH knockout may force cells to use alternative energy sources under hypoxic and 3D conditions, averting the Warburg effect and promoting cell survival under limited oxygen and nutrient availability in 3D spheroids." This could easily be tested by determining whether exogenous fatty acids are more readily oxidized by hypoxic 2D cultures or spheroids than occurs in normoxic 2D cultures.

We thank for this suggestion. We apologized for not being able to validate everything.

(4) Line 472: "Hypoxia induces high expression of Acaca and Fasn in NEJF10 cells indicating that hypoxia promotes saturated fatty acid synthesis...The beneficial effect of Fasn and Acaca KO to NEJF10 under hypoxia is probably due to reduction of saturated fatty acid synthesis, and this hypothesis needs to be tested in the future.". As with the preceding comment, this supposition could readily be supported directly by, for example, performing westerns blots for these enzymes and by showing that incubation of hypoxic 2D cells or spheroids converted more AcCoA into lipid.

We thank for this suggestion. However, functional validation for the Fasn and Acaca KO is out of focus in this study.

(5) In Supplementary Figure 2B&C, the central hub of the 2D normoxic cultures is Myc (as it should well be) whereas, in the normoxic 3D, the central hub is TP53 and Myc is not even present. The authors should comment on this. One would assume that Myc levels should still be quite high given that Myc is driven by an exogenous promoter. Does the centrality of TP53 indicate that the cells within the spheroids are growtharrested, being subjected to DNA damage and/or undergoing apoptosis?

The predicted transcription factor activity analysis was based on the differential ATAC-seq peaks among different culture through pairwise comparisons. If TP53 and MYC were not present under that condition, it did not mean their activity was absent.

“…the centrality of TP53 indicate that the cells within the spheroids are growth-arrested, being subjected to DNA damage and/or undergoing apoptosis?” This reviewer has raised an interesting question. We are investigating this hypothesis and hopefully we can give a clear answer in the future.

(6) In the Materials and Methods section (lines 711-720), the description of how spheroid formation was achieved is unclear. Why were the cells first plated into non-adherent 96 well plates and then into nonadherent T75 flasks? Did the authors actually utilize and expand the cells from 144 T75 flasks and did the cells continue to proliferate after forming spheroids? Many cancer cell types will initially form monolayers when plated onto non-adherent surfaces such as plastic Petri dishes and will form spheroid-like structures only after several days. Other cells will only aggregate on the "non-adherent" surface and form spheroid-like structures but will not actually detach from the plate's surface. Have the authors actually documented the formation of true, non-adherent spheroids at 2 days and did they retain uniform size and shape throughout the collection period? The single photo in Supplementary Figure 1 does not explain when this was taken. The authors include a schematic in Figure 2A of the various conditions that were studied. A similar cartoon should be included to better explain precisely how the spheroids were generated and clarify the rationale for 96 well plating. Overall, a clearer and more concise description of how spheroids were actually generated and their appearance at different stages of formation needs to be provided.

The cells were initially plated in non-adherent 96-well plates to facilitate the formation of spheroids in a controlled and uniform manner. As correctly mentioned by the reviewer, during the initial stages, cells cultured on non-adherent surfaces often form aggregates or clumps, and it takes a few days for them to develop into solid spheroids.

In our study, we aimed to achieve 3D spheroid formation immediately following the transduction process to allow for screening under both 2D and 3D conditions. Plating the cells into 96-well plates enabled us to monitor and control the formation of spheroids in smaller volumes before scaling up the culture in non-adherent T75 flasks for subsequent experimental steps. This setup allows us to maintain gene editing processes under both 2D and 3D conditions.

Regarding the proliferation and uniformity of spheroids:

• Yes, the spheroids continued to proliferate after their formation.

• True, non-adherent spheroids were documented as early as the next day. This was visually confirmed under microscopy, and size uniformity was maintained throughout the collection period by following optimized culture protocols.

We also agreed with the reviewer’s suggestion to include a cartoon schematic similar to Figure 2A, illustrating the spheroid generation process and clarifying the rationale for using 96-well plates. We have included such a cartoon and speroid growth curve monitored by Incucyte as Figure 2-figure supplement 2.

(7) The authors maintained 2D cultures in either normoxic or hypoxic (1% O2) states during the course of their experiments. On the other hand, 3D cultures were maintained under normoxic conditions, with the assumption that the interiors of the spheroids resemble the hypoxic interiors of tumors. However, the actual documentation of intra-spheroid hypoxia is never presented. It would be a good idea for the authors to compare the degree of hypoxia achieved by 2D (1% O2) and 3D cultures by staining with a hypoxia-detecting dye such as Image-iT Green. Comparing the fluorescence intensities in 2D cultures at various O2 concentrations might even allow for the construction of a "standard curve" that could serve to approximate the actual internal O2 concentration of spheroids. This would allow the authors to correlate the relative levels of hypoxia between 2D and 3D cultures.

This is an excellent idea that we certainly will do it in our future experiments.

(8) Related to the previous 2 points, the authors performed RNAseq on spheroids only 48 hours after initiating 3D growth. I am concerned that this might not have been a sufficiently long enough time for the cells to respond fully to their hypoxic state, especially given my concerns in Point 6. Might the results have been even more robust had the authors waited longer to perform RNA seq? Why was this short time used?

We agreed with this reviewer. We were unsure if 48hours was an ideal timepoint. It might be necessary to perform a longitudinal experiment to harvest samples under different timepoints in the future experiments.

(9) What happens to the gene expression pattern if spheroids are re-plated into standard tissue culture plates after having been maintained as spheroids? Do they resume 2D growth and does the gene expression pattern change back?

This is a great question and we have never thought about what the gene expression pattern would be if speroids are re-plated in 2D. This could be a challenging experiment because the gene expression and epigenetic changes are timing related. However, the cells do grow well after re-plated in 2D.

(10) Overall, the paper is quite descriptive in that it lists many gene sets that are altered in response to hypoxia and the formation of spheroids without really delving into the actual functional implications and/or prioritizing the sets. Some of these genes are shown by CRISPR screening to be essential for maintaining viability although in very few cases are these findings ever translated into functional studies (for example, see points 14 above). The list of genes and gene pathways could benefit from a better explanation and prioritization of which gene sets the authors believe to be most important for survival in response to hypoxia and for spheroid formation.

This was a genome-wide study that integrated RNA-seq, ATAC-seq and CRISPR KO, providing resource to understand the oncogenic pathways in different culture conditions. We believe we have clearly articulated the important genes/pathways in our abstract.

(11) The authors used a single MYC-driven tumor cell line for their studies. However, in their original paper (Fang, et al. Nat Commun 2023, 14: 4003.) numerous independent cell lines were described. It would help to know whether RNAseq studies performed on several other similar cell lines gave similar results in terms of up & down-regulated transcripts (i.e. representative of the other cell lines are NEJF10 cells).

We have not generated RNA-seq data for these cell lines cultured in different conditions.

Reviewer #2 (Public review):

Summary:

The manuscript by Fang et al., provides a tour-de-force study uncovering cancer cell's varied dependencies on several gene programs for their survival under different biological contexts. The authors addressed genomic differences in 2D vs 3D cultures and how hypoxia affects gene expression. They used a Myc-driven murine liver cancer model grown in 2D monolayer culture in normoxia and hypoxia as well as cells grown as 3D spheroids and performed CRISPR-based genome-wide KO screen to identify genes that play important roles in cell fitness. Some context-specific gene effects were further validated by in-vitro and in-vivo gene KO experiments.

Strengths:

The key findings in this manuscript are:

(1) Close to 50% of differentially expressed genes were common between 2D Hypoxia and 3D spheroids conditions but they had differences in chromatin accessibility.

(2) VHL-HIF1a pathway had differential cell fitness outcomes under 2D normoxia vs 2D hypoxia and 3D spheroids.

(3) Individual components of the mitochondrial respiratory chain complex had contrasting effects on cell fitness under hypoxia.

(4) Knockout of organogenesis or developmental pathway genes led to better cell growth specifically in the context of 3D spheroids and knockout of epigenetic modifiers had varied effects between 2D and 3D conditions.

(5) Another key program that leads to cells fitness outcomes in normoxia vs hypoxia is the lipid and fatty acid metabolism.

(6) Prmt5 is a key essential gene under all growth conditions, but in the context of 3D spheroids even partial loss of Prmt5 has a synthetic lethal effect with Mtap deletion and Mtap is epigenetically silenced specifically in the 3D spheroids.

We appreciate this reviewer for acknowledging the strengths of our study.

Issues to address:

(1) The authors should clarify the link between the findings of the enrichment of TGFb-SMAD signaling REACTOME pathway to the findings that knocking out TGFb-SMAD pathway leads to better cell fitness outcomes for cells in the 3D growth conditions.

We have clarified this link in abstract by saying “Notably, multicellular organogenesis signaling pathways including TGFb-SMAD, which is upregulated in 3D culture, specifically constrict the uncontrolled cell proliferation in 3D while inactivation of epigenetic modifiers (Bcor, Kmt2d, Mettl3 and Mettl14) has opposite outcomes in 2D vs. 3D:

(2) Supplementary Figure 4C has been cited in the text but doesn't exist in the supplementary figures section.

Sorry for this typo. It should be 5C which is Figure 2-figure supplement 3C in the new version of MS. We have corrected it now.

(3) A small figure explaining this ABC-Myc driven liver cancer model in Supplementary Figure 1 would be helpful to provide context.

We appreciate this suggestion. We have added a cartoon as Figure 1-figure supplement 1A to indicate the procedure for generation of this model.

(4) The method for spheroids formation is not found in the method section.

We described the method in our previous publication (Nature Communications 2023 Jul 6;14(1):4003.). However, we have added the information in method now, and the procedure is very simple (line 623-624). We found the murine liver cancer cell lines can readily form spheroids when they are cultured in low-attachment dish with standard DMEM complete media.

(5) In Supplementary Figure 1b, the comparisons should be stated the opposite way - 3D vs 2D normoxia and 2D-Hypoxia vs 2D-Normoxia.

We have made correction in the Figure legend of Figure S1B which is Figure 1B now in the new version of MS.

(6) There are typos in the legend for Supplementary Figure 10.

We have checked the typos.

(7) Consider putting Supplementary Figure 1b into the main Figure 1.

We have moved both Supplementary Figure 1a and 1b into main Figure 1 as Figure 1A and 1B. Hopefully, this will help the readers to catch the information easily.

(8) Please explain only one timepoint (endpoint) for 3D spheroids was performed for the CRISPR KO screen experiment, while several timepoints were done for 2D conditions? Was this for technical convenience?

As this reviewer speculated, indeed this was for technical convenience. We found that it was technically challenging to split the spheroids for CRISPR screening.

(9) In line 372, it is indicated that Bcor KO (Fig 5e) had growth advantage - this was observed in only one of the gRNA -- same with Kmt2d KO in the same figure where there was an opposite effect. Please justify the use of only one gRNA.

We actually used 4 gRNAs for each gene. In the heatmap, although one of the gRNA for each gene showed some levels of enrichment under hypoxic 2D condition, they were all highly enriched in 3D.

(10) Why was CRISPR based KO strategy not used for the PRMT5 gene but rather than the use of shRNA.? Note that one of the shRNA for PRMT5 had almost no KO (PRMT5-shRNA2 Figure 7B) but still showed phenotype (Figure 7D) - please explain.

We used shRNA as second approach for cross-validation. We agreed that the knockdown efficiency of shRNA2 was not as good as the others, with only about 40% knockdown efficiency.

(11) In Figure 7D, which samples (which shRNA group) were being compared to do the t-test?

The comparisons were for shCtrl and each of the shPRMT5. We have clarified this in figure legend.

(12) In line 240, it is stated that oxphos gene set is essential for NEJF10 cell survival in both normoxia and hypoxia conditions. But shouldn't oxphos be non-essential in hypoxia as cells move away from oxphos and become glycolytic?

This is a great question. While indeed hypoxia may promote the switch from oxphos to glycolysis, several studies showed that the low oxygen concentrations in hypoxic regions of tumors may not be limiting for oxphos, and ATP is generated by oxphos in tumors even at very low oxygen tensions (please see review Clin Cancer Res (2018) 24 (11): 2482–2490.). We therefore speculated that NEJF10 cells were still dependent on oxphos for ATP production under hypoxia. However, this needs further investigation. We have added this discussion in our manuscript (line 250-254).

(13) In line 485 it is mentioned that Pmvk and Mvd genes which are involved in cholesterol synthesis when knocked out had a positive effect on cell growth in 3D conditions and since cholesterol synthesis is essential for cell growth how does this not matter much in the context of 3D - please explain.

We thank this reviewer for this note. It seemed that only two gRNA for each were upregulated in 3D and it could be due to technical issue or clonal selection. We have deleted this sentence in our new version of MS.

Reviewer #3 (Public review):

Summary:

In this study, Fang et al. systematically investigate the effects of culture conditions on gene expression, genome architecture, and gene dependency. To do this, they cultivate the murine HCC line NEJF10 under standard culture conditions (2D), then under similar conditions but under hypoxia (1% oxygen, 2D hypoxia) and under normoxia as spheroids (3D). NEJF10 was isolated from a marine HCC model that relies exclusively on MYC as a driver oncogene. In principle, (1) RNA-seq, (2) ATAC-seq and (3) genetic screens were then performed in this isogenic system and the results were systematically compared in the three cultivation methods. In particular, genome-wide screens with the CRISPR library Brie were performed very carefully. For example, in the 2D conditions, many different time points were harvested to control the selection process kinetically. The authors note differential dependencies for metabolic processes (not surprisingly, hypoxia signaling is affected) such as the regulation and activity of mitochondria, but also organogenesis signaling and epigenetic regulation.

Strengths:

The topic is interesting and relevant and the experimental set-up is carefully chosen and meaningful. The paper is well written. While the study does not reveal any major surprises, the results represent an important resource for the scientific community.

We thank this reviewer for his/her positive comments.

Weaknesses:

However, this presupposes that the statistical analysis and processing are carried out very carefully, and this is where my main suggestions for revision begin. Firstly, I cannot find any information on the number of replicates in RNA- and ATAC-seq. This should be clearly stated in the results section and figure legends and cut-offs, statistical procedures, p-values, etc. should be mentioned as well. In principle, all NGS experiments (here ATAC- and RNA-seq) should be performed in replicates (at least duplicates, better triplicates) or the results should be validated by RT-PCR in independent biological triplicates. Secondly, the quantification of the analyses shown in the figures and especially in the legends is not sufficiently careful. Units are often not mentioned. Example Figure 4a: The legend says: 'gRNA reads' but how can the read count be -1? I would guess these are FC, log2FC, or Z-values. All figure legends need careful revision.

Based upon the reviewer’s suggestions, we have added details about the replicates in figure legend. For gRNA read heatmap, the scale bar indicates the Z score. We have added the information in figure legends.

Furthermore, I would find a comparison of the sgRNA abundances at the earliest harvesting time with the distribution in the library interesting, to see whether and to what extent selection has already taken place before the three culture conditions were established (minor point).

This is great point. Unfortunately, we did not perform such an analysis.

Recommendations for the authors:

Reviewing Editor:

There are three general issues:

First, there is a lack of detail regarding much of the analysis. In some cases, this makes it difficult to assess the value of the data, albeit, there is generally a consensus the information is really interesting.

Second, the findings - although provocative - lack mechanistic details and are focused more on descriptive findings. Hence, the manuscript would be improved by some effort at evaluating identified programs and providing some suggestions of mechanisms.

Third, the authors need to put much more effort into the clarity and tightness of the presentation.

We have made clarification in response to the reviewer’s comments.

Reviewer #1 (Recommendations for the authors):

Figure S1C. the labeling of the lower x-axis is inverted.

Due to space limitation, we changed the figure orientation in our old version of MS. We have tilted the figure back in the new version, which is Figure 1-figure supplement 1B now.

eLife Assessment

Centromeres are specific sites on chromosomes that are essential for mitosis and genome fidelity. This valuable research advance builds upon previous studies to convincingly show that the centromere-histone core contributes to force transduction through the kinetochore. The centromere mainly strengthens one of the two paths of force transduction, influenced by the centromeric DNA sequence. The mechanism underlying this phenomenon will be an exciting future avenue of research, given that centromeric DNAs are not conserved. This work will be of interest to those studying cell division and chromosome segregation.

Reviewer #1 (Public review):

Summary:

The authors address the role of the centromere histone core in force transduction by the kinetochore

Strengths:

They use a hybrid DNA sequence that combines CDEII and CDEIII as well as Widom 601 so they can make stable histones for biophysical studies (provided by the Widom sequence) and maintain features of the centromere (CDE II and III).

Weaknesses:

The main results are shown in one figure (Fig 2). Indeed the Centromere core of Widom and CDE II and III contribute to strengthening the binding force for the OA-beads. The data are very nicely done and convincingly demonstrate the point. The weakness is that this is the entire paper. It is certainly of interest to investigators in kinetochore biology, but beyond that the impact is fairly limited in scope.

Comments on revisions:

The additional information provided by the authors will help the reader understand and interpret the manuscript.

Reviewer #2 (Public review):

Summary:

This paper provides a valuable addendum to the findings described in Hamilton et al. 2020 (https://doi.org/10.7554/eLife.56582). In the earlier paper, the authors reconstituted the budding yeast centromeric nucleosome together with parts of the budding yeast kinetochore and tested which elements are required and sufficient for force transmission from microtubules to the nucleosome. Although budding yeast centromeres are defined by specific DNA sequences, this earlier paper did not use centromeric DNA but instead the generic Widom 601 DNA. The reason is that it has so far been impossible to stably reconstitute a budding yeast centromeric nucleosome using centromeric DNA.

In this new study, the authors now report that they were able to replace part of the Widom 601 DNA with centromeric DNA from chromosome 3. This makes the assay more closely resemble the in vivo situation. Interestingly, the presence of the centromeric DNA fragment makes one type of minimal kinetochore assembly, but not the other, withstand stronger forces.

Which kinetochore assembly turned out to be affected was somewhat unexpected, and can currently not be reconciled with structural knowledge of the budding yeast centromere/kinetochore. This highlights that, despite recent advances (e.g. Guan et al., 2021; Dendooven et al., 2023), aspects of budding yeast kinetochore architecture and function remain to be understood and that it will be important to dissect the contributions of the centromeric DNA sequence.

In the future, it will be interesting to pinpoint which interactions contribute to the enhanced force resistance in the presence of centromeric DNA.

Strength:

- The paper demonstrates that centromeric DNA can increase the attachment strength between budding yeast microtubules and centromeric nucleosomes.

Weakness:

- How centromeric DNA exerts this effect remains unclear.

Comments on revisions:

I appreciate the authors' detailed response and their decision to list all the tested in chimeras in Table 3.

All my prior comments have been addressed.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

Summary:

The authors address the role of the centromere histone core in force transduction by the kinetochore.

Strengths:

They use a hybrid DNA sequence that combines CDEII and CDEIII as well as Widom 601 so they can make stable histones for biophysical studies (provided by the Widom sequence) and maintain features of the centromere (CDE II and III).

Weaknesses:

The main results are shown in one figure (Figure 2). Indeed the Centromere core of Widom and CDE II and III contribute to strengthening the binding force for the OA-beads. The data are very nicely done and convincingly demonstrate the point. The weakness is that this is the entire paper. It is certainly of interest to investigators in kinetochore biology, but beyond that, the impact is fairly limited in scope.

This reviewer might have missed that this is a Research Advance, not an article. Research Advances are limited in scope by definition and provide a new development that builds on research reported in a prior paper. They can be of any length. Our Research Advance builds on our prior work, Hamilton et al., 2020 and provides the new result that native centromere sequences strengthen the attachment of the kinetochore to the nucleosome.

Reviewer #2:

Summary:

This paper provides a valuable addendum to the findings described in Hamilton et al. 2020 (https://doi.org/10.7554/eLife.56582). In the earlier paper, the authors reconstituted the budding yeast centromeric nucleosome together with parts of the budding yeast kinetochore and tested which elements are required and sufficient for force transmission from microtubules to the nucleosome. Although budding yeast centromeres are defined by specific DNA sequences, this earlier paper did not use centromeric DNA but instead the generic Widom 601 DNA. The reason is that it has so far been impossible to stably reconstitute a budding yeast centromeric nucleosome using centromeric DNA.

In this new study, the authors now report that they were able to replace part of the Widom 601 DNA with centromeric DNA from chromosome 3. This makes the assay more closely resemble the in vivo situation. Interestingly, the presence of the centromeric DNA fragment makes one type of minimal kinetochore assembly, but not the other, withstand stronger forces.

We thank the reviewer for their careful and positive assessment of our work.

Which kinetochore assembly turned out to be affected was somewhat unexpected, and can currently not be reconciled with structural knowledge of the budding yeast centromere/kinetochore. This highlights that, despite recent advances (e.g. Guan et al., 2021; Dendooven et al., 2023), aspects of budding yeast kinetochore architecture and function remain to be understood and that it will be important to dissect the contributions of the centromeric DNA sequence.

We couldn’t agree more.

Given the unexpected result, the study would become yet more informative if the authors were able to pinpoint which interactions contribute to the enhanced force resistance in the presence of centromeric DNA.

Strength:

The paper demonstrates that centromeric DNA can increase the attachment strength between budding yeast microtubules and centromeric nucleosomes.

Weakness:

How centromeric DNA exerts this effect remains unclear.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Additional specific mutants would be helpful in interpreting the effect observed. The authors speculate that a small segment of OA near the DNA (based on Dendooven et al., 2023) could be important. Would it be possible to introduce specific mutations and test this?

This would be an interesting study but is far beyond the scope of a Research Advance. In fact, it would make a nice thesis project for a new student. Although perhaps not obvious, these studies require a large set of reagents including wrapped nucleosomes, which must be made fresh (they cannot be frozen) and five purified recombinant complexes, purified by specialized protocols that maintain their activity. Moreover, each datapoint is gathered one at a time. For example, the data in Figure 2 in this manuscript includes 343 datapoints acquired one at a time over the course of 1.5 years.  

(2) Please provide the sequences of the other CEN3-W601 chimeras that were tested and did NOT stably wrap centromeric histone octamers. This may help others to design yet different constructs in the future. (Maybe the information is there and I didn't see it?)

We fully agree and thank the reviewer for this excellent suggestion. The sequences and summaries of their wrapping stability are now provided in Table 3, page 17.

(3) I wonder whether the authors tested the C0N3 sequence used in Dendooven et al., 2023. If not, could it be tested? This would more tightly couple the functional assay shown here with the structural work.

We did not test the CON3 sequence, which was published several years after the start of this work. We agree that a tight coupling between the functional assay and the structural work would be useful. However, we also see the advantage of being able to go beyond the structural work and include even more CEN3 sequence than has so far been possible in the structural work.  

In addition to measuring the role of DNA sequence in Okp1/Ame1 attachment to the nucleosome, we were interested in the role of DNA sequence in the attachment of Mif2. Therefore, we included all 35 bp of the Mif2 footprint in our chimeric CCEN DNA sequence. CON3 only includes 8 bp from CDEII. We did produce stable nucleosomes using CEN3-601 from Guan et al. (see Table 3). Again, CEN3-601 only includes 8 bp of the Mif2 footprint so we opted to study nucleosomes wrapped in our CCEN DNA with the entire Mif2 footprint. Curiously we found that even the entire Mif2 footprint was not enough to find the DNA sequence specificity seen in the EMSA experiments reported by Xiao et al., 2017.

To help readers understand the differences between all these constructs, we have included them in Table 3.

(4) Would an AlphaFold 3 prediction of the assemblies used in this paper be feasible and useful?

The structures of the Dam1 complex (Jenni et al., 2018), Ndc80 complex (Zahm, et al., 2023 and references therein), MIND complex (Dimitrova et al., 2016), OA complex (Dendooven et al., 2023), and the nucleosome (Xaio et al., 2017; Yan et al., 2019; Guan et al., 2021; Dendooven et al., 2023) are published. The interactions between many of these complexes are understood beyond the level that AlphaFold3 could provide (Dimitrova et al., 2016; Dendooven et al., 2023). One of the main questions is how Mif2 interacts with the nucleosome and the other components of the kinetochore. Even structural analyses that included Mif2 in the assembly detect little or no Mif2 in the final structure. Unfortunately, AlphaFold3 is also not helpful as it predicts only the structure of the dimerization domain, which was already known (Cohen et al., 2008).

AlphaFold3 predicts the rest of Mif2 is largely unstructured with several alpha helices predicted with low confidence.

(5) Given that the centromeric DNA piece included should be able to bind the CBF3 complex, would it be possible to add this complex and test the effect on force transmission?

This would be an interesting experiment, and we do expect CBF3 to bind. As stated above, this is far beyond the scope of this Research Advance. In our experience, with each new kinetochore subcomplex that we add into our reconstitutions, there are new challenges purifying the subcomplex in active form and in sufficient quantity. We are eager to add CBF3 but this is not something we can pull off in the context of this Research Advance. Thank you again for the time and energy spent reviewing our manuscript

eLife Assessment

The bacterial cell wall is crucial to maintain viability. It has previously been suggested that Gram positive bacteria have a periplasmic region between the cell membrane and peptidoglycan cell wall that this is maintained by the presence of teichoic acids. In this valuable study, Nguyen et al. make clever use of electron microscopy and metabolic labelling to interrogate the role of teichoic acids in supporting the maintenance of the periplasmic region in Streptococcus pneumoniae. The findings are solid and close some crucial knowledge gaps whilst providing novel tools to further interrogate discrepancies in the field. This work will be of broad interest to microbiologists.

Reviewer #1 (Public review):

The authors set out to analyse the roles of the teichoic acids of Streptococcus pneumoniae in supporting the maintenance of the periplasmic region. Previous work has proposed the periplasm to be present in Gram positive bacteria and here advanced electron microscopy approach was used. This also showed a likely role for both wall and lipo-teichoic acids in maintaining the periplasm. Next, the authors use a metabolic labelling approach to analyse the teichoic acids. This is a clear strength as this method cannot be used for most other well studied organisms. The labelling was coupled with super-resolution microscopy to be able to map the teichoic acids at the subcellular level and a series of gel separation experiments to unravel the nature of the teichoic acids and the contribution of genes previously proposed to be required for their display. The manuscript could be an important addition to the field but there are a number of technical issues which somewhat undermine the conclusions drawn at the moment. These are shown below and should be addressed. More minor points are covered in the private

Recommendations for Authors.

Weaknesses to be addressed:

(1) l. 144 Was there really only one sample that gave this resolution? Biological repeats of all experiments are required.

(2) Fig. 4A. Is the pellet recovered at "low" speeds not just some of the membrane that would sediment at this speed with or without LTA? Can a control be done using an integral membrane protein and Western Blot? Using the tacL mutant would show the behaviour of membranes alone.

(3) Fig. 4A. Using enzymatic digestion of the cell wall and then sedimentation will allow cell wall associated proteins (and other material) to become bound to the membranes and potentially effect sedimentation properties. This is what is in fact suggested by the authors (l. 1000, Fig. S6). In order to determine if the sedimentation properties observed are due to an artefact of the lysis conditions a physical breakage of the cells, using a French Press, should be carried out and then membranes purified by differential centrifugation. This is a standard, and well-established method (low-speed to remove debris and high-speed to sediment membranes) that has been used for S. pneumoniae over many years but would seem counter to the results in the current manuscript (for instance Hakenbeck, R. and Kohiyama, M. (1982), Purification of Penicillin-Binding Protein 3 from Streptococcus pneumoniae. European Journal of Biochemistry, 127: 231-236).

(4) l. 303-305. The authors suggest that the observed LTA-like bands disappear in a pulse chase experiment (Fig. 6B). What is the difference between this and Fig. 5B, where the bands do not disappear? Fig. 5C is the WT and was only pulse labelled for 5 min and so would one not expect the LTA-like bands to disappear as in 6B?

(5) Fig. 6B, l. 243-269 and l. 398-410. If, as stated, most of the LTA-like bands are actually precursor then how can the quantification of LTA stand as stated in the text? The "Titration of Cellular TA" section should be re-evaluated or removed? If you compare Fig. 6C WT extract incubated at RT and 110oC it seems like a large decrease in amount of material at the higher temperature. Thus, the WT has a lot of precursors in the membrane? This needs to be quantified.

(6) L. 339-351, Fig. 6A. A single lane on a gel is not very convincing as to the role of LytR. Here, and throughout the manuscript, wherever statements concerning levels of material are made, quantification needs to be done over appropriate numbers of repeats and with densitometry data shown in SI.

(7) 14. l. 385-391. Contrary to the statement in the text, the zwitterionic TA will have associated counterions that results in net neutrality. It will just have both -ve and +ve counterions in equal amounts (dependent on their valency), which doesn't matter if it is doing the job of balancing osmolarity (rather than charge).

Comments on revisions:

The resubmitted manuscript now contains new data and changes to the text.

The authors have largely covered my previous points in both sets of reviews (Public/Recommendations).

Public Review Points:

1 & 6: I still do not see a reproducibility statement as such, with details of the number of biological repeats etc.

2 & 3. Fig S7 seems to be quite telling. As predicted after physical breakage the membrane proteins sediment at high speed (rather than low speed). This presumably also means that the LTA comes down at high and not low speed. LTA was not measured due to cost of reagents. The Microfluidizer breaks the cells using a shear force and thus is unlikely to create very small membrane fragments. Thus, the sedimentation properties of membranes containing LTA are likely dependent on the way in which the cells are lysed. It is therefore worthwhile qualifying the statements on l. 35-36, 46-47 and 212 (as Ref 8 used mechanical breakage). This will give better direction to those in the field following up the findings.

It is also a little alarming that the mutanolysin is contaminated by protease and one hopes this does not affect any of the properties of the materials being analysed.

Reviewer #2 (Public review):

The Gram-positive cell wall contains for a large part of TAs, and is essential for most bacteria. However, TA biosynthesis and regulation is highly understudied because of the difficulties in working with these molecules. This study closes some of our important knowledge gaps related to this and provides new and improved methods to study TAs. It also shows an interesting role for TAs in maintaining a 'periplasmic space' in Gram positives. Overall, this is an important piece of work. Future work will need to address the possible causal link between TAs and periplasmic space, for instance using complemented mutants and CEMOVIS. It will be interesting to see what happens with the periplasmic space in other mutants besides TA or also in strains with capsules/without capsules and in PG mutants, or in lafB (essential for production of another glycolipid) mutants. Overall, I support the publication of this revised work as it pioneers some new methods that will definitively move the field forward.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

The authors set out to analyse the roles of the teichoic acids of Streptococcus pneumoniae in supporting the maintenance of the periplasmic region. Previous work has proposed the periplasm to be present in Gram positive bacteria and here advanced electron microscopy approach was used. This also showed a likely role for both wall and lipo-teichoic acids in maintaining the periplasm. Next, the authors use a metabolic labelling approach to analyse the teichoic acids. This is a clear strength as this method cannot be used for most other well studied organisms. The labelling was coupled with super-resolution microscopy to be able to map the teichoic acids at the subcellular level and a series of gel separation experiments to unravel the nature of the teichoic acids and the contribution of genes previously proposed to be required for their display. The manuscript could be an important addition to the field but there are a number of technical issues which somewhat undermine the conclusions drawn at the moment. These are shown below and should be addressed. More minor points are covered in the private Recommendations for Authors.

Weaknesses to be addressed:

(1) l. 144 Was there really only one sample that gave this resolution? Biological repeats of all experiments are required.

CEMOVIS is a very challenging method that is not amenable to numerous repeats. However, multiple images were recorded from at least two independent samples for each strain. Additional sample images are shown in a new Fig. S3.

CETOVIS is even more challenging (only two publications in Pubmed since 2015) and was performed on a single ultrathin section that, exceptionally, laid perfectly flat on the EM grid, allowing tomography data acquisition on ∆tacL cells. The reconstructed tomogram confirmed the absence of a granular layer in the depth of the section. Additionally, the numbering of Fig. S4A-B (previously misidentified as Fig. S2A-B) has been corrected in the text of V2.

(2) Fig. 4A. Is the pellet recovered at "low" speeds not just some of the membrane that would sediment at this speed with or without LTA? Can a control be done using an integral membrane protein and Western Blot? Using the tacL mutant would show the behaviour of membranes alone.

We think that the pellet is not just some of the membrane but most of it. In support of this view, the “low” speed pellets after enzymatic cell lysis contain not just some membrane lipids, but most of them (Fig. S10A). We therefore expect membrane proteins to be also present in this fraction. We performed a Western blot using antibodies against the membrane protein PBP2x (new Fig. S7C). Unfortunately, no signal was detected most likely due to protein degradation from contaminant proteases that we could trace to the purchased mutanolysin. The same sedimentation properties were observed with the ∆tacL strain as shown in Fig. 6A. However, in the ∆tacL strain the membrane pellet still contains membrane-bound TA precursors. It is therefore impossible to test definitely if pneumococcal membranes totally devoid of TA would sediment in the same way.

(3) Fig. 4A. Using enzymatic digestion of the cell wall and then sedimentation will allow cell wall associated proteins (and other material) to become bound to the membranes and potentially effect sedimentation properties. This is what is in fact suggested by the authors (l. 1000, Fig. S6). In order to determine if the sedimentation properties observed are due to an artefact of the lysis conditions a physical breakage of the cells, using a French Press, should be carried out and then membranes purified by differential centrifugation. This is a standard, and well-established method (low-speed to remove debris and high-speed to sediment membranes) that has been used for S. pneumoniae over many years but would seem counter to the results in the current manuscript (for instance Hakenbeck, R. and Kohiyama, M. (1982), Purification of Penicillin-Binding Protein 3 from Streptococcus pneumoniae. European Journal of Biochemistry, 127: 231-236).

Thank you for this suggestion. We have tested this hypothesis by breaking cells with a Microfluidizer followed by differential centrifugation. This experiment, which requires an important minimal volume, was performed with unlabeled cells (due to the cost of reagents) and assessed by Western blot using antibodies against the membrane protein PBP2x (new Fig. S7C). In this case, the majority of the membrane material was found in the high-speed pellet, as expected.

We also applied the spheroplast lysis procedure of Flores-Kim et al. to the labeled cells, and found that most of the labeled material sedimented at low speed (new Fig. S7B), as observed with our own procedure.

With these new results, the section on membrane density has been removed from the Supplementary Information. Instead, the fractionation is further discussed in terms of size of membrane fragments and presence of intact spheroplasts in the notes in Supplementary Information preceding Fig. S7.

(4) l. 303-305. The authors suggest that the observed LTA-like bands disappear in a pulse chase experiment (Fig. 6B). What is the difference between this and Fig. 5B, where the bands do not disappear? Fig. 5C is the WT and was only pulse labelled for 5 min and so would one not expect the LTA-like bands to disappear as in 6B?

Fig. 6B shows a pulse-chase experiment with strain ∆tacL, whereas Fig. 5C shows a similar experiment with the parental WT strain. The disappearance of the LTA-like band pattern with the ∆tacL strain (Fig. 6B), and their persistence in the WT strain (Fig. 5C), indicate that these bands are the undecaprenyl-linked TA in ∆tacL and proper LTA in the WT. A sentence has been added to better explain this point in V2.

Note that we have exchanged the previous Fig. 5C and Fig. S13B, so that the experiments of Fig. 5A and 5C are in the same medium, as suggested by Reviewer #2.

(5) Fig. 6B, l. 243-269 and l. 398-410. If, as stated, most of the LTA-like bands are actually precursor then how can the quantification of LTA stand as stated in the text? The "Titration of Cellular TA" section should be re-evaluated or removed? If you compare Fig. 6C WT extract incubated at RT and 110oC it seems like a large decrease in amount of material at the higher temperature. Thus, the WT has a lot of precursors in the membrane? This needs to be quantified.

Indeed, the quantification of the ratio of LTA and WTA in the WT strain rests on the assumption that the amount of membrane-linked polymerized TA precursors is negligible in this strain. This assumption is now stated in the Titration section. We think it is the case. The true LTA and TA precursors do not have exactly the same electrophoretic mobility, being shifted relative to each other by about half a ladder “step”. This difference is visible when samples are run in adjacent lanes on the same gel, as in the new Fig. 6C. The difference of migration was well documented in the original paper about the deletion of tacL, although tacL was known as rafX at that time, and the ladders were misidentified as WTA (Wu et al. 2014. A novel protein, RafX, is important for common cell wall polysaccharide biosynthesis in Streptococcus pneumoniae: implications for bacterial virulence. J Bacteriol. 196, 3324-34. doi: 10.1128/JB.01696-14). This reference was added in V2. The experiment in the new Fig. 6C was repeated to have all samples on the same gel and treated at a lower temperature. The minor effect on the amount of LTA when WT cells are heated at pH 4.2 may be due to the removal of some labeled phosphocholine. We have NMR evidence that the phosphocholine in position D is labile to acidic treatment of LTA, which may lack in some cases, as reported by Hess et al. (Nat Commun. 2017 Dec 12;8(1):2093. doi: 10.1038/s41467-017-01720-z).

(6) L. 339-351, Fig. 6A. A single lane on a gel is not very convincing as to the role of LytR. Here, and throughout the manuscript, wherever statements concerning levels of material are made, quantification needs to be done over appropriate numbers of repeats and with densitometry data shown in SI.

Yes indeed. Apart from the titration of TA in the WT strain, we haven’t yet carried out a thorough quantification of TA or LTA/WTA ratio in different strains and conditions, although we intend to do so in a follow-up study, using the novel opportunities offered by the method presented here.

However, to better substantiate our statement regarding the ∆lytR strain, we have quantified two experiments performed in C-medium with azido-choline, and two experiments of pulse labeling in BHI medium. The results are presented in the additional supplementary Fig. S14. The value of 51% was a calculation error, and was corrected to 41%. Likewise, the decrease in the WTA/LTA ratio was corrected to 5 to 7-fold.

(7) 14. l. 385-391. Contrary to the statement in the text, the zwitterionic TA will have associated counterions that result in net neutrality. It will just have both -ve and +ve counterions in equal amounts (dependent on their valency), which doesn't matter if it is doing the job of balancing osmolarity (rather than charge).

Thank you for pointing out this point. The paragraph has been corrected in V2.

Reviewer #2 (Public review):

The Gram-positive cell wall contains for a large part of TAs, and is essential for most bacteria. However, TA biosynthesis and regulation is highly understudied because of the difficulties in working with these molecules. This study closes some of our important knowledge gaps related to this and provides new and improved methods to study TAs. It also shows an interesting role for TAs in maintaining a 'periplasmic space' in Gram positives. Overall, this is an important piece of work. It would have been more satisfying if the possible causal link between TAs and periplasmic space would have been more deeply investigated with complemented mutants and CEMOVIS. For the moment, there is clearly something happening but it is not clear if this only happens in TA mutants or also in strains with capsules/without capsules and in PG mutants, or in lafB (essential for production of another glycolipid) mutants. Finally, some very strong statements are made suggesting several papers in the literature are incorrect, without actually providing any substantiation/evidence supporting these claims. Nevertheless, I support the publication of this work as it pioneers some new methods that will definitively move the field forward.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) l. 55 It is stated that TA are generally not essential. This needs to be introduced in a little more detail as in several species they are collectively. Need some more references here to give context.

We have expended the paragraph and added a selection of references in V2.

(2) l. 63 and Fig. 1A. Is the model based on the images from this paper? Is the periplasm as thick as the peptidoglycan layer? Would you not expect the density of WTA to be the same throughout the wall, rather than less inside? Do the authors think that the TA are present as rods in the cell envelope and because of this the periplasm looks a little like a bilayer, is this so? Is the relative thickness of the layers based on the data in the paper (Table 1)?

The model proposed in Fig. 1A is not based on our data. It is a representation of the model proposed by Harold Erickson, and the appropriate reference has been added to the figure legend in V2. We do not speculate on the relative density of WTA inside the peptidoglycan layer, at the surface or in the periplasm. The only constraint from the model is that the density of WTA in the periplasm should be sufficient for self-exclusion and allow the brush polymer theory to apply. The legend has been amended in V2.

We indeed think that the bilayer appearance of the periplasmic space in the wild type strain, and the single layer periplasmic space in the ∆tacL and ∆lytR support the Erickson’s model. Although the model was drawn arbitrarily, it turns out that the relative thickness of the peptidoglycan and periplasmic scale is in rough agreement with the measurements reported in Table 1.

(3) Fig. 2. It is hard to orient oneself to see the layers. The use of the term periplasmic space (l. 132) and throughout is probably not wise as it is not a space.

We prefer to retain this nomenclature since the term periplasmic space has been used in all the cell envelope CEMOVIS publications and is at the core of Erickson’s hypothesis about these observations and teichoic acids.

(4) L. 147. This is not referring to Fig. S2A-B as suggested but Fig. S3A-B.

This has been corrected.

(5) l. 148. How do you know the densities observed are due to PG or certainly PG alone? Perhaps it is better to call this the cell wall.

Yes. Cell wall is a better nomenclature and the text and Table 1 have been corrected in V2, in accordance with Fig. 2.

(6) l. 165. It is also worth noting that peripheral cell wall synthesis also happens at the same site so this may well not be just division.

Yes. We have replaced “division site” by “mid-cell” in V2.

(7) l. 214 What is the debris? If PG digestion has been successful then there will be marginal debris. Is this pellet translucent (like membranes)? If you use fluorescently labelled PG in the preparation has it all disappeared, as would be expected by fully digested and solubilised material?

In traditional protocols of bacterial membrane preparation, a low-speed centrifugation is first performed to discard “debris” that to our knowledge have not been well characterized but are thought to consist of unbroken cells and large fragments of cell wall. After enzymatic degradation of the pneumococcal cell wall, the low-speed pellet is not translucent as in typical membrane pellets after ultracentrifugation, but is rather loose, unlike a dense pellet of unbroken cells. A description of the pellet appearance was added in V2.

It is a good idea to check if some labeled PG is also pelleted at low-speed after digestion. In a double labeling experiment using azido-choline and a novel unpublished metabolic probe of the PG, we found that the PG was fully digested and labeled fragments migrated as a couple of fuzzy bands likely corresponding to different labeled peptides. These species were not pelleted at low speed.

(8) l. 219. Can you give a reference to certify that the low mobility material is WTA? Why does it migrate differently than LTA? Or is the PG digestion not efficient?

WTA released from sacculi by alkaline lysis were found to migrate as a smear at the top of native gels revealed by alcian-blue silver staining, which is incompatible with SDS (Flores-Kim, 2019, 2022). The references have be added in V2. It could be argued in this case that the smearing was due to partial degradation of the WTA by the alkaline treatment.

Bui et al. (2012) reported the preparation of WTA by enzymatic digestion of sacculi, but the resulting WTA were without muropeptide, presumably due to a step of boiling at pH 5 used to deactivate the enzymes.

To our knowledge, this is the first report of pneumococcal WTA prepared by digestion of sacculi and analyzed by SDS-PAGE. Since the migration of WTA in native and SDS-PAGE is similar, we hypothesize that they do not interact significantly with the dodecyl sulphate, in contrast to the LTA, which bear a lipidic moiety. The fuzziness of the WTA migration pattern may also result from the greater heterogeneity due to the attached muropeptide, such as different lengths (di-, tetra-saccharide…), different peptides despite the action of LytA (tri-, tetra-peptide…), different O-acetylation status, etc.

(9) L. 226-227, Fig S8. Presumably several of the major bands on the Coomassie stained gel are the lysozyme, mutanolysin, recombinant LytA, DNase and RNase used to digest the cell wall etc.? Can the sizes of these proteins be marked on the gel. Do any of them come down with the material at low-speed centrifugation?

We have provided a gel showing the different enzymes individually and mixed (new Fig. S9G). While performing several experiments of this type, we found that the mutanolysin might be contaminated with proteases. The enzymes do not appear to sediment at low speed.

(10) Fig. S9B. It is difficult to interpret what is in the image as there appear to be 2 populations of material (grey and sometimes more raised). Does the 20,000 g material look the same?

Fig. S10B is a 20,000 × g pellet. We agree that there appears to be two types of membrane vesicles, but we do not know their nature.

(11) l. 277 and Fig. 5A. Why is it "remarkable" that there are apparently more longer LTA molecules as the cell reach stationary phase?

This is the first time that a change of TA length is documented. Such a change could conceivably have consequences in the binding and activity of CBPs and the physiology of the cell envelope in general. These questions should be adressed in future studies.

(12) l. 280. How do you know which is the 6-repeat unit?

It is an assumption based on previous analyses by Gisch et al.( J Biol Chem 2013, 288(22):15654-67. doi: 10.1074/jbc.M112.446963). The reference was added.

(13) Fig. 5A and C. Panel C, the cells were grown in a different medium and so are not comparable to Panel A. Why is Fig. S12B not substituted for 5B? Presumably these are exponential phase cells.

We have interverted the Fig. S13B and 5C in V2, as suggested, and changed the text and legends accordingly.

Reviewer #2 (Recommendations for the authors):

L30: vitreous sections?

Corrected in V2.

L32: as their main universal function --> as a universal function. To show it's the main universal function, you will need to look at this across various bacterial species.

Changed to “possible universal function” in V2.

L35: enabled the titration the actual --> titration of the actual?

Corrected in V2.

L34: consider breaking up this very long sentence.

Done in V2.

L37: may compensate the absence--> may compensate for the absence.

Corrected in V2.

L45: Using metabolic labeling and electrophoresis showed --> Metabolic labeling and...

Corrected in V2.

L46: This finding casts doubts on previous results, since most LTA were likely unknowingly discarded in these studies. This needs to be rephrased and is unnecessarily callous. While the current work casts doubts on any quantitative assessments of actual LTA levels measured in previous studies, it does not mean any qualitative assessments or conclusions drawn from these experiments are wrong. Better would be to say: These findings suggest that previously reported quantitative assessments of LTA levels are likely underestimating actual LTA levels, since much of the LTA would have been unknowingly discarded.

If the authors do think that actual conclusions are wrong in previous work, then they need to be more explicit and explain why they were wrong.

Yes indeed. The statement was toned down in V2.

L55: Although generally non-essential. I would remove or rephrase this statement. I don't think any TA mutant will survive out in the wild and will be essential under a certain condition. So perhaps not essential for growth under ideal conditions, but for the rest pretty essential.

The paragraph was amended by qualifying the essentiality to laboratory conditions and including selected references.

L95: Note that the prevailing model until reference 20 (Gibson and Veening) was that the TA is polymerized intracellularly (see e.g. Figure 2 of PMID: 22432701, DOI: 10.1089/mdr.2012.0026). This intracellular polymerisation model seemed unlikely according to Gibson and Veening ('As TarP is classified by PFAM as a Wzy-type polymerase with predicted active site outside the cell, we speculate that TarP and TarQ polymerize the TA extracellularly in contrast to previous reports.'), but there is no experimental evidence as far as this referee knows of either model being correct.

Despite the lack of experimental evidence, we think that Gibson and Veening are very likely correct, based on their argument, and also by analogy with the synthesis of other surface polysaccharides from undecaprenyl- or dolichol-linked precursors. It is unfortunate that Figure 2 of PMID: 22432701, DOI: 10.1089/mdr.2012.0026 was published in this way, since there was no evidence for a cytoplasmic polymerization, to our knowledge.

L97: It is commonly believed, although I'm not sure it has ever been shown, that the capsule is covalently attached at the same position on the PG as WTA. Therefore, there must be some sort of regulation/competition between capsule biosynthesis and WTA biosynthesis (see also ref. 21). The presence of the capsule might thus also influence the characteristics of the periplasmic space. Considering that by far most pneumococcal strains are encapsulated, the authors should discuss this and why a capsule mutant was used in this study and how translatable their study using a capsule mutant is to S. pneumoniae in general.

A paragraph was added in the Introduction of V2 to present the complication and a sentence was added at the end of the discussion to mention that this should be studied in the future.

L102: Ref 29 should probably be cited here as well?

Since in Ref 29 (Flores-Kim et al. 2019) there is a detectable amount of LTA (presumably precursors TA) in the ∆tacL stain, we prefer to cite only Hess et al. 2017 regarding the absence of LTA in the absence of TacL. However, we added in V2 a reference to Flores-Kim et al. 2019 in the following paragraph regarding the role of the LTA/WTA ratio.

L106: dependent on the presence of the phosphotransferase LytR (21). --> dependent on the presence of the phosphotransferase LytR, whose expression is upregulated during competence (21).

Corrected in V2.

L119: I fail to see how the conclusions drawn by other groups (I assume the authors mean work from the Vollmer, Rudner, Bernhardt, Hammerschmidt, Havarstein, Veening groups?) are invalid if they compared WTA:LTA ratios between strains and conditions if they underestimated the LTA levels? Supposedly, the LTA levels were underestimated in all samples equally so the relative WTA/LTA ratio changes will qualitatively give the same outcome? I agree that these findings will allow for a reassessment of previous studies in which presumably too low LTA levels were reported, but I would not expect a difference in outcome when people compared WTA:LTA ratios between strains?

The sentence was rephrased in V2 to be neutral regarding previous work and rather emphasize future possibilities.

L131: Perhaps it would be good to highlight that such a conspicuous space has been noticed before by other EM methods (see e.g. Figs.4 and 5 or ref 19, or one of the most clear TEM S. pneumoniae images I have seen in Fig. 1F of Gallay et al, Nat. Micro 2021). However, always some sort of staining had previously been performed so it was never clear this was a real periplasmic space. CEMOVIS has this big advantage of being label free and imaging cells in their presumed native state.

Thanks for pointing out these beautiful data that we had overlooked. We have added a few sentences and references in the Discussion of V2.

L201: References are not numbered.

Corrected in V2.

L271/L892: Change section title. 'Evolution' can have multiple meanings. It would be more clear to write something like 'Increased TA chain length in stationary phase cells' or something like that.

Changed in V2.

L275: harvested

Corrected in V2.

L329: add, as suggested shown previously (I guess refs 24 and 29)

Reference to Hess et al. 2017 has been added in V2. A sentence and further references to Flores-Kim, 2019, 2022 and Wu et al. 2014 were added at the end of the discussion with respect to the LTA-like signal observed in these studies of ∆tacL strains.

L337: I think a concluding sentence is warranted here. These experiments demonstrate that membrane-bound TA precursors accumulate on the outside of the membrane, and are likely polymerized on the outside as well, in line with the model proposed in ref. 20.

From the point of view of formal logic, the accumulation of membrane-bound TA precursors on the outer face of the membrane does not prove that they were assembled there. They could still be polymerized inside and translocated immediately. However, since this is extremely unlikely for the reasons discussed by Gibson and Veening, we have added a mild conclusion sentence and the reference in V2.

L343: How accurate are these quantifications? Just by looking at the gel, it seems there is much less WTA in the lytR mutant than 50% of the wild type?

Yes, the 51% value was a calculation error. This was changed to 41%. Likewise, the decrease of the WTA amount relative to LTA was corrected to 5- to 7-fold.

Apart from the titration of TA in the WT strain, we haven’t yet carried out a careful quantification neither of TA nor of the LTA/WTA ratio in different strains and conditions, although we intend to do so in the near future using the method presented here.

However, to better substantiate our statement regarding the ∆lytR strain, we have quantified two experiments of growth in C-medium with azido-choline, and two experiments of pulse labeling in BHI medium. The results are presented in the additional supplementary Fig. S14.

L342: although WTA are less abundant and LTA appear to be longer (Fig. 6A). although WTA are less abundant and LTA appear to be longer (Fig. 6A), in line with a previous report showing that LytR the major enzyme mediating the final step in WTA formation (ref. 21). (or something like that). Perhaps better is to start this paragraph differently. For instance: Previous work showed that LytR is the major enzyme mediating the final step in WTA formation (ref. 21). As shown in Fig. 6A, the proportion of WTA significantly decreased in the lytR mutant. However, there was still significant WTA present indicating that perhaps another LCP protein can also produce WTA.

Changed in V2.

Of note, WTA levels would be a lot lower in encapsulated strains as used in Ref. 21 (assuming WTA and capsule compete for the same linkage on PG). So perhaps it would be hard to detect any residual WTA in a encapsulated lytR mutant?

Investigation of the relationship between TA and capsule incorporation or O-acetylation is definitely a future area of study using this method of TA monitoring.

L371: see my comments related to L131. Some TEM images clearly show the presence of a periplasmic space.

Comments and references have been added in V2.

L402: It would be really interesting to perform these experiments on a wild type encapsulated strain. Would these have much more LTA? (I understand you cannot do these experiments perhaps due to biosafety, but it might be interesting to discuss).

Yes. It would be interesting to compare the TA in D39 and D39 ∆cps strains. We have added this perspective at the end of the discussion in V2.

L418: ref lacks number

Corrected in V2.

L423: refs missing.

References added in V2.

L487: See my comments regarding L46. I do not see one valid point in the current paper why underestimating LTA levels would change any of the conclusions drawn in Ref. 21. I do not know the other papers cited well enough, but it seems highly unlikely that their conclusions would be wrong by systematically underestimating LTA levels. As far as I understand it, this current work basically confirms the major conclusions drawn by these 'doubtful' papers (that TacL makes LTA and LytR is the main WTA producer). As such, I find this sentence highly unfair without precisely specifying what the exact doubts are. Sure, this current paper now shows that probably people have discarded unknowingly LTA and therefore underestimated LTA levels, so any quantitative assessment of LTA levels are probably wrong. That is one thing. But to say this casts doubts on these studies is very serious and unfair (unless the authors provide good arguments to support these serious claims).

Yes indeed. The sentence was rephrased to be strictly factual in V2.

Table 2: I assume these strains are delta cps? Would be relevant to list this genotype.

The Table 2 was completed in V2.

The authors should comment on why the mutants have not been complemented, especially for lytR as it's the last gene in a complex operon. It would be great to see WTA levels being restored by ectopic expression of LytR.

Yes. We think this could be part of an in-depth study of the attachment of WTA, together with the investigation of the other LCP phosphotransferases.

eLife Assessment

This important work investigates the mechanism that underlies the switch between feeding and mating behaviors in the oriental fruit fly, Bactrocera dorsalis. Using a variety of approaches, the authors show that this switch is mediated by the neuropeptide, sulfakinin, acting peripherally through the sulfakinin receptor 1 to regulate the expression of antennal odorant receptors. The evidence is solid in support of the hypothesis that sulfakinin signaling mediates changes in the periphery, although additional sites of action may also contribute to these changes.

Joint Public Review:

Summary:

The behavioral switch between foraging and mating is important for resource allocation in insects. This study characterizes the role of sulfakinin and the sulfakinin receptor 1 in changes in olfactory responses associated with foraging versus mating behavior in the oriental fruit fly (Bactrocera dorsalis), a significant agricultural pest. This pathway regulates food consumption and mating receptivity in other species; here the authors use genetic disruption of sulfakinin and sulfakinin receptor 1 to provide strong evidence that changes in sulfakinin signaling modulate antennal responses to food versus pheromonal cues and alter the expression of ORs that detect relevant stimuli.

Strengths:

The authors utilize multiple complementary approaches including CRISPR/Cas9 mutagenesis, behavioral characterization, electroantennograms, RNA sequencing and heterologous expression to convincingly demonstrate the involvement of the sulfakinin pathway in the switch between foraging and mating behaviors. The use of both sulfakinin peptide and receptor mutants is a strength of the study and implicates specific signaling actors.

Weaknesses:

The authors demonstrate that SKR is expressed in olfactory neurons, however there are additional potential sites of action that may contribute to these results.

Author response:

The following is the authors’ response to the previous reviews

Joint Public Review:

Summary:

The behavioral switch between foraging and mating is important for resource allocation in insects. This study characterizes the role of sulfakinin and the sulfakinin receptor 1 in changes in olfactory responses associated with foraging versus mating behavior in the oriental fruit fly (Bactrocera dorsalis), a significant agricultural pest. This pathway regulates food consumption and mating receptivity in other species; here the authors use genetic disruption of sulfakinin and sulfakinin receptor 1 to provide strong evidence that changes in sulfakinin signaling modulate antennal responses to food versus pheromonal cues and alter the expression of ORs that detect relevant stimuli.

Strengths:

The authors utilize multiple complementary approaches including CRISPR/Cas9 mutagenesis, behavioral characterization, electroantennograms, RNA sequencing and heterologous expression to convincingly demonstrate the involvement of the sulfakinin pathway in the switch between foraging and mating behaviors. The use of both sulfakinin peptide and receptor mutants is a strength of the study and implicates specific signaling actors.

Weaknesses:

The authors demonstrate that SKR is expressed in olfactory neurons, however there are additional potential sites of action that may contribute to these results.

Recommendations for the authors:

The authors have addressed most of the issues raised by the reviewers. Below are a few outstanding issues.

(1) Lines 68-69 describe "control of B. dorsalis include the use of the behavioral responses to semiochemicals" but does not describe what these responses are or how behavior is modulated.

The sentence was revised as “Control of B. dorsalis include the use of the reproductive and feeding behavioral responses to semiochemicals” (lines 69 in the revision).

(2) Statistical analysis for 9 hour starved females at 5 minutes is missing in Figure 1D and S1.

We had added statistical analysis for 9 hour starved females at 5 minutes in the revised Figures 1D and S1, respectively (lines 578).

(3) The legend in Figure S2 should be revised as it is not clear from the figure which of the odors are food associated odors.

As suggested, we added food odor label in the revised Figure S2 (lines 666).

(4) Line 167: "Therefore, the upregulated OR genes in starved WT flies, OR7a.4, OR7a.8 and OR10a, were activated by the pheromonal components, while down regulated genes, OR49a and OR63a, were activated by food volatiles." Based on the data, this sentence is incorrect - Therefore, the upregulated OR genes in starved WT flies, OR7a.4, OR7a.8 and OR10a, were activated by the food components, whereas downregulated genes, OR49a and OR63a, were activated by pheromonal components."

We are sorry for our mistake. We had corrected it (lines 168-169).

(5) Line 192: "The coordinated action of sulfakinin on mutiple downstreams,..." should be revised to "downstream pathways or tissues" or simply removing "multiple downstream".

As suggested, we removed “multiple downstream”. See line 192.

(6) Reference formatting is inconsistent: see line 207 vs line 208.

We had corrected it as “(Wu et al., 2019)” (lines 207). 

(7) Lines 241-244 The broad discussion regarding the evolution and ancestral function of CCK here and the phylogeny in Figure S6 are peripheral to the authors claims.

As suggested, we removed the section and the Figure S6 in the revision.

eLife Assessment

This important study reports findings that Trpγ, a type of transient receptor potential (TRP) channel expressed in Dh44-releasing neuroendocrine cells, mediates starvation-dependent lipid catabolism. Overall, the claims of the authors are supported by solid evidence. The work should be of interest to both basic and medical biologists working on lipid metabolism.

Reviewer #1 (Public review):

Summary:

This research article by Nath et al. from the Lee Lab addresses how lipolysis under starvation is achieved by a transient receptor potential channel, TRPγ, in the neuroendocrine neurons to help animals survive prolonged starvation. Through a series of genetic analyses, the authors identify that trpγ mutations specifically lead to a failure in lipolytic processes under starvation, thereby reducing animals' starvation resistance. The conclusion was confirmed through total triacylglycerol levels in the animals and lipid droplet staining in the fat bodies. This study highlights the importance of transient receptor potential (TRP) channels in the fly brain to modulate energy homeostasis and combat metabolic stress. However, the co-expression of trpγ and Dh44-R2 in the gut is not convincing, especially in the picture of the arrows pointing at the autofluorescence signals in the gut (Figure 7P). Therefore, the authors should either confirm the co-expression or acknowledge that trpγ and Dh44-R2 are not co-expressed in the gut and modify their model in Figure 8 accordingly, although clarifying their co-expression may not change the main conclusions of this study. Overall, the revised version includes the required clarifications on their important results that strengthen the interpretations of the research as well as the visibility of this study.

Strengths:

This study identifies the biological meaning of TRPγ in promoting lipolysis during starvation, advancing our knowledge about the TRPγ channel and the neural mechanisms to combat metabolic stress. Furthermore, this study demonstrates the potential of the TRPγ channel as a target to develop new therapeutic strategies for human metabolic disorders by showing that metformin and AMPK pathways are involved in its function in lipid metabolisms during starvation in Drosophila.

Reviewer #2 (Public review):

Summary

In this paper, the function of trpγ in lipid metabolism was investigated. The authors found that lipid accumulation levels were increased in trpγ mutants and remained high during starvation; the increased TAG levels in trpγ mutants were restored by the expression of active AMPK in DH44 neurons and oral administration of the anti-diabetic drug metformin. Furthermore, oral administration of lipase, TAG and free fatty acids effectively restored survival of trpγ mutants under starvation conditions. These results indicate that TRPv plays an important role in the maintenance of systemic lipid levels through the proper expression of lipase. Furthermore, authors have shown that this function is mediated by DH44R2. This study provides an interesting finding in that the neuropeptide DH44 released from the brain regulates lipid metabolism through a brain-gut axis, acting on the receptor DH44R2 expressed in gut cells.

Strengths

Using Drosophila genetics, careful analysis of which cells express trpγ regulates lipid metabolism is performed in this study. The study supports its conclusions from various angles, including not only TAG levels, but also fat droplet staining and survival rate under starved conditions, and oral administration of substances involved in lipid metabolism.

Weaknesses

The function of lipases, as well as identification of cell types, in the DH44R2-expressing cells in the gut can be investigated.

Reviewer #3 (Public review):

In this manuscript, the authors demonstrated the significance of the TRPγ channel in regulating internal TAG levels. They found high TAG levels in TRPγ mutant, which was ascribed to a deficit in the lipolysis process due to the downregulation of brummer (bmm). It was notable that the expression of TRPγ in DH44+ PI neurons, but not dILP2+ neurons, in the brain restored the internal TAG levels and that the knockdown of TRPγ in DH44+ PI neurons resulted in an increase in TAG levels. These results suggested a non-cell autonomous effect of Dh44+PI neurons. Additionally, the expression of the TRPγ channel in Dh44 R2-expressing cells restored the internal TAG levels. The authors, however, did not provide an explanation of how TRPγ might function in both presynaptic and postsynaptic cells in the non-cell autonomous manner to regulate the TAG storage. The authors further determined the effect of TRPγ mutation on the size of lipid droplets (LD) and the lifespan and found that TRPγ mutation caused an increase in the size of LD and a decrease in the lifespan, which were reverted by feeding lipase and metformin. These were creative endeavors, I thought. The finding that DH44+ PI neurons have non-cell autonomous functions in regulating bodily metabolism (mainly sugar/lipid) in addition to directing sugar nutrient sensing and consumption is likely correct, but the paper has many loose ends.

Comments on revisions:

The authors have addressed nearly all of my concerns with additional experiments and explanations.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This research article by Nath et al. from the Lee Lab addresses how lipolysis under starvation is achieved by a transient receptor potential channel, TRPγ, in the neuroendocrine neurons to help animals survive prolonged starvation. Through a series of genetic analyses, the authors identify that TRPγ mutations specifically lead to a failure in lipolytic processes under starvation, thereby reducing animals' starvation resistance. The conclusion was confirmed through total triacylglycerol levels in the animals and lipid droplet staining in the fat bodies. This study highlights the importance of transient receptor potential (TRP) channels in the fly brain to modulate energy homeostasis and combat metabolic stress. While the data is compelling and the message is easy to follow, several aspects require further clarification to improve the interpretation of the research and its visibility in the field.

Strengths:

This study identifies the biological meaning of TRPγ in promoting lipolysis during starvation, advancing our knowledge about TRP channels and the neural mechanisms to combat metabolic stress. Furthermore, this study demonstrates the potential of the TRP channel as a target to develop new therapeutic strategies for human metabolic disorders by showing that metformin and AMPK pathways are involved in its function in lipid metabolisms during starvation in Drosophila.

Weaknesses:

Some key results that might strengthen their conclusions were left out for discussion or careful explanation (see below). If the authors could improve the writing to address their findings and connect their findings with conclusions, the research would be much more appreciated and have a higher impact in the field.

Here, I listed the major issues and suggestions for the authors to improve their manuscript:

(1) Are the increased lipid droplet size and the upregulated total TAG level measured in the starved or sated mutant in Figure 1? This information might be crucial for readers to understand the physiological function of TRP in lipid metabolism. In other words, clarifying whether the upregulated lipid storage is observed only in the starved trp mutant will advance our knowledge of TRPγ. If the increase of total TAG level is only observed in the starved animals, TRP in the Dh44 neurons might serve as a sensor for the starvation state required to promote lipolysis in starvation conditions. On the other hand, if the total TAG level increases in both starved and sated animals, activation of Dh44 through TRPγ might be involved in the lipid metabolism process after food ingestion.

We measured total TAG level in Figure 1 and LD sizes in Figure 2 under sated condition. We inserted “under sated condition” to clarify it. lines 97 and 147-148.

Thanks for your suggestions.

(2) It is unclear how AMPK activation in Dh44 neurons reduces the total triacylglycerol (TAG) levels in the animals (Figure 3G). As AMPK is activated in response to metabolic stress, the result in Figure 3G might suggest that Dh44 neurons sense metabolic stress through AMPK activation to promote lipolysis in other tissues. Do Dh44 neurons become more active during starvation? Is activation of Dh44 neurons sufficient to activate AMPK in the Dh44 neurons without starvation? Is activation of AMPK in the Dh44 neurons required for Dh44 release and lipolysis during starvation? These answers would provide more insights into the conclusion in Lines 192-193.

In our previous study, we demonstrated that trpγ mutants exhibited lower levels of glucose, trehalose and glycogen level (Dhakal et al. 2022), and in the current study, we observed excessive lipid storage in the trpγ mutant, indicating imbalanced energy homeostasis. Given the established role of AMPK in maintaining energy balance (Marzano et. al., 2021, Lin et al 2021), we employed the activated form of AMPK (UAS-AMPK^TD) in our experiments. Our result showed that expression of activated AMPK in Dh44 neurons led to a reduction in total TAG levels, suggesting that AMPK activation in these neurons can promote lipolysis even in the absence of starvation. Regarding the activation of Dh44 neurons, Dus et al in 2015 reported that Dh44 cells in the brain are activated by nutritive sugars especially in starvation conditions. In addition, another report showed a role of Dh44 neuron in regulating starvation induced sleep suppression (Oh et. al., 2023) which may imply that these neurons become more active under starved conditions. We did not directly assess whether Dh44 neuron activity increases during starvation or whether AMPK activation in these neurons is required for DH44 release and subsequent lipolysis, our finding support the notion that AMPK activation in Dh44 neuron is sufficient to reduce TAG levels, potentially by metabolic stress response typically observed during starvation. We explained it like the following: “Dh44 neurons regulate starvation-induced sleep suppression (Oh et. al., 2023), which implies that these neurons become more active under starved conditions.” lines 190-191.

(3) It is unclear how the lipolytic gene brummer is further downregulated in the trpγ mutant during starvation while brummer is upregulated in the control group (Figure 6A). This result implies that the trpγ mutant was able to sense the starvation state but responded abnormally by inhibiting the lipolytic process rather than promoting lipolysis, which makes it more susceptible to starvation (Figure 3B).

Thanks for your suggestions. We explained it like the following: “The data indicates that the trpg mutant can sense the starvation state but responds abnormally by suppressing lipolysis instead of activating it. This dysregulated lipolytic response likely increases the mutant's vulnerability to starvation, as it cannot effectively mobilize lipid stores for energy during periods of nutrient deprivation.” lines 251-254.

(4) There is an inconsistency of total TAG levels and the lipid droplet size observed in the Dh44 mutant but not in the Dh44-R2 mutant (Figures 7A and 7F). This inconsistency raises a possibility that the signaling pathway from Dh44 release to its receptor Dh44-R2 only accounts for part of the lipid metabolic process under starvation. Adding discussion to address this inconsistency may be helpful for readers to appreciate the finding.

Thanks for your suggestion. We included the following in the Discussion: “There is an inconsistency of total TAG levels and the LD size observed in the Dh44 mutant. This inconsistency raises a possibility that the signaling pathway from DH44 release to its receptor DH44R2 only accounts for part of the lipid metabolic process under starvation. While Dh44 mutant flies displayed normal internal TAG levels, Dh44R2 mutant flies exhibited elevated TAG levels. This suggested that the lipolysis phenotype could be facilitated by a neuropeptide other than DH44. Alternatively, a DH44 neuropeptide-independent pathway could mediate the lipolysis.” lines 429-436.

Reviewer #2 (Public Review):

Summary:

In this paper, the function of trpγ in lipid metabolism was investigated. The authors found that lipid accumulation levels were increased in trpγ mutants and remained high during starvation; the increased TAG levels in trpγ mutants were restored by the expression of active AMPK in DH44 neurons and oral administration of the anti-diabetic drug metformin. Furthermore, oral administration of lipase, TAG, and free fatty acids effectively restored the survival of trpγ mutants under starvation conditions. These results indicate that TRPv plays an important role in the maintenance of systemic lipid levels through the proper expression of lipase. Furthermore, authors have shown that this function is mediated by DH44R2. This study provides an interesting finding in that the neuropeptide DH44 released from the brain regulates lipid metabolism through a brain-gut axis, acting on the receptor DH44R2 presumably expressed in gut cells.

Strengths:

Using Drosophila genetics, careful analysis of which cells express trpγ regulates lipid metabolism is performed in this study. The study supports its conclusions from various angles, including not only TAG levels, but also fat droplet staining and survival rate under starved conditions, and oral administration of substances involved in lipid metabolism.

Weaknesses:

Lipid metabolism in the gut of DH44R2-expressing cells should be investigated for a better understanding of the mechanism. Fat accumulation in the gut is not mechanistically linked with fat accumulation in the fat body. The function of lipase in the gut (esp. R2 region) should be addressed, e.g. by manipulating gut-lipases such as magro or Lip3 in the gut in the contest of trpγ mutant. Also, it is not clarified which cell types in the gut DH44R2 is expressed. The study also mentioned only in the text that bmm expression in the gut cannot restore lipid droplet enlargement in the fat body, but this result might be presented as a figure.

We appreciate the reviewer’s insightful suggestions. Unfortunately, due to the unviability of the reagent (UAS-Lip3), we were unable to manipulate gut lipase in trpy mutants as proposed. However, we additionally performed immunostaining to examine the co-expression of trpγ and Dh44R2 in the gut, and our results indicate that both trpγ and Dh44R2 are co-expressed in the R2 region of the gut (Figure 7O and P). Furthermore, we have updated our figures to address the point that bmm expression in the gut does not restore lipid droplet enlargement in the fat body, with the revised version (Figure 5I and J).

Reviewer #3 (Public Review):

In this manuscript, the authors demonstrated the significance of the TRPγ channel in regulating internal TAG levels. They found high TAG levels in TRPγ mutant, which was ascribed to a deficit in the lipolysis process due to the downregulation of brummer (bmm). It was notable that the expression of TRPγ in DH44+ PI neurons, but not dILP2+ neurons, in the brain restored the internal TAG levels and that the knockdown of TRPγ in DH44+ PI neurons resulted in an increase in TAG levels. These results suggested a non-cell autonomous effect of Dh44+PI neurons. Additionally, the expression of the TRPγ channel in Dh44 R2-expressing cells restored the internal TAG levels. The authors, however, did not provide an explanation of how TRPγ might function in both presynaptic and postsynaptic cells in the non-cell autonomous manner to regulate the TAG storage. The authors further determined the effect of TRPγ mutation on the size of lipid droplets (LD) and the lifespan and found that TRPγ mutation caused an increase in the size of LD and a decrease in the lifespan, which were reverted by feeding lipase and metformin. These were creative endeavors, I thought. The finding that DH44+ PI neurons have non-cell autonomous functions in regulating bodily metabolism (mainly sugar/lipid) in addition to directing sugar nutrient sensing and consumption is likely correct, but the paper has many loose ends. I would like to see a revision that includes more experiments to tighten up the findings and appropriate interpretations of the results.

(1) The authors need to provide interpretations or speculations as to how DH44+ PI neurons have non-cell autonomous functions in regulating the internal TAG stores, and how both presynaptic DH44 neurons and postsynaptic DH44 R2 neurons require TRPγ for lipid homeostasis.

In Discussion, we had mentioned our previous finding. “ We previously proposed that TRPg holds DH44 neurons in a state of afterdepolarization, thus reducing firing rates by inactivating voltage-gated Na+ channels (Dhakal et al., 2022). At the physiological level, this induces the consistent release of DH44 and depletion of DH44 stores, resulting in nutrient utilization and storage malfunctions.”

We also included the following: “TRPg in DH44 neurons may influence the release of metabolic signals or hormones that act on postsynaptic DH44R2 cells. These postsynaptic cells could, in turn, modulate lipid storage and metabolism in a non-cell autonomous manner. However, the mechanism by which TRPg functions in DH44R2 cells remains unclear. One possible explanation is that TRPg in the gut may be activated by stretch or osmolarity (Akitake et al. 2015).” lines 439-440.

This interaction between presynaptic and postsynaptic cells may ensure a coordinated response to metabolic changes and maintain lipid homeostasis. Thus, both Dh44-expressing and Dh44-R2-expressing cells are crucial for the proper functioning of TRPγ in regulating internal TAG levels and lipid storage.

(2) The expression of TRPγ solely in DH44 R2 neurons of TRPγ mutant flies restored the TAG phenotype, suggesting an important function mediated by TRPγ in DH44 R2 neurons. However, the authors did not document the endogenous expression of TRPγ in the DH44R2+ gut cells. This needs to be shown.

We appreciate the reviewer’s suggestion. To address this, we performed immunostaining to examine the expression of TRPγ in the DH44R2+ gut cells. Our results, as shown in Figure 7 O and P, confirm that TRPγ is co-expressed in the Dh44R2+ cells in the gut. We also found that Dh44R2 is expressed in the brain as well. We documented this part like the following: “Given that Dh44R2 is predominantly expressed in the intestine, we performed immunostaining to examine whether Dh44R2 co-localizes with trpg in gut cells. Our results confirmed that Dh44R2 and trpg are co-expressed in intestinal cells (Figure 7O and P). Additionally, we analyzed Dh44R2 expression in the brain and found that two Dh44R2-expressing cells are co-localized with Dh44-expressing cells in the PI region (Figure 7Q). To further delineate whether Dh44R2-mediated fat utilization is specific to the brain, gut, or fat body, we knocked down Dh44R2^RNAi using Dh44-GAL4, myo1A-GAL4, and cg-GAL4, respectively (Figure 7–figure supplement 1E). Notably, knockdown of Dh44R2 with Myo1A-GAL4 resulted in elevated TAG levels, indicating that DH44R2 activity in lipid metabolism is specific to the gut.” lines 375-384.

(3) While Dh44 mutant flies displayed normal internal TAG levels, Dh44R2 mutant flies exhibited elevated TAG levels (Figure 7A). This suggested that the lipolysis phenotype could be facilitated by a neuropeptide other than Dh44. Alternatively, a Dh44 neuropeptide-independent pathway could mediate the lipolysis. In either case, an additional result is needed to substantiate either one of the hypotheses.

The Dh44 mutant flies exhibited normal TAG levels, whereas Dh44R2 mutant flies showed elevated TAG levels. However, when we examined the lipid droplets in the fat body, both Dh44 mutant and Dh44R2 mutant flies displayed larger lipid droplets, indicating a disruption in lipid metabolism. Additionally, we assessed starvation survival time and found that both Dh44 and Dh44R2 mutant flies exhibited reduced survival under starvation conditions compared to controls. Supplementation with lipase (Figure 7–figure supplement 1A), glycerol (Figure 7–figure supplement 1B), hexanoic acid (Figure 7–figure supplement 1C), and mixed TAGs (Figure 7–figure supplement 1D) improved starvation survival time, further supporting that the lipid metabolism pathway was impaired in both mutants. These observations highlight the role of Dh44 in regulating lipolysis. We included related Discussion: “There is an inconsistency of total TAG levels and the LD size observed in the Dh44 mutant. This inconsistency raises a possibility that the signaling pathway from DH44 release to its receptor DH44R2 only accounts for part of the lipid metabolic process under starvation. While Dh44 mutant flies displayed normal internal TAG levels, Dh44R2 mutant flies exhibited elevated TAG levels. This suggested that the lipolysis phenotype could be facilitated by a neuropeptide other than DH44. Alternatively, a DH44 neuropeptide-independent pathway could mediate the lipolysis.” lines 429-436.

(4) While the authors observed an increased area of fat body lipid droplets (LD) in Dh44 mutant flies (Figure 7F), they did not specify the particular region of the fat body chosen for measuring the LD area.

We have chosen the 2-3 segment in the abdomen for all fat body images, which we already mentioned in Nile red staining in the Method section line 630-631.

(5) The LD area only accounts for TAG levels in the fat body, whereas TAG can be found in many other body parts, including the R2 area as demonstrated in Figure 5A-D using Nile red staining. As such, measuring the total internal TAG levels would provide a more accurate representation of TAG levels than the average fat body LD area.

We have measured total internal TAG level in whole body throughout the experiments (Figure 1F, 2C, 2E, 3C, 3G, 4A, 4B, 7A, 7I, and many Supplementary Figures) except bmm expression using GAL4/UAS system. Now we include this new data in Figure 5–figure supplement 1) which is the same conclusion with LD analysis.

(6) In Figure 5F-I, the authors should perform the similar experiment with Dh44, Dh44R1, and Dh44R2 mutant flies.

We did the experiments with Dh44, Dh44R1, and Dh44R2 mutant flies and we found that Dh44 and Dh44R2 mutant flies showed reduced starvation survival time than control and which was increased after supplementation of lipase, glycerol, hexanoic acid and TAG (Figure 7– figure supplement 1A–D). lines 361-372.

(7) The representative image in Figure 6B does not correspond to the GFP quantification results shown in Figure 6C. In trpr1;bmm::GFP flies, the GFP signal appears stronger in starved conditions than in satiated conditions.

We updated it with new images. We quantified GFP intensity level using image J and found that GFP intensity level was significantly lower in starved condition in trpγ¹;bmm::GFP flies than sated condition.

(8) In Figure 6H-I, fat body-specific expression of bmm reversed the increased LD area in TRPγ mutants. The authors also showed that Dh44+PI neuron-specific expression of bmm yielded a similar result. The authors need to provide an interpretation as to how bmm acts in the fat body or DH44 neurons to regulate this.

We first inserted the following in results: “Furthermore, the expression of bmm in the fat body, as well as Dh44 neurons in the PI region, can promote lipolysis at the systemic level.” lines 276-277.

Additionally, we discussed it in the Discussion: “Brummer lipase is essential for regulating lipid levels in the insect fat body by mediating lipid mobilization and energy homeostasis. In Nilaparvata lugens, it facilitates triglyceride breakdown (Lu et al., 2018), while studies in Drosophila show that reduced Brummer lipase expression decreases fatty acids and increases diacylglycerol levels, highlighting its role in lipid metabolism (Nazario-Yepiz et al., 2021). Here, we additionally demonstrate that bmm expression in DH44 neurons within the PI region can systemically regulate TAG levels. Cell signaling or energy status in DH44 neurons may contribute to hormonal release that targets organs such as the fat body.” lines 451-459.

(9) The authors should explain why the DH44 R1 mutant did not represent similar results as the wild type.

We added “In addition, bmm levels in Dh44R1^Mi under starved condition did not increase as significantly as in the control. This suggests a unique role of DH44 and its receptors in regulating lipid metabolism and response to nutritional status in Drosophila.” lines 358-360.

(10) It would be good to have a schematic that represents the working model proposed in this manuscript.

We updated the schematic model in revised version (Figure 8).

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

This paper characterized the function of trpγ in Dh44-expressing PI neurons for lipid metabolism and lipolysis induced by prolonged starvation. The authors applied a series of lipolytic genetic manipulation and lipid/lipid metabolism supplements to rescue the trpγ deficits in lipolysis: the expression of active AMPK in the DH44-expressing PI neurons or brummer, a lipolytic gene, in the trpγ-expressing cells, and oral administration of the anti-diabetic drug metformin, lipase, TAG and free fatty acids. Despite this exhaustive characterization of the defective lipolysis in the trpγ mutants, there remain puzzles in inconsistent defects of Dh44 and DH44R2 in the total TAG levels and in the expression and functions of the receptor in the gut. Clarification of these points and other issues raised by the reviewers should improve the mechanisms of lipid metabolism through Dh44 signalling.

Reviewer #1 (Recommendations For The Authors):

(1) It might be worth introducing Dh44 in the introduction section as it is unclear to readers how the authors hypothesized the site-of-action of TRPγ in Dh44 neurons for lipid metabolism after reading the introduction.

We introduced the following: “We found that TRPg expression in Dh44 neuroendocrine cells in the brain is critical for maintaining normal carbohydrate levels in tissues (Dhakal et al. 2022). Building on this, we hypothesized that TRPg in Dh44 cells also regulates lipid and protein homeostasis.” lines 69-71.

(2) Providing a summary model in the end to integrate the present findings and their previous publication about TRPγ functions in Drosophila sugar selection would greatly help readers understand and appreciate the general role of TRPγ in balancing energy homeostasis.

We made a schematic model in Figure 8.

(3) Swapping the order of Figures 5 and 6 might be a better way to tell the story without logic gaps. The results addressing the mechanisms of metformin and TRPγ in promoting lipolysis under starvation are interrupted by the lipid storage data in the R2 cells in the current Figure 5A-5E. In addition, presenting Figure 5A-5E before or together with Figure 7 will help readers appreciate the expression of Dh44-R2 and its function in regulating lipid metabolism in Figure 7.

We did.

(4) It might be misleading to use the word "sated" for the condition of 5-hour mild starvation. The word "mild starvation" or the equivalents might be a better word choice.

We appreciate the reviewer’s concern. As hemolymph sugar level does not drop down significantly in 5 hr starvation, the previous papers (Dus et al 2015, Dhakal et al 2022) indicated it as sated condition. To use the word consistently, we prefer using “sated” instead of “mild starvation”.

(5) It is unclear what the white arrows are pointing at in Figures 7O and 7P. Some of those seem to be non-specific signals, so it is hard to connect the figure to the conclusion in Lines 351-353. It would be helpful to add some explanations to help readers interpret Figures 7O and 7P.

In the previous version, Figure 7O and 7P white arrows represented the expression of Dh44R2 in the SEZ region of the brain and R2 region of the gut. In revised version, to make clear, we performed additional immunostaining for the co-expression of trpγ and Dh44R2 in the gut. We found that trpγ and Dh44R2 co-expressed at the R2 region of the gut specifically (Figure 7O and P). Similarly, we found that two cells of Dh44R2 co-expressed in Dh44 cells in the PI region of the brain (now Figure 7Q). We updated this part. lines 375-380.

(6) The figure legend for the (G) panel in Figure 2-figure Supplement 1 was mislabeled as (F).

We corrected it.

(7) In Line 85, the authors might want to write "… among these mutants, only trpγ mutant displayed reduced carbohydrate levels, suggesting …". Please confirm the information for the sentence. lines 87-88.

We clarified it.

Reviewer #2 (Recommendations For The Authors):

(1) The trpγ[G4] would be difficult for non-Drosophila researchers to understand; it would be better to use trpγ-Gal4.

We got the mutant line from Dr. Craig Montell who named it. We explained it like the following in the main text: “controlled by GAL4 knocked into the trpg locus (trpg^G4 flies; +)” line 109.

(2) The arrows in Figures 7O and 7P need to be explained in the figure legends.

We did.

Reviewer #3 (Recommendations For The Authors):

(11) Lines 95-96 should have a reference.

We did.

(12) Lines 129-130: It should read "TRPγ expressed in DH44 cells is sufficient for the regulation of lipid levels."

We changed it as suggested.

(13) Figure 5E needs to be repeated with more trials.

We increased the n numbers. Previously (Figure 5E) we included area of 10 LDs from 3 samples, and in revised figure (Figure 6I) we have included 28 LDs from 10 samples.

(14) Figures 5F-I, bold lines are not too visible and therefore, dotted lines could be used.

We changed it as suggested.

(15) Line 356: It is not true that D-trehalose or D-fructose is commonly detected by DH44 neurons. These sugars at concentrations much higher than the physiological concentration range stimulate DH44 neurons (see Dus et al., 2015).

We removed it.

(16) Lines 362-363: It should read "Expression of TRPγ in DH44 neurons was necessary and sufficient to regulate the carbohydrate and lipid levels.".

We changed it.

(17) Lines 369-370: The authors need to consider removing the possible role of CRF in regulating lipid homeostasis. It could be considered to be far-fetched.

We removed it.

(18) Line 407-408: the sentence "Nevertheless, it is also known that DH44 neurons mediate the influence of dietary amino acids on promoting food intakes in flies (37)" needs to be removed. They used amino acid concentrations that were far greater than the physiological levels observed in the internal milieu of flies. Still, many laboratories cannot reproduce the result of using the high AA concentrations.

We removed it.

eLife Assessment

This study provides an important computational tool for analyzing and deconvoluting a pool of plasmids sequenced without barcoding using nanopore long-read sequencing. The tool, which has been convincingly validated, is readily available to scientists interested in rapid and cost-effective verification of plasmid sequences as well as in scaling up analysis by pooling samples within barcodes.

Reviewer #1 (Public review):

This manuscript presents SAVEMONEY, a computational tool designed to enhance the utilization of Oxford Nanopore Technologies (ONT) long-read sequencing for the design and analysis of plasmid sequencing experiments. In the past few years, with the improvement in both sequencing length and accuracy, ONT sequencing is being rapidly extended to almost all omics analyses which are dominated by short-read sequencing (e.g., Illumina). However, relatively higher sequencing errors of long-read sequencing techniques including PacBio and ONT is still a major obstacle for plasmid/clone-based sequencing service that aims to achieve single base/nucleotide accuracy. This work provides a guideline for sequencing multiple plasmids together using the same ONT run without molecular barcoding, followed by data deconvolution. The whole algorithm framework is well-designed, and some real data and simulation data are utilized to support the conclusions. The tool SAVEMONEY is proposed to target users who have their own ONT sequencers and perform library preparation and sequencing by themselves, rather than relying on commercial services. As we know and discussed by the authors, in the real world, to ensure accuracy, the researchers will routinely pick up multiple colonies in the same plasmid construction and submit for Sanger sequencing. However, SAVEMONEY is not able to support the simultaneous analysis of multiple colonies in the same run, as compared to the barcoding-based approaches. This is a major limitation in the significance of this work. Encouraging computational efforts in ONT data debarcoding for mixed-plasmid or even single-cell sequencing would be more valuable in the field.

Comments on revisions:

My previous concerns have been addressed, and the revised manuscript has been significantly approved.

Reviewer #2 (Public review):

The authors developed an algorithm that allows to deconvolute plasmid sequences from a mixture of plasmids that have been sequenced by nanopore long read technology. As library preparations and barcoding of individual samples increases sequencing costs, the algorithm bypasses this need and thus decreases time on sample prep and sequencing costs. In a first step, the tool assesses which of the plasmid constructions can be mixed in a single library preparation by calculating a distance matrix between the reference plasmid and the constructions producing sequence clusters. The user is given groups of plasmids, from different clusters, to be pooled together for sequencing. After sequencing, the algorithm deconvolutes the reads by classifying them based on alignments to the reference sequence. A Bayesian analysis approach is used to obtain a consensus sequence and quality scores.

Strengths

The authors exploit one of the main advantages of long read sequencing that is to accurately resolve regions of high complexity, as regularly found in plasmids, and developed a tool that can validate plasmid constructions by reducing sequencing costs. Multiple plasmids (up to six) can be analyzed simultaneously in a single library without the need of sample barcoding, also reducing sample preparation time. Although inserts must be different, just 2 bases difference would be enough for correct assignation. Maximizes cost-efficiency for projects that require large amounts of plasmid constructions and high-throughput validation. The algorithm also allows for linear DNA analysis offering extra flexibility.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (public review): 

This manuscript presents SAVEMONEY, a computational tool designed to enhance the utilization of Oxford Nanopore Technologies (ONT) long-read sequencing for the design and analysis of plasmid sequencing experiments. In the past few years, with the improvement in both sequencing length and accuracy, ONT sequencing is being rapidly extended to almost all omics analyses which are dominated by short-read sequencing (e.g., Illumina). However, relatively higher sequencing errors of long-read sequencing techniques including PacBio and ONT is still a major obstacle for plasmid/clone-based sequencing service that aims to achieve single base/nucleotide accuracy. This work provides a guideline for sequencing multiple plasmids together using the same ONT run without molecular barcoding, followed by data deconvolution. The whole algorithm framework is well-designed, and some real data and simulation data are utilized to support the conclusions. The tool SAVEMONEY is proposed to target users who have their own ONT sequencers and perform library preparation and sequencing by themselves, rather than relying on commercial services. As we know and discussed by the authors, in the real world, to ensure accuracy, the researchers will routinely pick up multiple colonies in the same plasmid construction and submit for Sanger sequencing. However, SAVEMONEY is not able to support the simultaneous analysis of multiple colonies in the same run, as compared to the barcoding-based approaches. This is a major limitation in the significance of this work. Encouraging computational ePorts in ONT data debarcoding for mixed-plasmid or even single-cell sequencing would be more valuable in the field. 

We thank the reviewer for the positive response to our manuscript and the helpful comments.

The tool SAVEMONEY is proposed to target users who have their own ONT sequencers and perform library preparation and sequencing by themselves, rather than relying on commercial services.

We apologize that we were not clear enough in the manuscript. Our tool is designed for users who rely on commercial services (i.e., those who cannot include a barcode by themselves). However, it can also benefit those performing library preparation, as SAVEMONEY can be applied after standard barcode-based sequencing and de-multiplexing. The combination of standard barcodes with SAVEMONEY would significantly expands the scope of sequencing applications. For example, it would enable sequencing of more plasmid types than the number of available barcodes and, in some cases, it may even eliminate the need for barcode introduction. Because we do not own ONT equipment and because the primary target audience for the SAVEMONEY algorithm are users without ONT equipment, we were not able to conduct experiments using ONT. However, to clarify these possibilities, we added a dedicated paragraph describing these issues (3rd paragraph in the discussion section).

However, SAVEMONEY is not able to support the simultaneous analysis of multiple colonies in the same run, as compared to the barcoding-based approaches.

We agree with the reviewer about this limitation of SAVEMONEY, as it does not allow mixing of plasmids from multiple colonies in the same cloning run. However, that does not necessarily mean that SAVEMONEY cannot reduce sequencing costs in cloning. For example, when sequencing two colonies from each of three diPerent constructs (six plasmids in total), the standard approach would require sequencing costs for six samples. However, with SAVEMONEY, up to three plasmids can be mixed per sample, allowing them to be sequenced as just two samples. As a result, the sequencing cost per plasmid is reduced to one-third. The greatest benefits can be realized when SAVEMONEY is used at the laboratory level or by multiple researchers. To make this point clearer, we have added sentences in the 5th paragraph of the discussion section.

(1) To provide more comprehensive information for users who care about the cost, the Introduction section should include a cost comparison between Sanger and ONT, with more details, such as diPerent ONT platforms (MinION, PromethION, FlongIe), chemistries (flow cells) and kits. This additional information will be more helpful and informative for the users who have their own sequencers and are the target audience for SAVEMONEY. 

We thank the reviewer for pointing this out. Since we do not own ONT equipment, we are unable to provide a total cost for using the ONT platform. However, we have included the price per sample (~$15 per plasmid) for the commercial service we have used, as well as the equipment that they employ (V14 chemistry on a PromethION with an R10.4.1 flow cell) and the number of reads obtained per plasmid (~100–1000) in the 4th paragraph of the introduction section.     Though these costs will inevitably change over time, this information should still be helpful for those who own ONT sequencers in estimating the costs.

(2) In "Overview of the algorithm" (Pages 3-4) under the Results section, instead of stating "However, coverage varies from ~100-1000 and is diPicult to predict because each nanopore flow cell has diPerent properties.", it will be beneficial to provide more detailed information, such as sequencing length, yield/read count per flow cell of diPerent platforms. This information will assist users in designing their own experiments ePectively. 

We thank the reviewer for the comment. As mentioned in the previous response, we are unable to provide sequencing length, yield/read count per flow cell because we do not own ONT equipment. However, we apologize if it was not clear in "Overview of the algorithm" section that we are discussing the use of results obtained from commercial services, and therefore we need to provide more detailed information about the results from the commercial service. We have now clarified in the sentence pointed out by the reviewr that the numbers are derived from the information provided by commercial sequencing services. In addition, we have also added that typical examples of the result properties, i.e., read length and quality score distribution, can be found in Fig. 2 at the end of the same paragraph.

(3) While this study optimized and evaluated the tool using a total of 14 plasmids, it may not provide suPicient power to represent the diversity of the plasmid world. Consideration should be given to expanding the dataset to include a broader range of plasmids in future studies to enhance the robustness and generalizability of the tool. 

We are grateful to the reviewer for their valuable input. It is very reasonable that we had to expect that a larger number of plasmids should be used, even though the main target of SAVEMONEY is those who utilize commercial services. In the previous version of SAVEMONEY, it was not possible to process in a reasonable amount of time if too many plasmids were provided, though the algorithm itself does not have no restrictions based on the number of plasmids. Therefore, we have changed the underlying code to improve the algorithm, making it more than 20 times faster than the previous version (the benchmark time mentioned in the 3rd paragraph of the discussion section was improved to 3.1 minutes from the previous 65 minutes, using the same dataset and the same computer). Additionally, SAVEMONEY is now compatible with multiprocessing. The processing time is expected to decrease approximately inversely proportional to the number of CPU cores used. We have added these updates at the end of the 3rd paragraph in the discussion section.

(4) If applicable and feasible, including a comparison or benchmark of SAVEMONEY against other similar tools would further strengthen the manuscript. This comparison would allow users to evaluate the advantages and disadvantages of diPerent tools for their specific needs. 

We thank the reviewer for the suggestion. We have added the benchmark using the similar tool, On-Ramp, with the exact same set of plasmids and FASTQ data used for our benchmark (4th paragraph in the discussion section). Because the machine specifications used in the On-Ramp web server are unknown, a direct comparison is not possible. However, using only laptop-level computational resources, SAVEMONEY was able to process the data 38% faster than On-Ramp. When using mini-PC level computational resources, the processing time was 64% faster than on-RAMP.

(5) The importance of pre-filtering raw sequencing reads should be emphasized as noisy reads can significantly impact the overall performance of the tool. It is essential to clarify whether any pre-filtering steps were performed in this study, such as filtering based on quality scores, read length, or other relevant factors. 

We apologize for not being clear. Unfortunately, the commercial sequencing service we used did not provide the information regarding pre-filtering. However, the impact of the quality of pre-filtering based on quality score and read length on the quality of the final results is theoretically minimal in SAVEMONEY. First, during the initial step of the post-analysis, the classification step, short reads compared to the full plasmid length can be excluded based on the user-defined “score_threshold”. Simultaneously, low-quality reads with poor alignment to the plasmid can also be excluded, because “score_threshold” is related to the normalized alignment score. Even if there are low-quality reads that are not excluded at this stage, the ePect can be minimized during the final step of the post-analysis that generates consensus sequences. This is because our Bayesian analysis considers not only the base calling but also the q-scores to determine the consensus. Therefore, we believe the overall impact of pre-filtering on the final results is negligible.

(6) The statement regarding the number of required reads per plasmid (20-30) and the maximum number of plasmids (up to six) that can be mixed in a single run may become outdated due to the rapid advancements in ONT technology. In the Discussion section, instead of assuming specific numbers, it would be more beneficial to provide information based on the current state of ONT sequencing, such as the number of reads per MinION flow cell that can be produced.

We thank the reviewer for pointing this out. Because the number of required reads per plasmid depends on the accuracy of each read (i.e., the number of required reads can be reduced if the accuracy increases), we have added the description of these points to the last paragraph of the discussion section.

Reviewer #2 (public review):  

The authors developed an algorithm that allows for deconvoluting of plasmid sequences from a mixture of plasmids that have been sequenced by nanopore long read technology. As library preparations and barcoding of individual samples increase sequencing costs, the algorithm bypasses this need and thus decreases time on sample prep and sequencing costs. In the first step, the tool assesses which of the plasmid constructions can be mixed in a single library preparation by calculating a distance matrix between the reference plasmid and the constructions producing sequence clusters. The user is given groups of plasmids, from diPerent clusters, to be pooled together for sequencing. After sequencing, the algorithm deconvolutes the reads by classifying them based on alignments to the reference sequence. A Bayesian analysis approach is used to obtain a consensus sequence and quality scores. 

Strengths 

The authors exploit one of the main advantages of long-read sequencing which is to accurately resolve regions of high complexity, as regularly found in plasmids, and developed a tool that can validate plasmid constructions by reducing sequencing costs. Multiple plasmids (up to six) can be analyzed simultaneously in a single library without the need for sample barcoding, also reducing sample preparation time. Although inserts must be diPerent, just 2 bases diPerence would be enough for a correct assignation. It maximizes cost-ePiciency for projects that require large amounts of plasmid constructions and highthroughput validation. 

We thank the reviewer for the positive response to our manuscript and the helpful comments.

Weaknesses 

The method proposed by the authors requires prior knowledge of plasmid sequences (i.e., blueprints or plasmid reference) and is not suitable for small experiments. The plasmid inserts or backbones must be diPerent e.g., multiple colonies from the same plasmid construction ePort cannot be submitted together. 

As also discussed in the response to reviewer 1, we agree with the reviewer that SAVEMONEY does not allow you the analysis of plasmids from multiple colonies in the same cloning experiment. However, that does not necessarily mean that SAVEMONEY cannot reduce the sequencing cost. For example, when sequencing two colonies from each of three diPerent constructs (six plasmids in total), the standard approach would require sequencing costs for six samples. However, with SAVEMONEY, up to three plasmids can be mixed per sample, allowing them to be sequenced as just two samples. As a result, the sequencing cost per plasmid is reduced to one-third. The greatest benefits can be realized when SAVEMONEY is used at the laboratory level or by multiple researchers. To make this point clearer, we have added sentences in the 5th paragraph of the discussion section.

The reviewer also expressed concern that SAVEMONEY is not suitable for experiments at a small scale. To put it more precisely, SAVEMONEY cannot be used when the experiment size is minimal, such as in a lab that consistently constructs only a single plasmid at a time. That said, the strength of SAVEMONEY lies in its scalability. Even in labs where plasmid construction is typically limited to one at a time, there may be occasional instances where two or more plasmids are created simultaneously. In such cases, SAVEMONEY can be used to reduce sequencing costs. Moreover, in a typical molecular biology lab where multiple plasmids are constructed every week, SAVEMONEY can be particularly ePective. Given its adaptability and cost-saving potential and widespread use since its initial publication on bioRxiv and on Google Colab, we are confident that SAVEMONEY will continue to be a valuable tool for a wide range of researchers.

Recommendations For The Authors:

Reviewer #2 (Recommendations For The Authors): 

The manucript assumes all samples are sent out for sequencing at a specific company. This could be generalized for a much broader use since many labs now own nanopore sequencers. In turn, the advantage of reducing hands-on sample prep becomes more evident. 

We thank the reviewer for pointing this out. We agree that SAVEMONEY can also benefit those performing library preparation. Combination of standard barcodes with SAVEMONEY significantly expands the scope of sequencing applications. For example, it enables sequencing of more plasmid types than the number of available barcodes and, in some cases, may even eliminate the need for the sample prep step to introduce barcode. Because we do not own ONT equipment, we could not conduct experiments using ONT. However, to clarify these possibilities, we added a dedicated paragraph (3rd paragraph in the discussion section).

The base calling model (high accuracy, super accuracy) used by Plasmidsaurus and tested here should be mentioned.  

We thank the reviewer for the suggestion. The description about the base calling model (HAC) was added in Materials and Methods section.

Other modifications to the revised manuscript 

Beyond changes made in response to reviewer comments above, we have also through our continued use and improvement of SAVEMONEY, made additional changes to the algorithm and therefore to the manuscript. Those changes are outlined below. Improvements in the pre-survey step

(1) The pre-survey algorithm was reduced to a Zero-One Integer Linear Programming Problem to guarantee the optimal combinations, as previous versions did not ensure an optimal solution. Relatedly, the explanation of the algorithm in the main manuscript was updated.

(2) The algorithm was modified to ensure that the number of plasmids distributed to each group is balanced. A new feature was also added to allow users to specify the number of groups, which is beneficial when balancing between cost and quality.

(3) An error was corrected in Fig. 2, where the distance calculation method for the hierarchical clustering step for group formation was Farthest Point Algorithm, which calculates distance between two clusters based on the farthest pair of plasmids. The correct method is the Nearest Point Algorithm. This error was present only in Fig. 2, while other implementations, including source code of SAVEMONEY and Google Colab page, were correct from the beginning. We have corrected the error in Fig. 2.

Modifications in figures, manuscripts, and other aspects

(1) Fig. 3 was updated to reflect the update of SAVEMONEY, although it did not show any important diPerences.

(2) Parameter names were updated as follows:

“threshold (pre)” -> “distance_threshold”

“threshold (post)” -> “score_threshold” Added “number_of_groups”

(3) The order of elements was rearranged in Fig. 4.

(4) Incorrect calculations were fixed in Fig. 4g, h, and i (old Fig. 4d, h, and l). Related to that, Fig. 4j, k, and l and Table 1 were added, in addition to the explanation in the main manuscript.

(5) SAVEMONEY was packaged and was released on PyPI to facilitate easy installation and integration by other developers.

(6) SAVEMONEY was updated and expanded to accommodate linear DNA fragments, such as PCR amplicons and long synthetic DNA. Users can select the topology of DNA by specifying that as an option. A description of this new capability was added at the end of “Overview of the algorithm” section.

eLife Assessment

This useful study reveals that as C. elegans, a poikilothermic ("cold-blooded") animal, adapt to cold (4ºC), they display a drastic reduction in translation (assessed by polysome profiling and SUNSET). The remaining translation (by ribo-seq) correlates with mRNA levels (by RNA-seq), and the changes in gene expression at least partially require IRE-1, an established endoplasmic reticulum stress sensor. The reviewers consider the data assessing global translation and RNA expression upon cold exposure and the data demonstrating the requirement of ire-1 to be solid, but the conclusion that "transcription" is the major regulatory step and "lipid changes" can be a signal for IRE-1 activation in cold adapted worms needs substantially more evidence. Overall, this study demonstrated a good correlation between translation and RNA levels and yielded an inventory of gene changes as C. elegans adapt to cold, and will be of general interest to researchers interested in stress response and cold adaptation.

Reviewer #2 (Public review):

Summary:

This study investigates cold induced states in C. elegans, using polysome profiling and RNA seq to identify genes that are differentially regulated and concluding that cold-specific gene regulation occurs at the transcriptional level. This study also includes analysis of one gene from the differentially regulated set, lips-11 (a lipase), and finds that it is regulated in response to a specific set of ER stress factors.

Strengths:

(1) Understanding how environmental conditions are linked to stress pathways is generally interesting.<br /> (2) The study used well-established genetic tools to analyze ER stress pathways.

Weaknesses:

(1) The conclusions regarding a general transcriptional response are based on a few genes, with much of the emphasis on lips-11, which does not affect survival in response to cold.

(2) Definitive conclusions regarding transcription vs translational effects would require the use of blockers such as alpha-amanitin or cyclohexamide. Although this may be beyond the scope of the study, it does affect the breadth of the conclusions that can be made.

(3) Conclusions regarding the role of lipids are based on supplementation with oleic acid or choline, yet there is no lipid analysis of the cold animals, or after lips-1 knockdown. Although choline is important for PC production, adding choline in normal PC could have many other metabolic impacts and doesn't necessarily implicate PC without lipidomic or genetic evidence. Although they note the caveats, their evidence falls short of proving a role in PC production.

Reviewer #3 (Public review):

Summary:

The authors sought to understand the molecular mechanisms that cells use to survive cold temperatures by studying gene expression regulation in response to cold in C. elegans. They determined whether gene expression changes during cold adaptation occur primarily at the transcriptional level and identified specific pathways, such as the unfolded protein response pathway, that are activated to possibly promote survival under cold conditions.

Strengths:

Effective use of bulk RNA sequencing (RNA-seq) to measure transcript abundance and ribosome profiling (ribo-seq) to assess translation rates, providing a comprehensive view of gene expression regulation during cold adaptation. This combined approach allows for correlation between mRNA levels and their translation, thereby offering evidence for the authors' conclusion that transcriptional regulation is the primary mechanism of cold-specific gene expression changes.

Weaknesses:

Many aspects of the weakness have been addressed by the revision. Still, the weak cold sensitivity phenotype observed in ire-1 mutants suggests the ER-UPR pathway's role is likely minor, modulatory or there is an unknown compensatory mechanism responsible for surviving cold.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1:

(…) some concerns with interpretations and technical issues make several major conclusions in this manuscript less rigorous, as explained in detail in comments below. In particular, the two major concerns I have: 1) the contradiction between the strong reduction of global translation, with puromycin incorporation gel showing no detectable protein synthesis in cold, and an apparently large fraction of transcripts whose abundance and translation in Fig. 2A are both strongly increased. 2) The fact that no transcripts were examined for dependance on IRE-1/XBP1 for their induction by cold, except for one transcriptional reporter, and some weaknesses (see below) in data showing activation of IRE-1/XBP-1 pathway. The conclusion for induction of UPR by cold via specific activation of IRE-1/XBP-1 pathway, in my opinion, requires additional experiments.

Relating to the first point, the results of puromycin incorporation and ribosome profiling are not contradictory. The former shows absolute changes in translation, i.e. changes in how much protein the cell is producing, while the latter shows relative changes between the produced proteins, i.e. how the cell prioritizes its protein production. An observed up-regulation in ribosome profiling does not necessarily mean (but could) that the corresponding protein goes up in absolute terms (units produced per time). Instead, it implies that out of the population of all translating ribosomes, a larger fraction is translating (prioritizing) this particular mRNA relative to other mRNAs. The second point is addressed later in the response.

Major concerns:

(1) Fig. 1B shows polysomes still present on day 1 of 4ºC exposure, but the gel in Fig. 1C suggests a complete lack of protein synthesis. Why?

We realized that the selected gel exposure may give the false impression of a complete lack of puromycin incorporation at 4ºC. To avoid confusion, we now show in Figure 1 – figure supplement 1 the original gel image next to its longer exposure. The quantification of puromycin incorporation remains in Fig. 1C (it is based on 3 biological replicates and only one replicate is shown in the corresponding supplement). We hope it is now clear that there is an ongoing puromycin incorporation/translation at 4ºC, albeit much reduced compared with 20ºC.

What is then the evidence that ribosomal footprints used in much of the paper as evidence of ongoing active translation are from actual translating rather than still bound to transcripts but stationary ribosomes, considering that cooling to 4ºC is often used to 'freeze' protein complexes and prevent separation of their subunits? The authors should explain whether ribosome profiling as a measure of active translation has been evaluated specifically at 4ºC, or test this experimentally.

While the ribosomal profiling alone might not prove ongoing translation, the residual puromycin incorporation does (see the longer gel exposure in Figure 1 – figure supplement 1). To strengthen this argument, we selected two additional genes (cebp-1 and numr-1) whose ribosomal footprints increase in the cold, and whose GFP-fusions were available from the CGC. Monitoring their expression, we observed the expected increase in the cold (see Figure 2 – figure supplement 3 A-B). The ongoing translation in the cold is also in line with our previous study (Peke et al., 2022), where we observed de novo protein synthesis of other proteins under the same cooling conditions as in this study.

They should also provide some evidence (like Western blots) of increases in protein levels for at least some of the strongly cold-upregulated transcripts, like lips-11.

As explained above, we addressed it by additionally examining two strains expressing GFP-fused proteins, whose translation in the cold is predicted to increase according to our ribosomal profiling data. See the new Figure 2 – figure supplement 3 A-B.

As puromycin incorporation seems to be the one direct measure of global protein synthesis here, it conflicts with much of the translation data, especially considering that quite a large fraction of transcripts have increased both mRNA levels and ribosome footprints, and thus presumably increased translation at 4ºC, in Fig. 2A.

We hope the above explanations put this concern to rest.

Also, it is not clear how quantitation in Fig. 1C relates to the gel shown, the quantitation seems to indicate about 50-60% reduction of the signal, while the gel shows no discernable signal.

A above, see a longer western blot exposure in Figure 1 – figure supplement 1 and note that the quantification is based on three biological replicates.

(2) It is striking that plips-11::GFP reporter is induced in day 1 of 4ºC exposure, apparently to the extent that is similar to its induction by a large dose of tunicamycin (Fig. 3 supplement),

We did not intend to compare the extend of induction between cold and tunicamycin treatment. The tunicamycin experiment was meant to confirm that, as suggested by expression data from Shen et al. 2005, lips-11 is upregulated upon UPR activation.

…but the three IRE-1 dependent UPR transcripts from Shen 2005 list were not induced at all on day 1 (Fig. 4 supplement). Moreover, the accumulation of the misfolded CPL-1 reporter, that was interpreted as evidence that misfolding may be triggering UPR at 4ºC, was only observed on day 1, when the induction of the three IRE-1 targets is absent, but not on day 3, when it is stronger. How does this agree with the conclusion of UPR activation by cold via IRE-1/XBP-1 pathway?

In the originally submitted supplemental figure, we compared mRNA levels between day 1 animals at 20ºC versus 4ºC. However, as argued later by this reviewer, it may be better to use day 0 animals at 20ºC as the reference (since at 20ºC the animals will continue producing embryos). Thus, we repeated the RT-qPCR analysis with additional time points (and genes relevant to other comments). This analysis, now in Figure 4 – figure supplement 2, shows that these mRNAs (dnj-27, srp-7, and C36B7.6) increased already at day 1 in the cold compared with the reference 20ºC animals on day 0, and their levels increased further on day 3.

It is true that the authors do note very little overlap between IRE-1/XBP-1-dependent genes induced by different stress conditions, but for most of this paper, they draw parallels between tunicamycin-induced and cold induced IRE-1/XBP-1 activation.

We carefully re-examined the manuscript to ensure that we do not draw parallels between cold and tunicamycin treatment. The three genes (dnj-27, srp-7, and C36B7.6) were taken from Shen et al. because that study reported lips-11 as an IRE-1-responsive gene, which we realized thanks to the Wormbase annotation of lips-11. Examining the three genes in our expression data, srp-7 (like lips-11) is also upregulated more than 2-fold, while the other two genes go up but less than 2-fold. As mentioned by the reviewer, we note little overlap between the different stress conditions suggesting that the response is context dependent. Additional differences may arise if, as we hypothesize, UPR is activated in the cold in response to both protein and lipid stress. Note that the 2-fold cutoff used in the previous Figure 7 – figure supplement 1 was (erroneously) on the log2 scale, so showed genes upregulated at least 4-fold. We now corrected it to 2-fold. While there are now a few more overlapping genes, the overall conclusion, that there is little overlap between different conditions, did not change. We now list the shared genes in the new Supplementary file 5.

The conclusion that "the transcription of some cold-induced genes reflects the activation of unfolded protein response (UPR)..." is based on analysis of only one gene, lips-11. No other genes were examined for IRE-1 dependence of their induction by cold, neither the other 8 genes that are common between the cold-induced genes here and the ER stress/IRE-1- induced in Shen 2005 (Venn diagram in Figure 7 supplement), nor the hsp-4 reporter. What is the evidence that lips-11 is not the only gene whose induction by cold in this paper's dataset depends on IRE-1? This is a major weakness and needs to be addressed.

Furthermore, whether induction by cold of lips-11 itself is due to IRE1 activation was not tested, only a partial decrease of reporter fluorescence by ire-1 RNAi is shown. A quantitative measure of the change of lips-11 transcript in ire-1 and xbp-1 mutants is needed to establish if it depends on IRE-1/XBP-1 pathway.

We now examined by RT-qPCR if the induction of the three genes from Shen at al. (dnj-27, srp-7, and C36B7.6), as well as lips-11 and hsp-4 depends on IRE-1. In the new Figure 4 – figure supplement 2, we show that the upregulation of all these genes is reduced in the cold in the ire1 mutant (although in the wild type, the increase of hsp-4 mRNA appeared to be non-significant, despite the observed upregulation of the hsp-4 GFP reporter).

The authors could provide more information and the additional data for the transcripts upregulated by both ER stress and cold, including the endogenous lips-11 and hsp-4 transcripts: their identity, fold induction by both cold and ER stress, how their induction is ranked in the corresponding datasets (all of these are from existing data), and do they depend on IRE-1/XBP-1 for induction by cold?

As above, the dependence of endogenous lips-11 and hsp-4 on IRE-1 is now shown in the new Figure 4 – figure supplement 2, and the shared genes from Figure 7 – figure supplement 1 are listed in the new Supplementary file 5. We did not perform additional analysis comparing various data sets, as we felt that understanding the differences between IRE-1-mediated transcription outputs across different conditions goes well beyond this study.

Without these additional data and considering that the authors did not directly measure the splicing of xbp-1 transcript (see comment for Fig. 3 below), the conclusion that cold induces UPR by specific activation of IRE-1/XBP-1 pathway is premature.

To address the splicing of endogenous xbp-1, we examined our ribosome profiling data for the translation of spliced xbp-1, and found that the spliced variant is more abundant in the cold. This data is now shown in Figure 3 – figure supplement 2B.

There are also technical issues that are making it difficult to interpret some of the results, and missing controls that decrease the rigor of conclusions:

(1) For RNAseq and ribosome occupancy, were the 20ºC day 1 adult animals collected at the same time as the other set was moved to 4ºC, or were they additionally grown at 20ºC for the same length of time as the 4ºC incubations, which would make them day 2 adults or older at the time of analysis? This information is only given for SUnSET: "animals were cultivated for 1 or 3 additional days at 4ºC or 20ºC".

In the RNAseq experiments, the 20ºC animals were collected at the same time as the others were moved to 10ºC (and then 4ºC), so they were not additionally grown at 20ºC. We make it now clear in Methods.

This could be a major concern in interpreting translation data: First, the inducibility of both UPR and HSR in worms is lost at exactly this transition, from day 1 to day 2 or 3 adults, depending on the reporting lab (for example Taylor and Dillin 2013, Labbadia and Morimoto, 2015, De-Souza et al 2022).

As explained above, the 20ºC animals were collected at the same time as the others were moved to 4ºC. Then, we reported before that ageing appears to be suppressed in animals incubated at 4ºC (Habacher et al., 2016; Figure S1C). Thus, it terms of their biological age, cold-incubated animals appear to be closer to the 20ºC animals at the time they are moved to the cold (day 0). Thus, the ageing-associated deterioration in UPR inducibility mentioned above presumably does not apply to cold-incubated animals, which is in line with the observed IRE-1-dependent upregulation of several genes in day 3 animals at 4ºC.

How do authors account for this? Would results with reporter induction, or induction of IRE-1 target genes in Fig. 4, change if day 1 adults were used for 20ºC?

Our analysis in Figure 4 – figure supplement 2 now includes 20ºC animals at day 0, 1, and 3.

Second, if animals at the time of shift to 4ºC were only beginning their reproduction, they will presumably not develop further during hibernation, while an additional day at 20ºC will bring them to the full reproductive capacity. Did 4ºC and 20ºC animals used for RNAseq and ribosome occupancy have similar numbers of embryos, and were the embryos at similar stages?

As explained above, the reference animals at 20ºC were young adults containing few embryos. Indeed, at 4ºC the animals do not accumulate embryos. Although we cannot say that for all genes, note that the genes analysed in Figure 4 – figure supplement 2 increase in abundance also when compared with the day 3 animals kept at 20ºC.

(2) Second, no population density is given for most of the experiments, despite the known strong effects of crowding (high pheromone) on C. elegans growth. From the only two specifics that are given, it seems that very different population sizes were used: for example, 150 L1s were used in survival assay, while 12,000 L1s in SUnSET. Have the authors compared results they got at high population densities with what would happen when animals are grown in uncrowded plates? At least a baseline comparison in the beginning should have been done.

None of the experiments involved crowded populations. In the SUnSET experiments, we just used larger and more plates to obtain sufficient material.

(3) Fig. 3: it is unclear why the accepted and well characterized quantitative measure of IRE1 activation, the splicing of xbp-1transcript, is not determined directly by RT-PCR. The fluorescent XBP-1spliced reporter, to my knowledge, has not been tested for its quantitative nature and thus its use here is insufficient. Furthermore, the image of this fluorescent reporter in Fig. 3b shows only one anterior-most row of cells of intestine, and quantitation was done with 2 to 5 nuclei per animal, while lips-11 is induced in entire intestine. Was there spliced XBP-1 in the rest of the intestinal nuclei? Could the authors show/quantify the entire animal (20 intestinal cells) rather than one or two rows of cells?

As explained above, we now included the analysis of xbp-1 splicing in Figure 3 – figure supplement 2B. As for the fluorescent reporter, it is difficult to measure all gut nuclei since part of the gut is occluded by the gonad. Nonetheless, we do see induction of the reporter in other gut nuclei and show now additional examples from midgut in Figure 3 – figure supplement 2A.  

(4) The differences in the outcomes from this study and the previous one (Dudkevich 2022) that used 15ºC to 2ºC cooling approach are puzzling, as they would suggest two quite different IRE-1 dependent programs of cold tolerance. It would be good if authors commented on overlapping/non-overlapping genes, and provided their thoughts on the origin of these differences considering the small difference in temperatures.

Indeed, there seem to be substantial differences between different temperatures and cooling paradigms. While understanding the C. elegans responses to cold is still in its infancy, one possible explanation for the observed differences is that we used different starting growth temperatures. While the initial populations in our study were grown at 20ºC, Dudkevich et al. used 15ºC. Worms display profound physiological differences between these two temperatures. For example, Xiao et al. (2013) showed that the cold-sensitive TRPA-1 channel is important at 15ºC but not 20ºC. Thus, the trajectories along which worms adapt to near freezing temperature may vary depending on their initial physiological state (and perhaps the target temperature, as we used 4ºC and they 2ºC). We now expanded argumentation on this topic in Discussion. I should also say that we planned on testing NLP-3 function in our paradigm, but our request for strains remained unanswered.

Second, have the authors performed a control where they reproduced the rescue by FA supplementation of poor survival of ire-1 mutants after the 15ºC to 2ºC shift? Without this or another positive control, and without measuring change in lipid composition in their own experiments, it is unclear whether the different outcomes with respect to FAs are due to a real difference in adaptive programs at these temperatures, or to failure in supplementation?

While we did not re-examine the findings by Dudkevich et al., we did include now another positive control. As reporter by Hou et al. (2014), supplementing unsaturated FAs rescues the induction of the hsp-4 reporter in fat-6 RNAi-ed animals. Although we were able to reproduce that result (Figure 6 – figure supplement 1), the same supplementation procedure did not suppress the lips11 reporter (Figure 6 – figure supplement 2).

(5) Have the authors tested whether and by how much ire-1(ok799) mutation shortens the lifespan at 20ºC? This needs to be done before the defect in survival of ire-1 mutants in Fig. 7a can be interpreted.

The lifespan at standard cultivation temperature was examined by others (Henis-Korenblit et al., 2010; Hourihan et al., 2016), showing that ire-1(ok799) mutants live shorter. However, while some mechanism that prolong lifespan may also improve cold survival, the two phenomena are not identical and whether IRE-1 facilitates longevity and cold survival in the same or different way remains to be seen.

Reviewer #2:

(1) The conclusions regarding a general transcriptional response are based on one gene, lips-11, which does not affect survival in response to cold. We would suggest altering the title, to replace "Reprograming gene expression: with" Regulation of the lipase lips-11".

We now examined IRE-1 dependent induction of additional genes – see Figure 4 – figure supplement 2. While we do not know what fraction of cold-induced genes depends on IRE-1, we feel that our findings justify the statement that that gene expression in the cold involves the IRE1/XBP-1 pathway (title) or that that the transcription of some/a subset of cold-induced genes depend on this pathway (in abstract, model, and discussion).

(2) There is no gene ontology with the gene expression data.

We now included the top 10 most enriched and suppressed gene categories between 10ºC and 4ºC (since the biggest change happens between these conditions, as shown in Figure 2 – figure supplement 1A). This is now included in the Figure 2 – figure supplement 2.

(3) Definitive conclusions regarding transcription vs translational effects would require use of blockers such as alpha amanatin or cyclohexamide.

As explained also for reviewer 1, we confirmed now that at least some genes, whose translation is upregulated based on the ribosome profiling, are indeed upregulated in the cold at the protein level (Figure 2 – figure supplement 3A-B). Thus, the increase in ribosomal occupancy seems to accurately reflect increased translation. Since mRNA levels correlate overall with the ribosomal occupancy, it appears that the mRNA levels are the main determinants of the translation output. Because the lips-11 promoter is sufficient to upregulate the GFP reporter in the cold, it further suggests that the regulation happens at the transcription level. It is true that at this point we cannot completely rule out the effects of mRNA stability, which we clearly acknowledge in the discussion.

(4) Conclusions regarding the role of lipids are based on supplementation with oleic acid or choline, yet there is no lipid analysis of the cold animals, or after lips-1 knockdown.

We agree that this is an important direction for future studies but feel that lipidomic analysis goes beyond the scope of current work.

Although choline is important for PC production, adding choline in normal PC could have many other metabolic impacts and doesn't necessarily implicate PC without lipidomic or genetic evidence.

We agree and acknowledge it now in Discussion: “However, choline also plays other roles, including in neurotransmitter synthesis and methylation metabolism. Thus, we cannot yet rule out the possibility that the protective effects of choline supplementation stem from functions outside PC synthesis.”

Reviewer #3:

The study has several weaknesses: it provides limited novel insights into pathways mediating transcriptional regulation of cold-inducible genes, as IRE-1 and XBP-1are already well-known responders to endoplasmic reticulum stress, including that induced by cold.

We presume the reviewer refers to the study by Dudkevich et al. (2022). As explained in our manuscript, there are important differences between that study and ours in how the IRE-1 signalling is utilized and to what ends.

Additionally, the weak cold sensitivity phenotype observed in ire-1 mutants casts doubt on the pathway's key role in cold adaptation. The study also overlooks previous research (e.g.PMID: 27540856) that links IRE-1 to SKN-1, another major stress-responsive pathway, potentially missing important interactions and mechanisms involved in cold adaptation.

We state in the manuscript that the IRE-1 pathway plays a modest but significant role in cold adaptation and state in the Fig. 7 model and Discussion that additional pathways work alongside IRE-1 to drive cold-specific gene expression.

Recommendations for the authors:

Reviewer #1:

Minor comments:

(1) Fig. 2B - reporter expression seems to be already present in the intestine of 20ºC animals. What is the turnover rate of GFP in the intestine and how is it affected by the temperature shift? If GFP degradation is inhibited, could it explain the increase in signal in 4ºC animals, rather than increased transcription? This seems to be true for the hsp-4 transcriptional reporter, as the GFP fluorescence appears to increase during 4ºC incubation (Fig. 4a), but the hsp-4 message levels are only increased after 1 day but not in later days at 4ºC, based on the RNAseq in provided dataset. How well do changes in lips-11 reporter fluorescence correspond to the changes in the endogenous lips-11 transcript?

Note that increased GFP fluorescence is accompanied by increased mRNA levels. In addition to the RNAseq data, we now also examined changes of the endogenous lips-11 transcript by RTqPCR and observed its strong (and IRE-1 dependent) upregulation in the cold– see Figure 4 – figure supplement 2. Moreover, we now included two other examples of GFP-tagged proteins whose fluorescence increases in the cold, concomitant with increased mRNA levels and ribosomal occupancy (Figure 2 – figure supplement 2A-B).

(2) Descriptions of methods to measure different aspects of translation are very abbreviated and in some places make it difficult to understand the paper. One example - what is RFP in Fig. 2a?

We replaced now “RFP” with “RPF” (ribosome protected fragment) and the abbreviation is explained firsts time it is used.

(3) How was the effectiveness of RNAi at 4ºC validated?

As explained in Methods, we subjected animals to RNAi long before they were transferred to 4ºC, so the corresponding protein is depleted prior to cooling.

(4) Several of the conclusions on translation and ribosomal occupancy are written in a somewhat confusing way. For example, the authors state that "shift from 10ºC to 4ºC had a strong effect" when describing "impact on translation (ribosomal occupancy)" (page 4), but in the next sentence, they state "a good correlation between mRNA levels and translation (Figure 2A)". Was ribosomal occupancy normalized to the transcript abundance?

We do not perceive any discrepancy between the two statements. The former refers to the difference between time points, where we observed the largest change in both the transcriptome and ribosomal occupancy from 10ºC to 4ºC (as can be inferred in the PCA plot in Figure 2 - figure supplement 1). The latter refers to the observation that changes in mRNA levels mirrored, in most of cases, similar changes in the ribosomal occupancy.

The ribosomal occupancy was not normalized, as that would essentially normalize the y-axis (ribosomal occupancy) with the x-axis (mRNA), and so express changes in “translational efficiency” as a function of changes in mRNA abundance. While this type of analysis can also reveal interesting biological phenomena, it would explore a different question.

(5) "For most transcripts ... increased the abundance of a particular protein appears to correlate depend primarily on the abundance of its mRNA" (page 5). This is an overstatement, the protein levels were not quantified.

As explained above, we now additionally monitored the expression of two GFP-tagged proteins (CEBP-1 and NUMR-1). Monitoring their expression, we observed the expected increase in GFP fluorescence in the cold (see Figure 2 – figure supplement 3 A-B). While we did not examine them also by western blot, these observations are in line with our conclusions.

(6) The statement "Since transcription is the main determinant of mRNA levels, these results suggest that cold-specific gene expression primarily depends on transcription activation" seems to assume that message degradation doesn't have much of an impact at 4ºC. What is the evidence here? The authors themselves later suggest either transcription or mRNA stability in Discussion.

While we cannot exclude that mRNA stability of some genes may be affected, this concern is more valid for the messages that go down in the cold. Although we have done it for only selected genes, each time we observed an increase in the mRNA levels, we also observed the corresponding increase in the protein; this study and Pekec et al. (2022). Then, the lips-11 reporter was designed to monitor the activity of its promoter, which we showed in sufficient to upregulate reporter GFP in the cold. We have now expanded the corresponding paragraph in Discussion, which will hopefully come across as more balanced.  

Reviewer #2:

(1) Alter title, conclusions to better reflect specific nature of the work.

We now provided additional data and feel that it justifies our conclusions and title.

(2) Use Gene Ontology searches to look at patterns of gene expression in RNA seq data.

We now show it in Figure 2 – figure supplement 2.

(3) Use genetic or lipidomic tools rather than solely adding exogenous lipids.

We agree that lipidomic analysis is an important direction for future research, but feel that lipidomic analysis and further genetic experiments go beyond the scope of current manuscript.

Reviewer #3:

To strengthen the evidence for the role of IRE-1 in cold adaptation, the authors might consider performing additional functional assays, such as testing the effects of IRE-1 and XBP-1 mutations under varying cold conditions and testing the genetic interaction of ire-1 with xbp-1, skn-1, and hsf-1 in cold sensitivities. It is also worth using alternative approaches such as independent alleles of ire-1, knockdowns or tissue-specific knockouts (without potential developmental compensation in global constitutive mutants) to better characterize the contribution of IRE-1 to cold adaptation. Additionally, studies that examine tissue-specific responses to cold exposure could provide important insights, as different tissues may utilize distinct molecular pathways to adapt to cold stress.

We also tested ire-1 and xbp-1 functions by RNAi-mediated depletion. SKN-1 is a good candidate for future studies, but Horikawa at al. (2024) showed that HSF-1 is not required for cold dormancy (at 4ºC); we also show now that HSF-1::GFP does not increase in the cold (Figure 2 – figure supplement 3C).

This reviewer also recommends clarifying the novelty of your findings in the context of existing literature, particularly regarding the established roles of IRE-1 and XBP-1 in responding to endoplasmic reticulum stress.

The entry point of this study was to clarify a long-standing problem in hibernation research, i.e., the apparent discrepancy between a global translation repression and de novo gene expression observed in the cold. By connecting cold-mediated expression of some genes to the IRE-1/XBP1 pathway, we strengthen the argumentation for transcription-mediated gene regulation in hibernating animals. We did go the extra mile to test the possible reason behind the activation of UPR^ER in the cold but feel that a deeper analysis deserves a separate study.

The term "hibernation" should be avoided or reworded since the study does not provide direct behavioral or physiological evidence for hibernation-like states; instead, the manuscript could refer to "cold-induced responses" or "adaptations to cold temperatures."

The term “hibernation” was used before even in the context of the C. elegans dauer state, which, arguably, is even less appropriate. In addition to a global suppression of translation shown here, we reported before that the same cooling regime suppresses ageing (Habacher et al., 2016; Figure S1C). Incubating at 4ºC also arrests C. elegans development (Horikawa et al., 2024). Thus, while the worm and mammalian hibernation are certainly not equivalent – which we clearly spell out – we like to use “hibernation” interchangeably with “cold dormancy” to draw attention to a fascinating aspect of C. elegans biology. Still, we use now quotation marks in the title to avoid misunderstanding.

The discussion could be strengthened by addressing the relevance of prior studies, such as those linking IRE-1 to SKN-1 (PMID: 27540856), TRPA-1 (PMID: 23415228), ZIP-10 (PMID: 29664006), HSF-1 (PMID: 38987256) in cold adaptation and elaborating on how your findings provide new

The IRE-1/SKN-1 and ZIP-10 papers are now mentioned when describing the model in Figure 7. The TRP-1 and HSF-1 papers are cited when discussing physiological differences between different cold temperatures. Consistent with our studies, the HSF-1 paper shows that nematodes enter a dormant state at 4ºC (but at 9ºC and higher temperatures continue developing). Importantly, HSF-1 promotes the development at 9ºC but is not important for the arrest at 4ºC. We also shown now in Figure 2 – figure supplement 3C that HSF-1 does not go up at 4ºC.

eLife Assessment

This manuscript provides important findings for understanding the mechanisms of a major gene causing the gonad of fish and other vertebrates, including mammals, to become an ovary rather than a testis. Evidence is solid, but alternative explanations for a number of the claims must be considered and discussed. The impact of the work would benefit by placing it in a richer historical context.

Reviewer #1 (Public Review):

The mechanisms that regulate establishment of the germline stem cells and germline progenitors during zebrafish reproductive development are not understood. Prior single cell analysis characterized the cell types of the early zebrafish ovary during and at stages after sexual differentiation. In this work Hsu et al. took a single approach to analyze the cell types present in the early gonad during early sex determination. As expected, they identified germline stem cells (GSCs) that express canonical GSC markers and distinct populations of progenitors. Unexpectedly, they found multiple populations of transcriptionally distinct progenitor populations that the authors termed early (those lacking the differentiation marker foxl2l), committed (those expressing fox2l2 and S-phase genes) and late (those expressing fox2l2 and meiotic genes) progenitors. Comparisons of their dataset to the published zebrafish ovary datasets confirmed the presence of these distinct progenitor populations in the ovary. Further, they convincingly validated the presence of these progenitor subtypes using fluorescent in situ hybridization. To investigate the relationship between progenitor subsets and known regulators of ovary differentiation, the authors conducted single cell analysis of gonads lacking the transcription factor, Foxl2l. As previously reported, Foxl2l absence blocks ovary differentiation and all foxl2l mutants develop testes. The single cell analysis here indicates that foxl2l is inappropriately expressed in GSCs and early progenitors and that germ cell differentiation is blocked at the committed progenitor stage since few committed progenitors and no late progenitors or meiotic transcripts were detected in the single cell analysis of foxl2l mutants. Based on the coexpression of genes that are not typically expressed together in normally developing germ cells, specifically nanos2 and foxl2l, and dmrt1 and foxl2l, the authors conclude that Foxl2l is required for the committed progenitor program and that it prevents committed progenitors from returning to the GSC state.

Overall, the data provide new insights into the cell populations of the early differentiating gonad, define distinct progenitor states, pinpoint a requirement for the ovary differentiation factor Foxl2l at a specific stage of progenitor differentiation, and generate new hypotheses to be tested. Many but not all of the conclusions are supported by compelling data, and some findings and conclusions need to be clarified in the context of the published literature.

(1) The authors conclude that the committed progenitors revert to GSCs based on the coexpression of nanos2 and foxl2l nanos2 and based on expression of id1 in mutants but not in WT. Without functional data demonstrating that the progenitors revert to an earlier state, alternative interpretations should be considered. For example, it is possible that the cells initiate the committed progenitor program but continue to express the GSC program and that the coexpression of both programs blocks differentiation. Consistent with this possibility, some Fox family members, FoxL2 and FoxPs for example, are known to be both activators and repressors of transcription or act primarily as repressors. Potentially relevant to this work, repressive activity of FoxL2 has been previously reported in the mammalian ovary (Pisarska et al Endocrinology 2004, Pisarska Am J. Phys Endo. Metabolism 2010, Kuo Reproduction 2012, Kuo Endocrinology 2011, as well as more recent publications). In that context interfering with FoxL2 was proposed to cause upregulated expression of genes normally repressed by FoxL2, accelerated follicle recruitment, and premature ovarian failure.

(2) The authors conclude that the committed progenitor stage is "the gate toward female determination" and that the cells "stay at S-Phase temporarily before differentiation". This conclusion seems to be based solely on single cell RNAseq expression. In several species, including zebrafish, meiotic entry occurs earlier in females and has been correlated with ovary development. The possibility that the late progenitor stage, the stage when meiotic genes are detected in this study and a stage missing in foxl2l mutants, is actually the key stage for female determination cannot be excluded by the data provided.

(3) The authors discuss prior working showing that loss of germ cells leads to male development and that germ cells are required for female development and claim to extend that work by showing here that some progenitors are already sexually differentiated. First, the stages compared are completely different. The earlier work looks at the primordial germ cells and their loss in the first few days of development before a gonad forms. In contrast, this work examines stages well after the gonad has formed and during sex determination. The second concern is that the conclusion that the progenitors are differentiated is based solely on the expression of foxl2l, which is initially expressed in the juvenile ovary state that lab strains have been shown to develop through (Wilson et al Front Cell Dev Bio 2024). While it is fair to state that some cells express ovary markers at this stage, it is unclear that this is sufficient evidence that the cells are differentiated. For example, in the context of the foxl2l mutant, the authors observe that GSCs and early progenitors inappropriately express foxl2l, but the mutants develop as males. Thus, expression of foxl2l transcripts alone is insufficient evidence to claim that the cells are already differentiated as female.

(4) The comparison between medaka and zebrafish foxl2l mutants seems to suggest that Foxl2l is required for meiosis in medaka but has a different role in zebrafish. However, if foxl2l represses the earlier developmental programs of GSCs and early progenitors, it is possible that continued expression of these early programs interferes with activation of meiotic genes. This could account for the absence of the late progenitor stage in foxl2l mutants since the late progenitor stage is defined by and distinguished from the earlier stages by expression of foxl2l and meiotic genes. If so, foxl2l may be similarly required in both systems.

(5) The authors state that "Foxl2l may ensure female differentiation by preventing stemness and antagonizing male development." It is unclear why suppressing stemness would be necessary for female differentiation since female zebrafish have stem cells as do male zebrafish. It seems likely that turning off the GSC and early differentiation programs is important for allowing expression of meiosis and oocyte differentiation genes, and that a gene other than Foxl2l is required for differentiation from GSCs to spermatocytes.

(6) Based on its expression in mutant progenitors, p53 is proposed to assist with alternative differentiation of mutant germ cells. Although p53 transcripts are expressed, no evidence is provided that p53 is involved in differentiation of germ cells, and sex bias has not been associated with the published p53 mutants in zebrafish. Furthermore, while p53 has been shown to be important for ovary to testis transformation in mutant contexts in adults, it appears dispensable for testis development in mutants that disrupt ovary differentiation in earlier stages (Rodriguez-Mari et al PLoS Gen 2010, Shive PNAS 2010, Hartung et al Mol. Reprod. Dev 2014, Miao Development 2017, Kaufman et al PLoSGen 2018, Bertho et al Development 2021. It is possible that p53 eliminates foxl2l mutant germ cells that are simultaneously expressing multiple developmental programs, but this possibility would need to be tested.

Reviewer #2 (Public Review):

In this manuscript, Hsu et al. used scRNA-seq to profile germ cells isolated from zebrafish ovaries. They identified the transcriptional profile of germ cells representing the early stages of oogenesis, from germline stem cells to newly formed follicle stage oocytes. They identified foxl2l as a gene expressed in probable oocyte progenitor cells, one of the least understood germ cell stages in the ovary. To understand to role of Foxl2l in oogenesis, they produced loss-of-function mutations in foxl2l using CRISPR/Cas9. They found that all foxl2l mutants are males as adults, suggesting that Foxl2l is required for oogenesis. To gain more insights, they performed scRNA-seq on cells isolated from 28 dpf foxl2l mutant ovaries and found that in the absence of foxl2l, germ cells appear to arrest as early progenitors. These results argue that Foxl2l, like its medaka homolog Foxl3, is necessary for promoting oocyte vs. spermatocyte differentiation during the oocyte progenitor stage.

Reviewer #3 (Public Review):

This is the first report to show a transcriptional factor, foxl2l, is essential for the development of female germs. Without foxl2l, germ cells will be developed into sperms. The report also clearly defined the arrested stage of early germ cells in foxl2l mutants, or stages that is critical for foxl2l to play a role for the further development of female germ cells. Due to lack of cell lineage tracing, the claim of foxl2l suppression of dedifferentiate of progenitor cells to GSC based on the gene expression and cell number changes is weak. In addition, separation of early germ cell types in foxl2l mutant using marker genes from WT may not be optimal.