Reviewer #2 (Public review):

Summary:

In "Founder effects arising from gathering dynamics systematically bias emerging pathogen surveillance" Bradford and Hang present an extension to the SIR model to account for the role of larger than pairwise interactions in infectious disease dynamics. They explore the impact of accounting for group interactions on the progression of infection through the various sub-populations that make up the population as a whole. Further, they explore the extent to which interaction heterogeneity can bias epidemiological inference from surveillance data in the form of IFR and variant growth rate dynamics. This work advances the theoretical formulation of the SIR model and may allow for more realistic modeling of infectious disease outbreaks in the future.

Strengths:

(1) This work addresses an important limitation of standard SIR models. While this limitation has been addressed previously in the form of network-based models, those are, as the authors argue, difficult to parameterize to real-world scenarios. Further, this work highlights critical biases that may appear in real-world epidemiological surveillance data. Particularly, over-estimation of variant growth rates shortly after emergence has led to a number of "false alarms" about new variants over the past five years (although also to some true alarms).

(2) While the results presented here generally confirm my intuitions on this topic, I think it is really useful for the field to have it presented in such a clear manner with a corresponding mathematical framework. This will be a helpful piece of work to point to to temper concerns about rapid increases in the frequency of rare variants.

(3) The authors provide a succinct derivation of their model that helps the reader understand how they arrived at their formulation starting from the standard SIR model.

(4) The visualizations throughout are generally easy to interpret and communicate the key points of the authors' work.

(5) I thank the authors for providing detailed code to reproduce manuscript figures in the associated GitHub repo.

Weaknesses:

(1) The authors argue that network-based SIR models are difficult to parameterize (line 66), however, the model presented here also has a key parameter, mainly P_n, or the distribution of risk groups in the population. I think it is important to explore the extent to which this parameter can be inferred from real-world data to assess whether this model is, in practice, any easier to parameterize.

(2) The authors explore only up to four different risk groups, accounting for only four-wise interactions. But, clearly, in real-world settings, there can be much larger gatherings that promote transmission. What was the justification for setting such a low limit on the maximum group size? I presume it's due to computational efficiency, which is understandable, but it should be discussed as a limitation.

(3) Another key limitation that isn't addressed by the authors is that there may be population structure beyond just risk heterogeneity. For example, there may be two separate (or, weakly connected) high-risk sub-groups. This will introduce temporal correlation in interactions that are not (and can not easily be) captured in this model. My instinct is that this would dampen the difference between risk groups shown in Figure 2A. While I appreciate the authors's desire to keep their model relatively simple, I think this limitation should be explicitly discussed as it is, in my opinion, relatively significant.

Author response:

Reviewer #1 (Public review):

Summary:

This work considers the biases introduced into pathogen surveillance due to congregation effects, and also models homophily and variants/clades. The results are primarily quantitative assessments of this bias but some qualitative insights are gained e.g. that initial variant transmission tends to be biased upwards due to this effect, which is closely related to classical founder effects.

Strengths:

The model considered involves a simplification of the process of congregation using multinomial sampling that allows for a simpler and more easily interpretable analysis.

Weaknesses:

This simplification removes some realism, for example, detailed temporal transmission dynamics of congregations.

We appreciate Reviewer #1's comments. We hope our framework, like the classic SIR model, can be adapted in the future to build more complex and realistic models.

Reviewer #2 (Public review):

Summary:

In "Founder effects arising from gathering dynamics systematically bias emerging pathogen surveillance" Bradford and Hang present an extension to the SIR model to account for the role of larger than pairwise interactions in infectious disease dynamics. They explore the impact of accounting for group interactions on the progression of infection through the various sub-populations that make up the population as a whole. Further, they explore the extent to which interaction heterogeneity can bias epidemiological inference from surveillance data in the form of IFR and variant growth rate dynamics. This work advances the theoretical formulation of the SIR model and may allow for more realistic modeling of infectious disease outbreaks in the future.

Strengths:

(1) This work addresses an important limitation of standard SIR models. While this limitation has been addressed previously in the form of network-based models, those are, as the authors argue, difficult to parameterize to real-world scenarios. Further, this work highlights critical biases that may appear in real-world epidemiological surveillance data. Particularly, over-estimation of variant growth rates shortly after emergence has led to a number of "false alarms" about new variants over the past five years (although also to some true alarms).

(2) While the results presented here generally confirm my intuitions on this topic, I think it is really useful for the field to have it presented in such a clear manner with a corresponding mathematical framework. This will be a helpful piece of work to point to to temper concerns about rapid increases in the frequency of rare variants.

(3) The authors provide a succinct derivation of their model that helps the reader understand how they arrived at their formulation starting from the standard SIR model.

(4) The visualizations throughout are generally easy to interpret and communicate the key points of the authors' work.

(5) I thank the authors for providing detailed code to reproduce manuscript figures in the associated GitHub repo.

Weaknesses:

(1) The authors argue that network-based SIR models are difficult to parameterize (line 66), however, the model presented here also has a key parameter, mainly P_n, or the distribution of risk groups in the population. I think it is important to explore the extent to which this parameter can be inferred from real-world data to assess whether this model is, in practice, any easier to parameterize.

(2) The authors explore only up to four different risk groups, accounting for only four-wise interactions. But, clearly, in real-world settings, there can be much larger gatherings that promote transmission. What was the justification for setting such a low limit on the maximum group size? I presume it's due to computational efficiency, which is understandable, but it should be discussed as a limitation.

(3) Another key limitation that isn't addressed by the authors is that there may be population structure beyond just risk heterogeneity. For example, there may be two separate (or, weakly connected) high-risk sub-groups. This will introduce temporal correlation in interactions that are not (and can not easily be) captured in this model. My instinct is that this would dampen the difference between risk groups shown in Figure 2A. While I appreciate the authors's desire to keep their model relatively simple, I think this limitation should be explicitly discussed as it is, in my opinion, relatively significant.

We appreciate Reviewer 2's thoughtful comments and wish to address some of the weaknesses:

We agree that inferring P_n from real data will be challenging, but think this is an important direction for future research. Further, we’d like to reframe our claim that our approach is "easier to parameterize" than network models. Rather, P_n has fewer degrees of freedom than analogous network models, just as many different networks can share the same degree distribution. Fewer degrees of freedom mean that we expect our model to suffer from fewer identifiability issues when fitting to data, though non-identifiability is often inescapable in models of this nature (e.g., \beta and \gamma in the SIR model are not uniquely identifiable during exponential growth). Whether this is more or less accurate is another question. Classic bias-variance tradeoffs argue that a model with a moderate complexity trained on one data set can better fit future data than overly simple or overly complex models.

We chose four risk groups for purposes of illustration, but this can be increased arbitrarily. It should be noted that the simulation bottleneck when increasing the numbers of risk groups is numerical due the stiffness of the ODEs. This arises because the nonlinearity of infection terms scales with the number of risk groups (e.g., ~ \beta * S * I^3 for 4 risk groups). As such, a careful choice of numerical solvers may be required when integrating the ODEs. Meanwhile, this is not an issue for stochastic, individual based implementation (e.g., Gillespie). As for how well this captures super-spreading, we believe choosing smaller risk groups does not hinder modeling disease spread at large gatherings. Consider a statistical interpretation, where individuals at a large gathering engage in a series of smaller interactions over time (e.g., 2/3/4/etc person conversations). The key determinants of the resulting gathering size distribution at any one large gathering are the number of individuals within some shared proximity over time and the infectiousness/dispersal of the pathogen. Of course, whether this interpretation is a sufficient approximation for classic super-spreading events (e.g., funerals during 2014-2015 West Africa Ebola outbreak) is a matter of debate. Our framework is best interpreted at a population level where the effects of any single gathering are washed out by the overall gathering distribution, P_n. As the prior weakness highlighted, establishing P_n is challenging, but we believe empirically measuring proxies of it may provide future insight in how behavior impacts disease spread. For example, prior work has combined contact tracing and co-location data from connection to WiFi networks to estimate the distribution of contacts per individual, and its degree of overdispersion (Petros et al. Med 2022).

We chose to introduce our framework in a simple SIR context familiar to many readers. This decision does not in any way limit applying it to settings with more population structure. Rather, we believe our framework is easily adaptable and that our presentation (hopefully) makes it clear how to do this. For example, two weakly connected groups could be easily achieved by (for each gathering) first sampling the preferred group and then sampling from the population in a biased manner. The biased sampling could even be a function of gathering sizes, time, etc. The resulting infection terms are still (sums of) multinomials. More generally, the sampling probabilities for an individual of some type need not be its frequency (e.g., S/N, I/N). Indeed, we believe generating models with complex social interactions is both simplified and made more robust by focusing on modeling the generative process of attending gatherings.

eLife Assessment

The study introduces new tools for measuring the intracellular calcium concentration close to transmitter release sites, which may be relevant for synaptic vesicle fusion and replenishment. This approach yields important new information about the spatial and temporal profile of calcium concentrations near the site of entry at the plasma membrane. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in calcium domains. Key gaps in the data presented mean that the evidence for the main conclusions is currently incomplete.

Reviewer #1 (Public review):

This paper describes technically-impressive measurements of calcium signals near synaptic ribbons in goldfish bipolar cells. The data presented provides high spatial and temporal resolution information about calcium concentrations along the ribbon at various distances from the site of entry at the plasma membrane. This is important information. Important gaps in the data presented mean that the evidence for the main conclusions is currently inadequate.

Strengths

(1) The technical aspects of the measurements are impressive. The authors use calcium indicators bound to the ribbon and high-speed line scans to resolve changes with a spatial resolution of ~250 nm and a temporal resolution of less than 10 ms. These spatial and temporal scales are much closer to those relevant for vesicle release than previous measurements.

(2) The use of calcium indicators with very different affinities and different intracellular calcium buffers helps provide confirmation of key results.

Weaknesses

(1) Multiple key points of the paper lack statistical tests or summary data from populations of cells. For example, the text states that the proximal and distal calcium kinetics in Figure 2A differ. This is not clear from the inset to Figure 2A - where the traces look like scaled versions of each other. Values for time to half-maximal peak fluorescence are given for one example cell but no statistics or summary are provided. Figure 8 shows examples from one cell with no summary data. This issue comes up in other places as well.

(2) Figure 5 is confusing. The figure caption describes red, green, and blue traces, but the figure itself has only two traces in each panel and none are red, green, or blue. It's not possible currently to evaluate this figure.

(3) The rise time measurements in Figure 2 are very different for low and high-affinity indicators, but no explanation is given for this difference. Similarly, the measurements of peak calcium concentration in Figure 4 are very different from the two indicators. That might suggest that the high-affinity indicator is strongly saturated, which raises concerns about whether that is impacting the kinetic measurements.

Reviewer #2 (Public review):

Summary:

The study introduces new tools for measuring intracellular Ca2+ concentration gradients around retinal rod bipolar cell (rbc) synaptic ribbons. This is done by comparing the Ca2+ profiles measured with mobile Ca2+ indicator dyes versus ribbon-tethered (immobile) Ca2+ indicator dyes. The Ca2+ imaging results provide a straightforward demonstration of Ca2+ gradients around the ribbon and validate their experimental strategy. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in Ca2+ domains as a function of Ca2+ buffering. In addition, the authors try to demonstrate that there is heterogeneity among synaptic ribbons within an individual rbc terminal.

Strengths:

The study introduces a new set of tools for estimating Ca2+ concentration gradients at ribbon AZs, and the experimental results are accompanied by an open-source, computational model that nicely describes Ca2+ buffering at the rbc synaptic ribbon. In addition, the dissociated retinal preparation remains a valuable approach for studying ribbon synapses. Lastly, excellent EM.

Weaknesses:

Heterogeneity in the spatiotemporal dynamics of Ca2+ influx was not convincingly related to ribbon size, nor was the functional relevance of Ca2+ dynamics to rod bipolars demonstrated (e.g., exocytosis to different postsynaptic targets). In addition, the study would benefit from the inclusion of the Ca2+ currents that were recorded in parallel with the Ca2+ imaging.

Reviewer #3 (Public review):

Summary:

In this study, the authors have developed a new Ca indicator conjugated to the peptide, which likely recognizes synaptic ribbons, and have measured microdomain Ca near synaptic ribbons at retinal bipolar cells. This interesting approach allows one to measure Ca close to transmitter release sites, which may be relevant for synaptic vesicle fusion and replenishment. Though microdomain Ca at the active zone of ribbon synapses has been measured by Hudspeth and Moser, the new study uses the peptide recognizing synaptic ribbons, potentially measuring the Ca concentration relatively proximal to the release sites.

Strengths:

The study is in principle technically well done, and the peptide approach is technically interesting, which allows one to image Ca near the particular protein complexes. The approach is potentially applicable to other types of imaging.

Weaknesses:

Peptides may not be entirely specific, and the genetic approach tagging particular active zone proteins with fluorescent Ca indicator proteins may well be more specific. I also feel that "Nano-physiology" is overselling, because the measured Ca is most likely the local average surrounding synaptic ribbons. With this approach, nobody knows about the real release site Ca or the Ca relevant for synaptic vesicle replenishment. It is rather "microdomain physiology" which measures the local Ca near synaptic ribbons, relatively large structures responsible for fusion, replenishment, and recycling of synaptic vesicles.

Author response:

Public Reviews:

Reviewer #1 (Public review):

This paper describes technically-impressive measurements of calcium signals near synaptic ribbons in goldfish bipolar cells. The data presented provides high spatial and temporal resolution information about calcium concentrations along the ribbon at various distances from the site of entry at the plasma membrane. This is important information. Important gaps in the data presented mean that the evidence for the main conclusions is currently inadequate.

Strengths

(1) The technical aspects of the measurements are impressive. The authors use calcium indicators bound to the ribbon and high-speed line scans to resolve changes with a spatial resolution of ~250 nm and a temporal resolution of less than 10 ms. These spatial and temporal scales are much closer to those relevant for vesicle release than previous measurements.

(2) The use of calcium indicators with very different affinities and different intracellular calcium buffers helps provide confirmation of key results.

Thank you very much for this positive evaluation of our work.

Weaknesses

(1) Multiple key points of the paper lack statistical tests or summary data from populations of cells. For example, the text states that the proximal and distal calcium kinetics in Figure 2A differ. This is not clear from the inset to Figure 2A - where the traces look like scaled versions of each other. Values for time to half-maximal peak fluorescence are given for one example cell but no statistics or summary are provided. Figure 8 shows examples from one cell with no summary data. This issue comes up in other places as well.

Thank you for this feedback. We will address this in our revised manuscript.

(2) Figure 5 is confusing. The figure caption describes red, green, and blue traces, but the figure itself has only two traces in each panel and none are red, green, or blue. It's not possible currently to evaluate this figure.

Thank you for pointing out this oversight. The figure indeed only shows the proximal and distal calcium signals, but not the cytoplasmic ones. The figure will be corrected in our revised manuscript.

(3) The rise time measurements in Figure 2 are very different for low and high-affinity indicators, but no explanation is given for this difference. Similarly, the measurements of peak calcium concentration in Figure 4 are very different from the two indicators. That might suggest that the high-affinity indicator is strongly saturated, which raises concerns about whether that is impacting the kinetic measurements.

As we had mentioned in the text, we do believe that the high-affinity version is partially saturated. This will be a problem for strong depolarizations and signals near the membrane. The higher affinity indicators are more useful for reporting calcium levels on the ribbon after the depolarization when the signal from the low affinity indicators is small. We will address this in the discussion of the revision.

Reviewer #2 (Public review):

Summary:

The study introduces new tools for measuring intracellular Ca2+ concentration gradients around retinal rod bipolar cell (rbc) synaptic ribbons. This is done by comparing the Ca2+ profiles measured with mobile Ca2+ indicator dyes versus ribbon-tethered (immobile) Ca2+ indicator dyes. The Ca2+ imaging results provide a straightforward demonstration of Ca2+ gradients around the ribbon and validate their experimental strategy. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in Ca2+ domains as a function of Ca2+ buffering. In addition, the authors try to demonstrate that there is heterogeneity among synaptic ribbons within an individual rbc terminal.

Strengths:

The study introduces a new set of tools for estimating Ca2+ concentration gradients at ribbon AZs, and the experimental results are accompanied by an open-source, computational model that nicely describes Ca2+ buffering at the rbc synaptic ribbon. In addition, the dissociated retinal preparation remains a valuable approach for studying ribbon synapses. Lastly, excellent EM.

Thank you very much for this appreciation.

Weaknesses:

Heterogeneity in the spatiotemporal dynamics of Ca2+ influx was not convincingly related to ribbon size, nor was the functional relevance of Ca2+ dynamics to rod bipolars demonstrated (e.g., exocytosis to different postsynaptic targets). In addition, the study would benefit from the inclusion of the Ca2+ currents that were recorded in parallel with the Ca2+ imaging.

Thank you for this critique. We agree that the relationship between size and Ca2+ signal is not established by our recordings. By analogy to the hair cell literature, we believe that it is a reasonable hypothesis, but more studies will be necessary to definitively determine whether the signal relates to the ribbon size or synaptic signaling. This will be addressed in future experiments.

We will include the Ca²⁺ currents in the revision.

Reviewer #3 (Public review):

Summary:

In this study, the authors have developed a new Ca indicator conjugated to the peptide, which likely recognizes synaptic ribbons, and have measured microdomain Ca near synaptic ribbons at retinal bipolar cells. This interesting approach allows one to measure Ca close to transmitter release sites, which may be relevant for synaptic vesicle fusion and replenishment. Though microdomain Ca at the active zone of ribbon synapses has been measured by Hudspeth and Moser, the new study uses the peptide recognizing synaptic ribbons, potentially measuring the Ca concentration relatively proximal to the release sites.

Strengths:

The study is in principle technically well done, and the peptide approach is technically interesting, which allows one to image Ca near the particular protein complexes. The approach is potentially applicable to other types of imaging.

Thank you very much for this appreciation.

Weaknesses:

Peptides may not be entirely specific, and the genetic approach tagging particular active zone proteins with fluorescent Ca indicator proteins may well be more specific. I also feel that "Nano-physiology" is overselling, because the measured Ca is most likely the local average surrounding synaptic ribbons. With this approach, nobody knows about the real release site Ca or the Ca relevant for synaptic vesicle replenishment. It is rather "microdomain physiology" which measures the local Ca near synaptic ribbons, relatively large structures responsible for fusion, replenishment, and recycling of synaptic vesicles.

The peptide approach has been used fairly extensively in the ribbon synapse field and the evidence that it efficiently labels the ribbon is well established, however, we do acknowledge that the peptide is in equilibrium with a cytoplasmic pool. Thus, some of the signal arises from this cytoplasmic pool. The alternative of a genetically encoded Ca-indicator concatenated to a ribbon protein would not have this problem, but would be more limited in flexibility in changing calcium indicators. We believe both approaches have their merits, each with separate advantages and disadvantages.

As for the nano vs. micro argument, we certainly do not want to suggest that we are measuring the same nano-domains, in the 10s of nanometers, that drive neurotransmitter release, but we do believe we are in the sub-micrometer--100s of nm—range. We chose the term based on the usage by other authors to describe similar measurements (Neef et al., 2018; https://doi.org/10.1038/s41467-017-02612-y), but we see the reviewer’s point. To avoid confusion, we will change the title in the revision.

eLife Assessment

This study presents valuable findings on the increased prevalence of pain in women with polycystic ovary syndrome and its relationship to health outcomes. The evidence supporting the conclusions is compelling with a large number of patients and sound methodology, and can be used as a starting point for studies of etiology and mechanisms of pain in women with polycystic ovary syndrome and comorbidities. The work will be of interest to medical biologists working on polycystic ovary syndrome pathophysiology and clinicians.

Reviewer #1 (Public review):

Summary:

This retrospective study provides new data regarding the prevalence of pain in women with PCOS and its relationship with health outcomes. Using data from electronic health records (EHR), the authors found a significantly higher prevalence of pain among women with PCOS compared to those without the condition: 19.21% of women with PCOS versus 15.8% in non-PCOS women. The highest prevalence of pain was conducted among Black or African American (32.11%) and White (30.75%) populations. Besides, women with PCOS and pain have at least a 2-fold increased prevalence of obesity (34.68%) at baseline compared to women with PCOS in general (16.11%). Also, women with PCOS had the highest risk for infertility and T2D, but women with PCOS and pain had higher risks for ovarian cysts and liver disease. Regarding these results, the authors suggested the critical need to address pain in the diagnosis and management of PCOS due to its significant impact on patient health outcomes.

Strengths:

(1) The problem of pain assessment in PCOS patients is well described and the authors provided a clear rationale selection of the retrospective design to investigate this problem.

(2) A large number of analyzed patient records (76,859,666 women) and their uniformity increases the power of the study. Using the Propensity Score Matching makes it possible to reduce the heterogeneity of the compared cohorts and the influence of comorbid conditions.

(3) Analysis in different ethnic cohorts provides actual and necessary data regarding the prevalence of pain and its relationship with different health conditions that will be helpful for clinicians to make a diagnosis and manage PCOS in women of different ethnicities.

(4) Assessment of the risk of different health conditions including PCOS-associated pathology as other common groups of diseases in PCOS women with or without pain allows to differentiate the risk of comorbid conditions depending on the presence of one symptom (pelvic or abdominal pain, dysmenorrhea).

Weaknesses:

(1) Although the paper has strengths in methodology and data analysis, it also has some weaknesses. The lack of a hypothesis doesn't allow us to evaluate the aim and significance of this study.

(2) The exclusion criteria don't include conditions, that can lead to symptoms similar to PCOS: thyroid diseases, hyperprolactinemia, and congenital adrenal hyperplasia. Thyroid status is not being taken into account in the criteria for matching. All these conditions could occur as on prevalence results as on risk assessment.

(3) The significant weakness of the study is the absence of a Latin American cohort. Probably the White cohort includes Latin Americans or others, but the results of the study cannot be extrapolated to particular White ethnicities.

(4) The authors didn't provide sufficient rationale for future health outcomes and this list didn't include diseases of the digestive system or disorders of thyroid glands, which can also cause abdominal pain.

Reviewer #2 (Public review):

Summary:

The study offers a thorough analysis of the prevalence of pain in women with polycystic ovary syndrome (PCOS) and its associations with health outcomes across various racial groups. Furthermore, the research investigates the prevalence of PCOS and pain among different racial demographics, as well as the increased risk of developing various conditions in comparison to individuals who have PCOS alone.

Strengths:

The study emphasizes pain as a significant comorbidity of PCOS, an area that is critically underexplored in existing literature. The findings regarding the increased prevalence of some of the diseases in the PCOS + pain group provide valuable direction for future research and clinical care. I believe physicians should incorporate pain score assessments into their clinical practice to improve patient's quality of life and raise awareness about pain management. If future research focuses on the mechanisms of pain, it would provide a better understanding of pain and allow for a focus on the underlying causes rather than just symptomatic management. The study also highlights the association between PCOS+pain and various comorbidities, such as obesity, hypertension, and type 2 diabetes, as well as conditions like infertility and ovarian cysts, offering a holistic view of the burden of PCOS.

Weaknesses:

Due to the nature of the retrospective study, some data may not be readily available in the system. Instead of simply categorizing participants based on whether they experience pain, it would be more useful to employ a pain scale or questionnaire to better understand the severity and type of patients' pain. This approach would allow for a more thorough analysis of pain improvement following treatment with the three widely used medications for PCOS. Additionally, it would be beneficial for the authors to specify subtypes of the disease rather than generalizing conditions, such as mentioning specific digestive system disorders or mental health disorders. The lack of detailed analysis of specific disorders limits the depth of the findings. This may cause authors to make incorrect conclusions.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This retrospective study provides new data regarding the prevalence of pain in women with PCOS and its relationship with health outcomes. Using data from electronic health records (EHR), the authors found a significantly higher prevalence of pain among women with PCOS compared to those without the condition: 19.21% of women with PCOS versus 15.8% in non-PCOS women. The highest prevalence of pain was conducted among Black or African American (32.11%) and White (30.75%) populations. Besides, women with PCOS and pain have at least a 2-fold increased prevalence of obesity (34.68%) at baseline compared to women with PCOS in general (16.11%). Also, women with PCOS had the highest risk for infertility and T2D, but women with PCOS and pain had higher risks for ovarian cysts and liver disease. Regarding these results, the authors suggested the critical need to address pain in the diagnosis and management of PCOS due to its significant impact on patient health outcomes.

Strengths:

(1) The problem of pain assessment in PCOS patients is well described and the authors provided a clear rationale selection of the retrospective design to investigate this problem.(2) A large number of analyzed patient records (76,859,666 women) and their uniformity increases the power of the study. Using the Propensity Score Matching makes it possible to reduce the heterogeneity of the compared cohorts and the influence of comorbid conditions.(3) Analysis in different ethnic cohorts provides actual and necessary data regarding the prevalence of pain and its relationship with different health conditions that will be helpful for clinicians to make a diagnosis and manage PCOS in women of different ethnicities. (4) Assessment of the risk of different health conditions including PCOS-associated pathology as other common groups of diseases in PCOS women with or without pain allows to differentiate the risk of comorbid conditions depending on the presence of one symptom (pelvic or abdominal pain, dysmenorrhea).

We appreciate the positive feedback on this manuscript. Pain assessment in women with PCOS is of paramount interest and because of a gap in this research area, we are trying to address it.

Weaknesses:

(1) Although the paper has strengths in methodology and data analysis, it also has some weaknesses.

The lack of a hypothesis doesn't allow us to evaluate the aim and significance of this study.

We would like to thank the Reviewer for their valuable feedback regarding the hypothesis of this study. We understand that the hypothesis may not have been written clearly under the objectives and we will correct this in the formal revision.

The primary hypothesis of this study is that women with PCOS experience a higher prevalence to pain (including dysmenorrhea, abdominal pain and pelvic pain) compared to women without PCOS, and this prevalence varies by racial groups. Our hypothesis aims to explore the relationship between PCOS and pain, the associated health risks, and the potential racial disparities in pain prevalence and long-term health outcomes. Additionally, we seek to assess the effect of treatment on reducing pain symptoms in women with PCOS. This study not only examines the immediate burden of pain but also investigates its long-term consequences, including risks of infertility, obesity, and type 2 diabetes.

To enhance clarity for readers, we will explicitly state this hypothesis in the revised manuscript and ensure that its connection to the study’s objectives is clearly articulated. We appreciate the Reviewer’s insights and will incorporate these refinements to strengthen the manuscript.

(2) The exclusion criteria don't include conditions, that can lead to symptoms similar to PCOS: thyroid diseases, hyperprolactinemia, and congenital adrenal hyperplasia. Thyroid status is not being taken into account in the criteria for matching. All these conditions could occur as on prevalence results as on risk assessment.

We would like to thank the Reviewer for highlighting the need to include these additional conditions that mimic PCOS. After excluding hypothyroidism, hyperprolactinemia, and adrenal hyperplasia from the PCOS and PCOS and pain cohorts, we observed that 7,690 patients (1.65%) with PCOS and 1,854 patients (1.36%) with PCOS were removed. Based on this observation, we plan to add these three conditions to our exclusion criteria and rerun our analysis for disease prevalence and relative risk for our resubmission.

We will update the manuscript accordingly to reflect these exclusions and ensure clarity in our methodology. Additionally, we will discuss the rationale for excluding these conditions to improve transparency and provide a more precise interpretation of our findings.

(3) The significant weakness of the study is the absence of a Latin American cohort. Probably the White cohort includes Latin Americans or others, but the results of the study cannot be extrapolated to particular White ethnicities.

We appreciate the Reviewer’s suggestion to include Latin American cohorts in studies. In this paper we only used race as a variable and did not incorporate ethnicity. However, for our resubmission we plan to include self-reported ethnicity in our analysis which will capture the Latin American cohort stratified by self-reported race groups. This addition will provide a more comprehensive understanding of racial and ethnic differences in our study population, and we will update the manuscript accordingly to reflect this expansion.

(4) The authors didn't provide sufficient rationale for future health outcomes and this list didn't include diseases of the digestive system or disorders of thyroid glands, which can also cause abdominal pain.

We appreciate the Reviewer comment and understand their concern. Our current results highlight the prevalence of disorders of the digestive system in Figure 2 and in the results section. To further strengthen our analysis, we plan to include disorders of the digestive system in our relative risk (RR) assessment. However, we will not be able to include the same analysis for thyroid dysfunctions as they will be considered as an exclusion criterion. These updates will be incorporated into the revised manuscript to ensure clarity and completeness.

Reviewer #2 (Public review):

Summary:

The study offers a thorough analysis of the prevalence of pain in women with polycystic ovary syndrome (PCOS) and its associations with health outcomes across various racial groups. Furthermore, the research investigates the prevalence of PCOS and pain among different racial demographics, as well as the increased risk of developing various conditions in comparison to individuals who have PCOS alone.

Strengths:

The study emphasizes pain as a significant comorbidity of PCOS, an area that is critically underexplored in existing literature. The findings regarding the increased prevalence of some of the diseases in the PCOS + pain group provide valuable direction for future research and clinical care. I believe physicians should incorporate pain score assessments into their clinical practice to improve patient's quality of life and raise awareness about pain management. If future research focuses on the mechanisms of pain, it would provide a better understanding of pain and allow for a focus on the underlying causes rather than just symptomatic management. The study also highlights the association between PCOS+pain and various comorbidities, such as obesity, hypertension, and type 2 diabetes, as well as conditions like infertility and ovarian cysts, offering a holistic view of the burden of PCOS.

We sincerely appreciate the Reviewer’s insightful comments. We hope that our findings will encourage further research on the occurrence of pain in women with PCOS and that others will replicate our results to strengthen the evidence in this area. As noted in our introduction, there are currently no standardized abdominal pain score assessments specifically for women with PCOS. We hope that the findings from this study will contribute to efforts toward developing a standardized pain assessment for the PCOS community. In the meantime, further research across more diverse populations will be essential to build a more comprehensive understanding of this issue.

Weaknesses:

Due to the nature of the retrospective study, some data may not be readily available in the system. Instead of simply categorizing participants based on whether they experience pain, it would be more useful to employ a pain scale or questionnaire to better understand the severity and type of patients' pain. This approach would allow for a more thorough analysis of pain improvement following treatment with the three widely used medications for PCOS. Additionally, it would be beneficial for the authors to specify subtypes of the disease rather than generalizing conditions, such as mentioning specific digestive system disorders or mental health disorders. The lack of detailed analysis of specific disorders limits the depth of the findings. This may cause authors to make incorrect conclusions.

We appreciate the Reviewer for highlighting the importance of categorizing pain levels experienced by women with PCOS. However, there is currently no standardized pain assessment for abdominal pain, and therefore more research is required before such a classification can be made. Additionally, the electronic health record data we leveraged via the TriNextX platform does not include any pain scale data from unstructured notes. Despite these limitations, this study is an important step toward recognizing abdominal and pelvic pain in women with PCOS. Our findings indicate that women with PCOS report abdominal pain independent of digestive conditions such as irritable bowel syndrome— a condition often associated with pain in this population.

We would like to thank the Reviewer for their thoughtful comment with respect to subtyping the future health outcomes. To address this, we plan to include the most common diseases associated with PCOS for each general disease group as a supplemental figure in the revised manuscript.

eLife Assessment

This valuable study characterises the activity of motor units from two of the three anatomical subdivisions ("heads") of the triceps muscle while mice walked on a treadmill at various speeds. Although this is the most thorough characterisation of motor unit activity in walking mice to date, the evidence supporting some of the claims, especially pertaining to probabilistic recruitment of motor units, is incomplete. Further investigating whether the differences in motor unit recruitment across muscle heads go beyond their different mechanical functions would also strengthen the paper.

Reviewer #1 (Public review):

Summary:

Here, the authors have addressed the recruitment and firing patterns of motor units (MUs) from the long and lateral heads of the triceps in the mouse. They used their newly developed Myomatrix arrays to record from these muscles during treadmill locomotion at different speeds, and they used template-based spike sorting (Kilosort) to extract units. Between MUs from the two heads, the authors observed differences in their firing rates, recruitment probability, phase of activation within the locomotor cycle, and interspike interval patterning. Examining different walking speeds, the authors find increases in both recruitment probability and firing rates as speed increases. The authors also observed differences in the relation between recruitment and the angle of elbow extension between motor units from each head. These differences indicate meaningful variation between motor units within and across motor pools and may reflect the somewhat distinct joint actions of the two heads of triceps.

Strengths:

The extraction of MU spike timing for many individual units is an exciting new method that has great promise for exposing the fine detail in muscle activation and its control by the motor system. In particular, the methods developed by the authors for this purpose seem to be the only way to reliably resolve single MUs in the mouse, as the methods used previously in humans and in monkeys (e.g. Marshall et al. Nature Neuroscience, 2022) do not seem readily adaptable for use in rodents.

The paper provides a number of interesting observations. There are signs of interesting differences in MU activation profiles for individual muscles here, consistent with those shown by Marshall et al. It is also nice to see fine-scale differences in the activation of different muscle heads, which could relate to their partially distinct functions. The mouse offers greater opportunities for understanding the control of these distinct functions, compared to the other organisms in which functional differences between heads have previously been described.

The Discussion is very thorough, providing a very nice recounting of a great deal of relevant previous results.

Weaknesses:

The findings are limited to one pair of muscle heads. While an important initial finding, the lack of confirmation from analysis of other muscles acting at other joints leaves the general relevance of these findings unclear.

While differences between muscle heads with somewhat distinct functions are interesting and relevant to joint control, differences between MUs for individual muscles, like those in Marshall et al., are more striking because they cannot be attributed potentially to differences in each head's function. The present manuscript does show some signs of differences for MUs within individual heads: in Figure 2C, we see what looks like two clusters of motor units within the long head in terms of their recruitment probability. However, a statistical basis for the existence of two distinct subpopulations is not provided, and no subsequent analysis is done to explore the potential for differences among MUs for individual heads.

The statistical foundation for some claims is lacking. In addition, the description of key statistical analysis in the Methods is too brief and very hard to understand. This leaves several claims hard to validate.

Reviewer #2 (Public review):

The present study, led by Thomas and collaborators, aims to describe the firing activity of individual motor units in mice during locomotion. To achieve this, they implanted small arrays of eight electrodes in two heads of the triceps and performed spike sorting using a custom implementation of Kilosort. Simultaneously, they tracked the positions of the shoulder, elbow, and wrist using a single camera and a markerless motion capture algorithm (DeepLabCut). Repeated one-minute recordings were conducted in six mice at five different speeds, ranging from 10 to 27.5 cm·s⁻¹.

From these data, the authors reported that:

(1) a significant portion of the identified motor units was not consistently recruited across strides,<br /> (2) motor units identified from the lateral head of the triceps tended to be recruited later than those from the long head,<br /> (3) the number of spikes per stride and peak firing rates were correlated in both muscles, and<br /> (4) the probability of motor unit recruitment and firing rates increased with walking speed.

The authors conclude that these differences can be attributed to the distinct functions of the muscles and the constraints of the task (i.e., speed).

Strengths:

The combination of novel electrode arrays to record intramuscular electromyographic signals from a larger muscle volume with an advanced spike sorting pipeline capable of identifying populations of motor units.

Weaknesses:

(1) There is a lack of information on the number of identified motor units per muscle and per animal.

(2) All identified motor units are pooled in the analyses, whereas per-animal analyses would have been valuable, as motor units within an individual likely receive common synaptic inputs. Such analyses would fully leverage the potential of identifying populations of motor units.

(3) The current data do not allow for determining which motor units were sampled from each pool. It remains unclear whether the sample is biased toward high-threshold motor units or representative of the full pool.

(4) The behavioural analysis of the animals relies solely on kinematics (2D estimates of elbow angle and stride timing). Without ground reaction forces or shoulder angle data, drawing functional conclusions from the results is challenging.

Major comments:

(1) Spike sorting

The conclusions of the study rely on the accuracy and robustness of the spike sorting algorithm during a highly dynamic task. Although the pipeline was presented in a previous publication (Chung et al., 2023, eLife), a proper validation of the algorithm for identifying motor unit spikes is still lacking. This is particularly important in the present study, as the experimental conditions involve significant dynamic changes. Under such conditions, muscle geometry is altered due to variations in both fibre pennation angles and lengths.

This issue differs from electrode drift, and it is unclear whether the original implementation of Kilosort includes functions to address it. Could the authors provide more details on the various steps of their pipeline, the strategies they employed to ensure consistent tracking of motor unit action potentials despite potential changes in action potential waveforms, and the methods used for manual inspection of the spike sorting algorithm's output?

(2) Yield of the spike sorting pipeline and analyses per animal/muscle

A total of 33 motor units were identified from two heads of the triceps in six mice (17 from the long head and 16 from the lateral head). However, precise information on the yield per muscle per animal is not provided. This information is crucial to support the novelty of the study, as the authors claim in the introduction that their electrode arrays enable the identification of populations of motor units.

Beyond reporting the number of identified motor units, another way to demonstrate the effectiveness of the spike sorting algorithm would be to compare the recorded EMG signals with the residual signal obtained after subtracting the action potentials of the identified motor units, using a signal-to-residual ratio.

Furthermore, motor units identified from the same muscle and the same animal are likely not independent due to common synaptic inputs. This dependence should be accounted for in the statistical analyses when comparing changes in motor unit properties across speeds and between muscles.

(3) Representativeness of the sample of identified motor units

However, to draw such conclusions, the authors should exclusively compare motor units from the same pool and systematically track violations of the recruitment order. Alternatively, they could demonstrate that the motor units that are intermittently active across strides correspond to the smallest motor units, based on the assumption that these units should always be recruited due to their low activation thresholds.

One way to estimate the size of motor units identified within the same muscle would be to compare the amplitude of their action potentials, assuming that all motor units are relatively close to the electrodes (given the selectivity of the recordings) and that motoneurons innervating more muscle fibres generate larger motor unit action potentials.

Currently, the data seem to support the idea that motor units that are alternately recruited across strides have recruitment thresholds close to the level of activation or force produced during slow walking. The fact that recruitment probability monotonically increases with speed suggests that the force required to propel the mouse forward exceeds the recruitment threshold of these "large" motor units. This pattern would primarily reflect spatial recruitment following the size principle rather than flexible motor unit control.

(4) Analysis of recruitment and firing rates

The authors currently report active duration and peak firing rates based on spike trains convolved with a Gaussian kernel. Why not report the peak of the instantaneous firing rates estimated from the inverse of the inter-spike interval? This approach appears to be more aligned with previous studies conducted to describe motor unit behaviour during fast movements (e.g., Desmedt & Godaux, 1977, J Physiol; Van Cutsem et al., 1998, J Physiol; Del Vecchio et al., 2019, J Physiol).

(5) Additional analyses on behaviour

The authors currently analyse motor unit recruitment in relation to elbow angle. It would be valuable to include a similar analysis using the angular velocity observed during each stride, as higher velocity would place each muscle in a less favourable position on the force-velocity relationship for generating the required force. More broadly, comparing stride-by-stride changes in firing rates with changes in elbow angular velocity would further strengthen the final analyses presented in the results section.

Reviewer #3 (Public review):

Summary:

Using the approach of Myomatrix recording, the authors report that:

(1) Motor units are recruited differently in the two types of muscles.<br /> (2) Individual units are probabilistically recruited during the locomotion strides, whereas the population bulk EMG has a more reliable representation of the muscle.<br /> (3) The recruitment of units was proportional to walking speed.

Strengths:

The new technique provides a unique data set, and the data analysis is convincing and well-performed.

Weaknesses:

The implications of "probabilistical recruitment" should be explored, addressed, and analyzed further.

Comments:

One of the study's main findings (perhaps the main finding) is that the motor units are "probabilistically" recruited. The authors do not define what they mean by probabilistically recruited, nor do they present an alternative scenario to such recruitment or discuss why this would be interesting or surprising. However, on page 4, they do indicate that the recruitment of units from both muscles was only active in a subset of strides, i.e., they are not reliably active in every step.

If probabilistic means irregular spiking, this is not new. Variability in spiking has been seen numerous times, for instance in human biceps brachii motor units during isometric contractions (Pascoe, Enoka, Exp physiology 2014) and elsewhere. Perhaps the distinction the authors are seeking is between fluctuation-driven and mean-driven spiking of motor units as previously identified in spinal motor networks (see Petersen and Berg, eLife 2016, and Berg, Frontiers 2017). Here, it was shown that a prominent regime of irregular spiking is present during rhythmic motor activity, which also manifests as a positive skewness in the spike count distribution (i.e., log-normal).

eLife Assessment

This important study identifies a novel role for Hes5+ astrocytes in modulating the activity of descending pain-inhibitory noradrenergic neurons from the locus coeruleus during stress-induced pain facilitation. The role of glia in modulating neurological circuits including pain is poorly understood, and in that light, the role of Hes5+ astrocytes in this circuit is a key finding with broader potential impacts. However, the impact of this work is limited by incomplete evidence, notably the fact that acute restraint stress is generally anti-nociceptive rather than pro-nociceptive, and a lack of specificity in defining this novel circuit.

Reviewer #1 (Public review):

Summary

In this article, Kawanabe-Kobayashi et al., aim to examine the mechanisms by which stress can modulate pain in mice. They focus on the contribution of noradrenergic neurons (NA) of the locus coeruleus (LC). The authors use acute restraint stress as a stress paradigm and found that following one hour of restraint stress mice display mechanical hypersensitivity. They show that restraint stress causes the activation of LC NA neurons and the release of NA in the spinal cord dorsal horn (SDH). They then examine the spinal mechanisms by which LC→SDH NA produces mechanical hypersensitivity. The authors provide evidence that NA can act on alphaA1Rs expressed by a class of astrocytes defined by the expression of Hes (Hes+). Furthermore, they found that NA, presumably through astrocytic release of ATP following NA action on alphaA1Rs Hes+ astrocytes, can cause an adenosine-mediated inhibition of SDH inhibitory interneurons. They propose that this disinhibition mechanism could explain how restraint stress can cause the mechanical hypersensitivity they measured in their behavioral experiments.

Strengths:

(1) Significance. Stress profoundly influences pain perception; resolving the mechanisms by which stress alters nociception in rodents may explain the well-known phenomenon of stress-induced analgesia and/or facilitate the development of therapies to mitigate the negative consequences of chronic stress on chronic pain.

(2) Novelty. The authors' findings reveal a crucial contribution of Hes+ spinal astrocytes in the modulation of pain thresholds during stress.

(3) Techniques. This study combines multiple approaches to dissect circuit, cellular, and molecular mechanisms including optical recordings of neural and astrocytic Ca2+ activity in behaving mice, intersectional genetic strategies, cell ablation, optogenetics, chemogenetics, CRISPR-based gene knockdown, slice electrophysiology, and behavior.

Weaknesses:

(1) Mouse model of stress. Although chronic stress can increase sensitivity to somatosensory stimuli and contribute to hyperalgesia and anhedonia, particularly in the context of chronic pain states, acute stress is well known to produce analgesia in humans and rodents. The experimental design used by the authors consists of a single one-hour session of restraint stress followed by 30 min to one hour of habituation and measurement of cutaneous mechanical sensitivity with von Frey filaments. This acute stress behavioral paradigm corresponds to the conditions in which the clinical phenomenon of stress-induced analgesia is observed in humans, as well as in animal models. Surprisingly, however, the authors measured that this acute stressor produced hypersensitivity rather than antinociception. This discrepancy is significant and requires further investigation.

(2) Specifically, is the hypersensitivity to mechanical stimulation also observed in response to heat or cold on a hotplate or coldplate?

(3) Using other stress models, such as a forced swim, do the authors also observe acute stress-induced hypersensitivity instead of stress-induced antinociception?

(4) Measurement of stress hormones in blood would provide an objective measure of the stress of the animals.

(5) Results:

a) Optical recordings of Ca2+ activity in behaving rodents are particularly useful to investigate the relationship between Ca2+ dynamics and the behaviors displayed by rodents.

b) The authors report an increase in Ca2+ events in LC NA neurons during restraint stress: Did mice display specific behaviors at the time these Ca2+ events were observed such as movements to escape or orofacial behaviors including head movements or whisking?

c) Additionally, are similar increases in Ca2+ events in LC NA neurons observed during other stressful behavioral paradigms versus non-stressful paradigms?

d) Neuronal ablation to reveal the function of a cell population.

e) The proportion of LC NA neurons and LC→SDH NA neurons expressing DTR-GFP and ablated should be quantified (Figures 1G and J) to validate the methods and permit interpretation of the behavioral data (Figures 1H and K). Importantly, the nocifensive responses and behavior of these mice in other pain assays in the absence of stress (e.g., hotplate) and a few standard assays (open field, rotarod, elevated plus maze) would help determine the consequences of cell ablation on processing of nociceptive information and general behavior.

f) Confirmation of LC NA neuron function with other methods that alter neuronal excitability or neurotransmission instead of destroying the circuit investigated, such as chemogenetics or chemogenetics, would greatly strengthen the findings. Optogenetics is used in Figure 1M, N but excitation of LC→SDH NA neuron terminals is tested instead of inhibition (to mimic ablation), and in naïve mice instead of stressed mice.

g) Alpha1Ars. The authors noted that "Adra1a mRNA is also expressed in INs in the SDH".

h) The authors should comprehensively indicate what other cell types present in the spinal cord and neurons projecting to the spinal cord express alpha1Ars and what is the relative expression level of alpha1Ars in these different cell types.

i) The conditional KO of alpha1Ars specifically in Hes5+ astrocytes and not in other cell types expressing alpha1Ars should be quantified and validated (Figure 2H).

j) Depolarization of SDH inhibitory interneurons by NA (Figure 3). The authors' bath applied NA, which presumably activates all NA receptors present in the preparation.

k) The authors' model (Figure 4H) implies that NA released by LC→SDH NA neurons leads to the inhibition of SDH inhibitory interneurons by NA. In other experiments (Figure 1L, Figure 2A), the authors used optogenetics to promote the release of endogenous NA in SDH by LC→SDH NA neurons. This approach would investigate the function of NA endogenously released by LC NA neurons at presynaptic terminals in the SDH and at physiological concentrations and would test the model more convincingly compared to the bath application of NA.

l) As for other experiments, the proportion of Hes+ astrocytes that express hM3Dq, and the absence of expression in other cells, should be quantified and validated to interpret behavioral data.

m) Showing that the effect of CNO is dose-dependent would strengthen the authors' findings.

n) The proportion of SG neurons for which CNO bath application resulted in a reduction in recorded sIPSCs is not clear.

o) A1Rs. The specific expression of Cas9 and guide RNAs, and the specific KD of A1Rs, in inhibitory interneurons but not in other cell types expressing A1Rs should be quantified and validated.

(6) Methods:

It is unclear how fiber photometry is performed using "optic cannula" during restraint stress while mice are in a 50ml falcon tube (as shown in Figure 1A).

Reviewer #2 (Public review):

Summary:

This study investigates the role of spinal astrocytes in mediating stress-induced pain hypersensitivity, focusing on the LC (locus coeruleus)-to-SDH (spinal dorsal horn) circuit and its mechanisms. The authors aimed to delineate how LC activity contributes to spinal astrocytic activation under stress conditions, explore the role of noradrenaline (NA) signaling in this process, and identify the downstream astrocytic mechanisms that influence pain hypersensitivity.

The authors provide strong evidence that 1-hour restraint stress-induced pain hypersensitivity involves the LC-to-SDH circuit, where NA triggers astrocytic calcium activity via alpha1a adrenoceptors (alpha1aRs). Blockade of alpha1aRs on astrocytes - but not on Vgat-positive SDH neurons - reduced stress-induced pain hypersensitivity. These findings are rigorously supported by well-established behavioral models and advanced genetic techniques, uncovering the critical role of spinal astrocytes in modulating stress-induced pain.

However, the study's third aim - to establish a pathway from astrocyte alpha1aRs to adenosine-mediated inhibition of SDH-Vgat neurons - is less compelling. While pharmacological and behavioral evidence is intriguing, the ex vivo findings are indirect and lack a clear connection to the stress-induced pain model. Despite these limitations, the study advances our understanding of astrocyte-neuron interactions in stress-pain contexts and provides a strong foundation for future research into glial mechanisms in pain hypersensitivity.

Strengths:

The study is built on a robust experimental design using a validated 1-hour restraint stress model, providing a reliable framework to investigate stress-induced pain hypersensitivity. The authors utilized advanced genetic tools, including retrograde AAVs, optogenetics, chemogenetics, and subpopulation-specific knockouts, allowing precise manipulation and interrogation of the LC-SDH circuit and astrocytic roles in pain modulation. Clear evidence demonstrates that NA triggers astrocytic calcium activity via alpha1aRs, and blocking these receptors effectively reduces stress-induced pain hypersensitivity.

Weaknesses:

Despite its strengths, the study presents indirect evidence for the proposed NA-to-astrocyte(alpha1aRs)-to-adenosine-to-SDH-Vgat neurons pathway, as the link between astrocytic adenosine release and stress-induced pain remains unclear. The ex vivo experiments, including NA-induced depolarization of Vgat neurons and chemogenetic stimulation of astrocytes, are challenging to interpret in the stress context, with the high CNO concentration raising concerns about specificity. Additionally, the role of astrocyte-derived D-serine is tangential and lacks clarity regarding its effects on SDH Vgat neurons. The astrocyte calcium signal "dip" after LC optostimulation-induced elevation are presented without any interpretation.

Reviewer #3 (Public review):

Summary

This is an exciting and timely study addressing the role of descending noradrenergic systems in nocifensive responses. While it is well-established that spinally released noradrenaline (aka norepinephrine) generally acts as an inhibitory factor in spinal sensory processing, this system is highly complex. Descending projections from the A6 (locus coeruleus, LC) and the A5 regions typically modulate spinal sensory processing and reduce pain behaviours, but certain subpopulations of LC neurons have been shown to mediate pronociceptive effects, such as those projecting to the prefrontal cortex (Hirshberg et al., PMID: 29027903).

The study proposes that descending cerulean noradrenergic neurons potentiate touch sensation via alpha-1 adrenoceptors on Hes5+ spinal astrocytes, contributing to mechanical hyperalgesia. This finding is consistent with prior work from the same group (dd et al., PMID:). However, caution is needed when generalising about LC projections, as the locus coeruleus is functionally diverse, with differences in targets, neurotransmitter co-release, and behavioural effects. Specifying the subpopulations of LC neurons involved would significantly enhance the impact and interpretability of the findings.

Strengths

The study employs state-of-the-art molecular, genetic, and neurophysiological methods, including precise CRISPR and optogenetic targeting, to investigate the role of Hes5+ astrocytes. This approach is elegant and highlights the often-overlooked contribution of astrocytes in spinal sensory gating. The data convincingly support the role of Hes5+ astrocytes as regulators of touch sensation, coordinated by brain-derived noradrenaline in the spinal dorsal horn, opening new avenues for research into pain and touch modulation.

Furthermore, the data support a model in which superficial dorsal horn (SDH) Hes5+ astrocytes act as non-neuronal gating cells for brain-derived noradrenergic (NA) signalling through their interaction with substantia gelatinosa inhibitory interneurons. Locally released adenosine from NA-stimulated Hes5+ astrocytes, following acute restraint stress, may suppress the function of SDH-Vgat+ inhibitory interneurons, resulting in mechanical pain hypersensitivity. However, the spatially restricted neuron-astrocyte communication underlying this mechanism requires further investigation in future studies.

Weaknesses

(1) Specificity of the LC Pathway targeting

The main concern lies with how definitively the LC pathway was targeted. Were other descending noradrenergic nuclei, such as A5 or A7, also labelled in the experiments? The authors must convincingly demonstrate that the observed effects are mediated exclusively by LC noradrenergic terminals to substantiate their claims (i.e. "we identified a circuit, the descending LC→SDH-NA neurons").

a) For instance, the direct vector injection into the LC likely results in unspecific effects due to the extreme heterogeneity of this nucleus and retrograde labelling of the A5 and A7 nuclei from the LC (i.e., Li et al., PMID: 26903420).

b) It is difficult to believe that the intersectional approach described in the study successfully targeted LC→SDH-NA neurons using AAVrg vectors. Previous studies (e.g., PMID: 34344259 or PMID: 36625030) demonstrated that similar strategies were ineffective for spinal-LC projections. The authors should provide detailed quantification of the efficiency of retrograde labelling and specificity of transgene expression in LC neurons projecting to the SDH.

c) Furthermore, it is striking that the authors observed a comparably strong phenotypical change in Figure 1K despite fewer neurons being labelled, compared to Figure 1H and 1N with substantially more neurons being targeted. Interestingly, the effect in Figure 1K appears more pronounced but shorter-lasting than in the comparable experiment shown in Figure 1H. This discrepancy requires further explanation.

d) A valuable addition would be staining for noradrenergic terminals in the spinal cord for the intersectional approach (Figure 1J), as done in Figures 1F/G. LC projections terminate preferentially in the SDH, whereas A5 projections terminate in the deep dorsal horn (DDH). Staining could clarify whether circuits beyond the LC are being ablated.

e) Furthermore, different LC neurons often mediate opposite physiological outcomes depending on their projection targets-for example, dorsal LC neurons projecting to the prefrontal cortex PFCx are pronociceptive, while ventral LC neurons projecting to the SC are antinociceptive (PMIDs: 29027903, 34344259, 36625030). Given this functional diversity, direct injection into the LC is likely to result in nonspecific effects.

Conclusion on Specificity: The authors are strongly encouraged to address these limitations directly, as they significantly affect the validity of the conclusions regarding the LC pathway. Providing more robust evidence, acknowledging experimental limitations, and incorporating complementary analyses would greatly strengthen the manuscript.

(2) Discrepancies in Data

a) Figures 1B and 1E: The behavioural effect of stress on PWT (Figure 1E) persists for 120 minutes, whereas Ca²⁺ imaging changes (Figure 1B) are only observed in the first 20 minutes, with signal attenuation starting at 30 minutes. This discrepancy requires clarification, as it impacts the proposed mechanism.

b) Figure 4E: The effect is barely visible, and the tissue resembles "Swiss cheese," suggesting poor staining quality. This is insufficient for such an important conclusion. Improved staining and/or complementary staining (e.g., cFOS) are needed. Additionally, no clear difference is observed between Stress+Ab stim. and Stress+Ab stim.+CPT, raising doubts about the robustness of the data.

c) Discrepancy with Existing Evidence: The claim regarding the pronociceptive effect of LC→SDH-NAergic signalling on mechanical hypersensitivity contrasts with findings by Kucharczyk et al. (PMID: 35245374), who reported no facilitation of spinal convergent (wide-dynamic range) neuron responses to tactile mechanical stimuli, but potent inhibition to noxious mechanical von Frey stimulation. This discrepancy suggests alternative mechanisms may be at play and raises the question of why noxious stimuli were not tested.

(3) Sole reliance on Von Frey testing

The exclusive use of von Frey as a behavioural readout for mechanical sensitisation is a significant limitation. This assay is highly variable, and without additional supporting measures, the conclusions lack robustness. Incorporating other behavioural measures, such as the adhesive tape removal test to evaluate tactile discomfort, the needle floor walk corridor to assess sensitivity to uneven or noxious surfaces, or the kinetic weight-bearing test to measure changes in limb loading during movement, could provide complementary insights. Physiological tests, such as the Randall-Selitto test for noxious pressure thresholds or CatWalk gait analysis to evaluate changes in weight distribution and gait dynamics, would further strengthen the findings and allow for a more comprehensive assessment of mechanical sensitisation.

Overall Conclusion

This study addresses an important and complex topic with innovative methods and compelling data. However, the conclusions rely on several assumptions that require more robust evidence. Specificity of the LC pathway, experimental discrepancies, and methodological limitations (e.g., sole reliance on von Frey) must be addressed to substantiate the claims. With these issues resolved, this work could significantly advance our understanding of astrocytic and noradrenergic contributions to pain modulation.

eLife Assessment

This is a useful follow-up on previous work on the same LGI1-ADAM22 complex using cross-linking to stabilize a trimeric state that the authors had previously observed by SEC-MALS and small-angle X-ray scattering (the previous crystal structure was determined in a dimeric form). A strength of this solid work is that oligomeric states do not affect the critical interaction between LGI1 and ADAM23, so the previous conclusions are still valid. A weakness is that the physiological relevance of the trimeric assembly is unclear.

Reviewer #1 (Public review):

The structure of a heterohexameric 3:3 LGI1-ADAM22 complex is resolved by Yamaguchi et al. It reveals the intermolecular LGI1 interactions and their role in bringing three ADAM22 molecules together. This may be relevant for the clustering of axonal Kv1 channels and control over their density. While it is currently not clear if the heterohexameric 3:3 LGI1-ADAM22 complex has a physiological role, the detailed structural information, presented here, allows us to pinpoint mutations or other strategies to probe the relevance of the 3:3 complex in future work.

The experimental work is done to a high standard, and I have no comments on that part. I do have several recommendations that I hope will be considered.

(1) A previously determined 2:2 heterodimeric complex of LGI1-ADAM22 was suggested to play a role in trans interactions. Could the authors discuss if the heterohexameric 3:3 LGI1-ADAM22 is more likely to represent a cis complex or a trans complex, or if both are possible?

(2) It is not entirely clear to me if the LGI1-ADAM22 complex is also crosslinked in the HS-AFM experiments. Could this be more clearly indicated? In addition, if this is the case, could an explanation be given about how the complex can still dissociate?

(3) The LGI1 and ADAM22 are of similar size. To me, this complicates the interpretation of dissociation of the complex in the HS-AFM data. How is the overinterpretation of this data prevented? In other words, what confidence do the authors have in the dissociation steps in the HS-AFM data?

(4) What is the "LGI1 collapse" mentioned in Figure 4c?

(5) Am I correct that the structure indicates that the trimerization is entirely organized by LGI1? This would suggest LGI1 trimerizes on its own. Can this be discussed? Has this been observed?

(6) C3 symmetry was not applied in the cryo-EM reconstruction of the heterohexameric 3:3 LGI1-ADAM22 complex. How much is the complex deviating from C3 symmetry? What interactions stabilize the specific trimeric conformation reconstructed here, compared to other trimeric conformations?

Reviewer #2 (Public review):

Summary:

The study by Yamaguchi et al. provides compelling evidence for the formation of a 3:3 complex between the ectodomain of ADAM22 and LGI1, as demonstrated using single-particle cryo-EM and HS-AFM. This represents the first instance in which the 3:3 complex has been resolved sufficiently to enable molecular modeling, allowing the authors to identify key interfaces mediating ADAM22-LGI1 interactions. HS-AFM revealed weak interactions within the 3:3 complexes, suggesting the dynamic nature of ADAM22-LGI1 interactions, which may play a role in modulating synaptic activity.

Strength:

A strength of this study lies in the novel identification of the 3:3 complexes, captured at an unprecedented level of resolution and validated by HS-AFM. This discovery, together with the authors' previous findings demonstrating a 2:2 stoichiometry, gives rise to an intriguing hypothesis regarding the dynamic nature of the ADAM22-LGI1 complex in regulating both cis- and trans-synaptic interactions.

Weakness:

The functional significance of these two complexes in the context of synapse remains speculative. Additionally, the structural presentations in Figures 1-3 (especially Figures 2-3) lack the clarity needed for general readers to fully understand the authors' key points. Enhancing the quality of these visual representations would greatly improve accessibility and comprehension.

eLife Assessment

This paper presents the important finding that BNIP3/NIX, a mitophagy receptor, and its binding to ATG18 are required for mitophagy during muscle cell reorganization in Drosophila. Although the involvement of the BNIP3-ATG18/WIPI axis in mitophagy induction has been reported in mammalian cell culture systems, this study provides the first compelling evidence for this pathway in vivo in animals. The physiological significance of this BNIP3-dependent mitophagy will require further investigation.

Reviewer #1 (Public review):

Summary:

During early Drosophila pupal development, a subset of larval abdominal muscles (DIOMs) is remodelled using an autophagy-dependent mechanism.

To better understand this not very well studied process, the authors have generated a transcriptomics time course using dissected abdominal muscles of various stages from wild-type and autophagy-deficient mutants. The authors have further identified a function for BNIP3 in muscle mitophagy using this system.

Strengths:

(1) The paper does provide a detailed mRNA time course resource for DIOM remodelling.

(2) The paper does find an interesting BNIP3 loss of function phenotype, a block of mitophagy during muscle remodelling, and hence identifies a specific linker between mitochondria and the core autophagy machinery. This adds to the mechanism of how mitochondria are degraded.

(3) Sophisticated fly genetics demonstrates that the larval muscle mitochondria are, to a large extent, degraded by autophagy during DIOM remodelling.

Weaknesses:

(1) Mitophagy during DIOM remodelling is not novel (earlier papers from Fujita et al.).

(2) The transcriptomics time course data are not well connected to the autophagy part. Both could be separated into 2 independent manuscripts.

(3) The muscle phenotypes need better quantifications, both for the EM and light microscopy data in various figures.

(4)The transcriptomics data are hard to browse in the provided PDF format.

Reviewer #2 (Public review):

Summary:

Autophagy (macroautophagy) is known to be essential for muscle function in flies and mammals. To date, many mitophagy (selective mitochondrial autophagy) receptors have been identified in mammals and other species. While the loss of mitophagy receptors has been shown to impair mitochondrial degradation (e.g., OPTN and NDP52 in Parkin-mediated mitophagy and NIX and BNIP3 in hypoxia-induced mitophagy) at the level of cultured cells, it remains unclear, especially under physiological conditions in vivo. In this study, the authors revealed that one of the receptors BNIP3 plays a critical role in mitochondrial degradation during muscle remodeling in vivo.

Overall, the manuscript provides solid evidence that BNIP3 is involved in mitophagy during muscle remodeling with in vivo analyses performed. In particular, all experiments in this study are well-designed. The text is well written and the figures are very clear.

Strengths:

(1) In each experiment, appropriate positive and negative controls are used to indicate what is responsible for the phenomenon observed by the authors: e.g. FIP200, Atg18, Stx17 siRNAs during DIOM remodeling in Figure 2 and Full, del-LIR, del-MER in Figure 5.

(2) Although the transcriptional dynamics of DIOM remodeling during metamorphosis is autophagy-independent, the transcriptome data obtained by the authors would be valuable for future studies.

(3) In addition to the simple observation that loss of BNIP3 causes mitochondrial accumulation, the authors further observed that, by combining siRNA against STX17, which is required for fusion of autophagosomes with lysosomes, BNIP3 KO abolishes mitophagosome formation, which will provide solid evidence for BNIP3-mediated mitophagy. Furthermore, using a Gal80 temperature-sensitive approach, the authors showed that mitochondria derived from larval muscle, but not those synthesized during hypertrophy, remain in BNIP3 KO fly muscles.

Weaknesses:

(1) Because BNIP3 KO causes mitochondrial accumulation, it is expected that adult flies will have some physiological defects, but this has not been fully analyzed or sufficiently mentioned in the manuscript.

(2) In Figure 5, the authors showed that BNIP3 binds to Atg18a by co-IP, but no data are provided on whether MER-mut or del-MER attenuates the affinity for Atg18a.

Reviewer #3 (Public review):

Summary:

Fujita et al build on their earlier, 2017 eLife paper that showed the role of autophagy in the developmental remodeling of a group of muscles (DIOM) in the abdomen of Drosophila. Most larval muscles undergo histolysis during metamorphosis, while DIOMs are programmed to regrow after initial atrophy to give rise to temporary adult muscles, which survive for only 1 day after eclosion of the adult flies (J Neurosci. 1990;10:403-1. and BMC Dev Biol 16, 12, 2016). The authors carry out transcriptomics profiling of these muscles during metamorphosis, which is in agreement with the atrophy and regrowth phases of these muscles. Expression of the known mitophagy receptor BNIP3/NIX is high during atrophy, so the authors have started to delve more into the role of this protein/mitophagy in their model. BNIP3 KO indeed impairs mitophagy and muscle atrophy, which they convincingly demonstrate via nice microscopy images. They also show that the already known Atg8a-binding LIR and Atg18a-binding MER motifs of human NIX are conserved in the Drosophila protein, although the LIR turned out to be less critical for in vivo protein function than the MER motif.

Strengths:

Established methodology, convincing data, in vivo model.

Weaknesses:

The significance for Drosophila physiology and for human muscles remains to be established.

eLife Assessment

This paper provides a compelling and rigorous quantitative analysis of the turnover and maintenance of CD4+ tissue-resident memory T cell clones, in the skin and the lamina propria. It provides a fundamental advance in our understanding of CD4 T cell regulation. Interestingly, in both tissues, maintenance involves an influx from progenitors on the time scale of months. The evidence that is based on fate mapping and mathematical inference is strong, although open questions on the interpretation of the Ki67-based fate mapping remain.

Reviewer #1 (Public review):

Summary:

Compelling and clearly described work that combines two elegant cell fate reporter strains with mathematical modelling to describe the kinetics of CD4+ TRM in mice. The aim is to investigate the cell dynamics underlying the maintenance of CD4+TRM.

The main conclusions are that:<br /> (1) CD4+ TRM are not intrinsically long-lived.<br /> (2) Even clonal half-lives are short: 1 month for TRM in skin, and even shorter (12 days) for TRM in lamina propria.<br /> (3) TRM are maintained by self-renewal and circulating precursors.

Strengths:

(1) Very clearly and succinctly written. Though in some places too succinctly! See suggestions below for areas I think could benefit from more detail.

(2) Powerful combination of mouse strains and modelling to address questions that are hard to answer with other approaches.

(3) The modelling of different modes of recruitment (quiescent, neutral, division linked) is extremely interesting and often neglected (for simpler neutral recruitment).

Weaknesses/scope for improvement:

(1) The authors use the same data set that they later fit for generating their priors. This double use of the same dataset always makes me a bit squeamish as I worry it could lead to an underestimate of errors on the parameters. Could the authors show plots of their priors and posteriors to check that the priors are not overly-influential? Also, how do differences in priors ultimately influence the degree of support a model gets (if at all)? Could differences in priors lead to one model gaining more support than another?

(2) The authors state (line 81) that cells were "identified as tissue-localised by virtue of their protection from short-term in vivo labelling (Methods; Fig. S1B)". I would like to see more information on this. How short is short term? How long after labelling do cells need to remain unlabelled in order to be designated tissue-localised (presumably label will get to tissue pretty quickly -within hours?). Can the authors provide citations to defend the assumption that all label-negative cells are tissue-localised (no false negatives)? And conversely that no label-positive cells can be found in the tissue (no false positives)? I couldn't actually find the relevant section in the methods and Figure S1B didn't contain this information.

(3) Are the target and precursor populations from the same mice? If so is there any way to reflect the between-individual variation in the precursor population (not captured by the simple empirical fit)? I am thinking particularly of the skin and LP CD4+CD69- populations where the fraction of cells that are mTOM+ (and to a lesser extent YFP+) spans virtually the whole range. Would it be nice to capture this information in downstream predictions if possible?

(4) In Figure 3, estimates of kinetics for cells in LP appear to be more dependent on the input model (quiescent/neutral/division-linked) than the same parameters in the skin. Can the authors explain intuitively why this is the case?

(5) Can the authors include plots of the model fits to data associated with the different strengths of support shown in Figure 4? That is, I would like to know what a difference in the strength of say 0.43 compared with 0.3 looks like in "real terms". I feel strongly that this is important. Are all the fits fantastic, and some marginally better than others? Are they all dreadful and some are just less dreadful? Or are there meaningful differences?

(6) Figure 4 left me unclear about exactly which combinations of precursors and targets were considered. Figure 3 implies there are 5 precursors but in Figure 4A at most 4 are considered. Also, Figure 4B suggests skin CD69- were considered a target. This doesn't seem to be specified anywhere.

Reviewer #2 (Public review):

This manuscript addresses a fundamental problem of immunology - the persistence mechanisms of tissue-resident memory T cells (TRMs). It introduces a novel quantitative methodology, combining the in vivo tracing of T-cell cohorts with rigorous mathematical modeling and inference. Interestingly, the authors show that immigration plays a key role in maintaining CD4+ TRM populations in both skin and lamina propria (LP), with LP TRMs being more dependent on immigration than skin TRMs. This is an original and potentially impactful manuscript. However, several aspects were not clear and would benefit from being explained better or worked out in more detail.

(1) The key observations are as follows:

a) When heritably labeling cells due to CD4 expression, CD4+ TRM labeling frequency declines with time. This implies that CD4+ TRMs are ultimately replenished from a source not labeled, hence not expressing CD4. Most likely, this would be DN thymocytes.

b) After labeling by Ki67 expression, labeled CD4+ TRMs also decline - This is what Figure 1B suggests. Hence they would be replaced by a source that was not in the cell cycle at the time of labeling. However, is this really borne out by the experimental data (Figure 2C, middle row)? Please clarify.

(2) For potential source populations (Figure 2D): Please discuss these data critically. For example, CD4+ CD69- cells in skin and LP start with a much lower initial labeling frequency than the respective TRM populations. Could the former then be precursors of the latter? A similar question applies to LN YFP+ cells. Moreover, is the increase in YFP labeling in naïve T cells a result of their production from proliferative thymocytes? How well does the quantitative interpretation of YFP labeling kinetics in a target population work when populations upstream show opposite trends (e.g., naïve T cells increasing in YFP+ frequency but memory cells in effect decreasing, as, at the time of labeling, non-activated = non-proliferative T cells (and hence YFP-) might later become activated and contribute to memory)?

(3) Please add a measure of variation (e.g., suitable credible intervals) to the "best fits" (solid lines in Figure 2).

(4) Could the authors better explain the motivation for basing their model comparisons on the Leave-One-Out (LOO) cross-validation method? Why not use Bayesian evidence instead?

eLife Assessment

This study approaches an important topic providing insight into the neuronal circuitry that interconnects memory consolidation and sleep. The data were collected and analysed using a solid methodology, contributing new findings for neurobiologists working on how memories are stored and the roles of sleep. However, the data is incomplete to support the proposed role of the PAM-DPM circuits as the link between sleep state and long-term memory consolidation.

Reviewer #1 (Public review):

Summary:

The authors aim to use state-of-the art behaviour, imaging, and connectome techniques to identify the neural interaction between sleep and long-term memory consolidation in the PAM-DPM circuits, a well-known dopaminergic pathway within Drosophila Mushroom Body.

Strengths:

From a Drosophila sleep researcher's perspective, the investigation follows a clear and logical strategy to collect a huge dataset of sleep, appetitive memory, and live imaging. The authors clearly identified and showed that activation of a PAM subset: alpha-1 reduces sleep quality and memory consolidation in a starvation-dependent manner. The authors also convincingly demonstrated the corresponding neuronal responses of DPM neurons following PAM alpha-1 activation, and the positive role of DPM neural activity in sleep and memory consolidation. Moreover, the authors applied a new way of sleep statistics to demonstrate hour-by-hour changes between treatment and genotypes. Importantly, the authors demonstrated that memory loss derived from PAM alpha 1 activation can be partly restored by ectopic sleep enhancement via feeding THIP during the memory consolidation period after training.

Weaknesses:

Two investigatory gaps relate to the misalignment between circuital activity and behaviours, due to the nature of large circuital functional analysis like this. Firstly, the central observation of the study indicates that PAM alpha1 activation causes DPM inhibition which disrupts sleep and memory consolidation. Therefore one would expect a reduced PAMalpha1 and increased DPM activities after memory training, but the authors found that the endogenous CRTC::GFP reported neuronal activity for PAMalpha1 and DPM are both increased after memory training (Figure 9). This can be due to the difficult functional demarcation among the 14 PAMalpha1 projections. Secondly, the authors acknowledged the contradicting finding that memory defect is detected in PAMalpha1 inactivation (Figure 7C), yet suggested a tight link between sleep and memory consolidation; it is clear loss of PAM subset activity can disrupt memory consolidation without affecting sleep (cf Figure 7C and 7I).

Reviewer #2 (Public review):

Summary:

Sleep plays a critical role in memory consolidation, but the neural mechanisms underlying this relationship remain poorly understood. The authors present novel findings implicating two small neuronal groups with inhibitory connections, PAM-a1 to DPM, in sleep regulation and LTM consolidation. However, whether the PAM-a1 to DPM microcircuit promotes LTM consolidation through sleep regulation requires further investigation.

Strengths:

The authors report several novel findings. Brief activation or inhibition of PAM-a1 neurons, or brief inhibition of DPM neurons during the first few hours after training, impairs 24-hour LTM. Notably, these brief manipulations disrupt sleep for many hours afterward, particularly at night. Interestingly, disruption of PAM-a1 and DPM neurons impairs sleep and appetitive memory consolidation only under starvation conditions, and pharmacological induction of sleep during the night rescues the LTM defects. These findings suggest that PAM-a1 and DPM neurons are involved in sleep regulation and LTM consolidation under starvation. These are important findings that advance our understanding of the link between sleep and memory consolidation.

Weaknesses:

Some claims lack sufficient evidence or clarity:

(1) All sleep experiments are conducted under the "training" (temperature-change) condition. While genotypic controls are helpful, additional no-training controls are required to confirm that the observed differences are due to training rather than unknown genotype-related factors. The fact that experimental genotypes exhibit significantly altered sleep even before "training" (e.g., Figs. 7H, J, K, 8A, B, D) highlights the necessity of these controls.

(2) Previous studies on disrupted memory due to sleep reduction have primarily examined conditions with severe sleep deprivation. In contrast, this report claims that relatively small decreases in total sleep accompanied by sleep fragmentation are responsible for impaired memory consolidation. It remains unclear whether sleep fragmentation at this level is truly critical for memory consolidation. The authors should cause sleep loss and fragmentation of similar magnitude through other means and determine whether it can impair LTM.

(3) The authors employed a neural activity reporter to show that starvation increases the basal activity of PAM-a1 but not DPM neurons in untrained flies (Figures 9C-E). They observed small increases in the activity of both neuron groups immediately after training but not one hour later. Given the inhibitory connection from PAM-a1 to DPM, it is unclear why both neuron groups show increased activity after training. Additionally, as the authors acknowledge, it is puzzling how the inactivation of PAM-a1 produces similar effects on sleep and memory as DPM inhibition and PAM-a1 activation. Further experiments are needed to clarify these findings, such as manipulating PAM-a1 activity during the one-hour post-training period and evaluating the effect on DPM activity. Including data from training under fed conditions would provide a more comprehensive understanding of state-dependent neural activity. Even if certain experiments are not feasible, these issues warrant further discussion. It is also important to clarify that the term "synchronized" does not imply single-spike-level synchrony.

(4) The authors considered that PAM-a1 and DPM might function in parallel, independent pathways for sleep and LTM. They rejected this possibility based on the lack of additive effects when both neuronal groups were simultaneously inactivated. However, they found that MB299B-labelled neurons exert stronger memory effects than MB043B-labelled neurons, while MB043B neurons have stronger sleep effects. If sleep is a primary driver of memory consolidation, a stronger correlation between memory and sleep effects would be expected. This observation merits further discussion.

(5) Given prior knowledge that PAM neurons are heterogeneous and that the R58E02 driver is broadly expressed, data in Figures 1-5 concerning PAM are outdated. The use of more restricted PAM-a1 drivers from the outset would make the manuscript easier to read and interpret.

(6) Some figures lack relevant data, certain experiments are missing necessary controls, and anomalies are present in some data sets.

Reviewer #3 (Public review):

Summary:

Understanding the neural circuits that link sleep and memory remains a fundamental challenge in neuroscience. In this study, Lin Yan and colleagues investigate how dopamine signaling in Drosophila regulates long-term memory (LTM) formation in the context of sleep. They identify a specific microcircuit between protocerebral anterior medial dopamine neurons (PAM-DANs) and dorsal paired medial (GABAergic DPM) neurons that modulates memory consolidation. Their findings suggest that disrupting the basal activity of PAM-α1 neurons during early consolidation impairs LTM, with particularly pronounced effects under starvation conditions. Notably, sleep fragmentation caused by this disruption can be pharmacologically rescued, restoring LTM. These results provide compelling evidence that dopamine signaling plays a crucial role in linking sleep and memory, offering new insights into the underlying mechanisms.

Strengths:

This study presents a well-executed investigation into sleep-memory interactions, utilizing a combination of connectomics, behavioral assays, functional imaging, and pharmacological manipulations. The authors convincingly demonstrate that the PAM-α1 and DPM circuits interact, highlighting a potential mechanism by which sleep influences memory consolidation. The anatomical and functional dissection of this circuit is of high interest to the field, and the study's integration of sleep and memory processes contributes significantly to our understanding of dopamine's role in cognitive functions.

Weaknesses:

While the study is well-designed and presents compelling findings, some aspects require further clarification. The interpretation of dopamine receptor signaling remains incomplete, particularly regarding inhibitory pathways. The role of DPM in memory consolidation is not entirely conclusive, as different genetic approaches yield variable results. Additionally, some inconsistencies in neuronal activity patterns and experimental variability, especially regarding sleep patterns or pharmacological rescue, should be addressed to strengthen the mechanistic framework.

Conclusion:

Overall, this study provides valuable new insights into how sleep and dopamine circuits interact to regulate memory consolidation. While the findings are compelling, addressing the points above-particularly receptor signaling and the specific role of DPM and its activity patterns within the microcircuit would further solidify the study's conclusions.

eLife Assessment

Lu and colleagues developed an important imaging protocol that combines expansion microscopy, light-sheet microscopy, and image segmentation for use with the planarian Schmidtea mediterranea, a powerful model system for regeneration. This represents a substantial improvement on current standards and enables more rapid data acquisition. The utility of this solid protocol is demonstrated by quantifying several aspects of this flatworm's neural anatomy and musculature during homeostasis and regeneration. This work will be of interest to researchers looking to implement more systematic approaches towards imaging and quantifying intact specimens.

Reviewer #1 (Public review):

Summary:

The planarian flatworm Schmidtea mediterranea is widely used as a model system for regeneration because of its remarkable ability to regenerate its entire body plan from very small fragments of tissue, including the complete and rapid regeneration of the CNS. Prior to this study, analysis of CNS regeneration in planaria has mostly been performed on a gross anatomical level. Lu et al. describe a careful and detailed analysis of the planarian neuroanatomy and musculature in both the homeostatic and regenerating contexts. To improve the effective resolution of their imaging, the authors optimized a tissue expansion protocol for planaria. Imaging was performed by light sheet microscopy, and the resulting optical sections were tiled to reconstruct whole worms. Labelled tissues and cells were then segmented to allow quantification of neurons, muscle fibers, and all cells in individual worms.

Strengths:

The resulting workflow can produce highly detailed and quantifiable 3D reconstructions at a rate that is fast enough to allow the analysis of large numbers of whole animals.

Weaknesses:

While Lu et al. have shown how their methodology and workflow can be used to image and quantify features from whole animals, it is unclear how well their technique as described will perform at sub-cellular resolutions based upon the data that they show.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors apply tissue expansion and tiling light sheet microscopy to study allometric growth and regeneration in planaria. They developed image analysis pipelines to help them quantify different neuronal subtypes and muscles in planaria of different sizes and during regeneration. Among the strengths of this work, the authors provide beautiful images that show the potential of the approaches they are taking and their ability to quantify specific cell types in relatively large numbers of whole animal samples. Many of their findings confirm previous results in the literature, which helps validate the techniques and pipelines they have applied here. Among their new observations, they find that the body wall muscles at the anterior and posterior poles of the worm are organized differently and show that the muscle pattern in the posterior head of beta-catenin RNAi worms resembles the anterior muscle pattern. They also show that glial cell processes appear to be altered in beta-catenin or insulin receptor-1 RNAi worms. Weaknesses include some over-interpretation of the data and lack of consideration or citation of relevant previous literature, as discussed below.

Strengths:

This method of tissue expansion will be useful for researchers interested in studying this experimental animal. The authors provide high-quality images that show the utility of this technique. Their analysis pipeline permits them to quantify cell types in relatively large numbers of whole animal samples.

The authors provide convincing data on changes in total neurons and neuronal sub-types in different-sized planaria. They report differences in body wall muscle pattern between the anterior and posterior poles of the planaria, and that these differences are lost when a posterior head forms in beta-catenin RNAi planaria. They also find that glial cell projections are reduced in insulin receptor-1 RNAi planaria.

Comments on revisions:

The authors have satisfactorily addressed the major concerns of the previous reviewers.

Author response:

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

Reviewer #1(Public review):

comment 1: Lu et al. use their workflow to visualize RNA expression of five enzymes that are each involved in the biosynthetic pathway of different neurotransmitters/modulators, namely chat (cholinergeric), gad (GABAergic), tbh (octopaminergic), th (dopaminergic), and tph (serotonergic). In this way, they generate an anatomical atlas of neurons that produce these molecules. Collectively these markers are referred to as the "neuronpool." They overstate when they write, "The combination of these five types of neurons constitutes a neuron pool that enables the labeling of all neurons throughout the entire body." This statement does not accurately represent the state of our knowledge about the diversity of neurons in S. mediterranea. There are several lines of evidence that support the presence of glutamatergic and glycinergic neurons, including the following. The glutamate receptor agonists NMDA and AMPA both produce seizure-like behaviors in S. mediterranea that are blocked by the application of glutamate receptor antagonists MK-801 and DNQX (which antagonize NMDA and AMPA glutamate receptors, respectively; Rawls et al., 2009). scRNA-Seq data indicates that neurons in S. mediterranea express a vesicular glutamate transporter, a kainite-type glutamate receptor, a glycine receptor, and a glycine transporter (Brunet Avalos and Sprecher, 2021; Wyss et al., 2022). Two AMPA glutamate receptors, GluR1 and GluR2, are known to be expressed in the CNS of another planarian species, D. japonica (Cebria et al., 2002). Likewise, there is abundant evidence for the presence of peptidergic neurons in S. mediterranea (Collins et al., 2010; Fraguas et al., 2012; Ong et al., 2016; Wyss et al., 2022; among others) and in D. japonica (Shimoyama et al., 2016). For these reasons, the authors should not assume that all neurons can be assayed using the five markers that they selected. The situation is made more complex by the fact that many neurons in S. mediterranea appear to produce more than one neurotransmitter/modulator/peptide (Brunet Avalos and Sprecher, 2021; Wyss et al., 2022), which is common among animals (Vaaga et al., 2014; Brunet Avalos and Sprecher, 2021). However the published literature indicates that there are substantial populations of glutamatergic, glycinergic, and peptidergic neurons in S. mediterranea that do not produce other classes of neurotransmission molecule (Brunet Avalos and Sprecher, 2021; Wyss et al., 2022). Thus it seems likely that the neuronpool will miss many neurons that only produce glutamate, glycine or a neuropeptide.

In response to your comments, we agree that our initial statement regarding the "neuron pool" overstated the extent of neuronal coverage provided by the five selected markers. We have revised the sentence as “The combination of these five types of neurons constitutes a neuron pool that enables the labeling of most of the neurons throughout the entire body, including the eyes, brain, and pharynx”.

Furthermore, we chose the five neurotransmitter systems (cholinergic, GABAergic, octopaminergic, dopaminergic, and serotonergic) based on their well-characterized roles in planarian neurobiology and the availability of reliable markers. However, we acknowledge the limitations of this approach and recognize that it does not encompass all neuron types, particularly those involved in glutamatergic, glycinergic, and peptidergic signaling, which have been documented in S. mediterranea. We have also added the content about other neuron types in our revised results section “Additionally, the neuron system of S. mediterranea is complex which characterized by considerable diversity among glutamatergic, glycinergic, and peptidergic neurons in planarians and many neurons in S. mediterranea express more than one neurotransmitter or neuropeptide, which adds further complexity to the system. We used five markers for a proof of concept illustration. By employing Fluorescence in Situ Hybridization (FISH), we successfully visualized a variety of planarian neurons, including cholinergic (chat⁺), serotonergic (tph⁺), octopaminergic (tbh⁺), GABAergic (gad⁺), and dopaminergic (th⁺) neurons based on their well-characterized roles in planarian neurobiology and the availability of reliable markers. (Figure S2A, Supplemental video 2) (Currie et al., 2016). The combination of these five types of neurons constitutes a neuron pool that enables the labeling of most of the neurons throughout the entire body, including the eyes, brain, and pharynx (Figure 1B).”

comment 2: The authors use their technique to image the neural network of the CNS using antibodies raised vs. Arrestin, Synaptotagmin, and phospho-Ser/Thr. They document examples of both contralateral and ipsilateral projections from the eyes to the brain in the optic chiasma (Figure 1C-F). These data all seem to be drawn from a single animal in which there appears to be a greater than normal number of nerve fiber defasciculatations. It isn't clear how well their technique works for fibers that remain within a nerve tract or the brain. The markers used to image neural networks are broadly expressed, and it's possible that most nerve fibers are too densely packed (even after expansion) to allow for image segmentation. The authors also show a close association between estrella-positive glial cells and nerve fibers in the optic chiasma.

Thank you for your detailed feedback. While we did not perform segmentation of all neuron fibers, we were able to segment more isolated fibers that were not densely packed within the neural tracts. We use 120 nm resolution to segment neurons along the three axes. Our data show the presence of both contralateral and ipsilateral projections of visual neurons. Although Figure 1C-F shows data from one planarian, we imaged three independent specimens to confirm the consistency of these observations. In the revised manuscript, we have included a discussion on the limitations of TLSM in reconstructing neural networks. In the discussion part, we added “It should be noted that the current resolution for our segmentation may be limited when resolving fibers within densely packed regions of the nerve tracts”.

comment 3: The authors count all cell types, neuron pool neurons, and neurons of each class assayed. They find that the cell number to body volume ratio remains stable during homeostasis (Figure S3C), and that the brain volume steadily increases with increasing body volume (Figure S3E). They also observe that the proportion of neurons to total body cells is higher in worms 2-6 mm in length than in worms 7-9 mm in length (Figure 2D, S3F). They find that the rate at which four classes of neurons (GABAergic, octopaminergic, dopaminergic, serotonergic) increase relative to the total body cell number is constant (Figure S3G-J). They write: "Since the pattern of cholinergic neurons is the major cell population in the brain, these results suggest that the above observation of the non-linear dynamics between neurons and cell numbers is likely from the cholinergic neurons." This conclusion should not be reached without first directly counting the number of cholinergic neurons and total body cells. Given that glutamatergic, glycinergic, and peptidergic neurons were not counted, it also remains possible that the non-linear dynamics are due (in part or in whole) to one or more of these populations.

We have revised the statement into “These results suggest that the above observation of the non-linear dynamics between neuron and total cell number is not likely from the octopaminergic, GABAergic, dopaminergic, and serotonergic neurons. Since our neuron pool may not include glutamatergic, glycinergic, and peptidergic neurons, the non-linear dynamics may be from cholinergic neurons or other neurons not included in our staining.”

Reviewer #2 (Public review):

Weaknesses:

(1) The proprietary nature of the microscope, protected by a patent, limits the technical details provided, making the method hard to reproduce in other labs.

Thank you for your comment. We understand the importance of reproducibility and transparency in scientific research. We would like to point out that the detailed design and technical specifications of the TLSM are publicly available in our published work: Chen et al., Cell Reports, 2020. Additionally, the protocol for C-MAP, including the specific experimental steps, is comprehensively described in the methods section of this paper. We believe that these resources should provide sufficient information for other labs to replicate the method.

(2) The resolution of the analyses is mostly limited to the cellular level, which does not fully leverage the advantages of expansion microscopy. Previous applications of expansion microscopy have revealed finer nanostructures in the planarian nervous system (see Fan et al. Methods in Cell Biology 2021; Wang et al. eLife 2021). It is unclear whether the current protocol can achieve a comparable resolution.

Thank you for raising this important point. The strength of our C-MAP protocol lies in its fluorescence-protective nature and user convenience. Notably, the sample can be expanded up to 4.5-fold linearly without the need for heating or proteinase digestion, which helps preserve fluorescence signals. In addition, the entire expansion process can be completed within 48 hours. While our current analysis focused on cellular-level structures, our method can achieve comparable or better resolution and we will add this information in the revised manuscript as “It is important to point out that the strength of our C-MAP protocol lies in its fluorescence-protective nature and user convenience. Notably, the sample can be expanded up to 4.5-fold linearly without the need for heating or proteinase digestion, which helps preserve fluorescence signals. In addition, the entire expansion process can be completed within 48 hours. Based on our research requirement, two spatial resolutions were adopted to image expanded planarians, 2×2×5 μm³ and 0.5×0.5×1.6 μm³. The resolution can be further improved to 500 nm and 120 nm, respectively.”

(3) The data largely corroborate past observations, while the novel claims are insufficiently substantiated.

A few major issues with the claims:

Line 303-304: While 6G10 is a widely used antibody to label muscle fibers in the planarian, it doesn't uniformly mark all muscle types (Scimone at al. Nature 2017). For a more complete view of muscle fibers, it is important to use a combination of antibodies targeting different fiber types or a generic marker such as phalloidin. This raises fundamental concerns about all the conclusions drawn from Figures 4 and 6 about differences between various muscle types. Additionally, the authors should cite the original paper that developed the 6G10 antibody (Ross et al. BMC Developmental Biology 2015).

We appreciate the reviewer’s insightful comments and acknowledge that 6G10 does not uniformly label all muscle fiber types. We agree that this limitation should be recognized in the interpretation of our results. We have revised the manuscript to explicitly state the limitations of using 6G10 alone for muscle fiber labeling and highlight the need for additional markers. We have included the following statement in the Results section: “It is noted that previous studies reported that 6G10 does not label all body wall muscles equivalently with the limitation of predominantly labeling circular and diagonal fibers (Scimone et al., 2017; Ross et al., 2015). Our observation may be limited by this preference”. We would also clarify that the primary objective of our study was to demonstrate the application of our 3D tissue reconstruction method in addressing traditional research questions. Nonetheless, we agree that expanding the labeling strategy in future studies would allow for a more thorough investigation of muscle fiber diversity. Relevant citations have been properly revised and updated.

(4) Lines 371-379: The claim that DV muscles regenerate into longitudinal fibers lacks evidence. Furthermore, previous studies have shown that TFs specifying different muscle types (DV, circular, longitudinal, and intestinal) both during regeneration and homeostasis are completely different (Scimone et al., Nature 2017 and Scimone et al., Current Biology 2018). Single-cell RNAseq data further establishes the existence of divergent muscle progenitors giving rise to different muscle fibers. These observations directly contradict the authors' claim, which is only based on images of fixed samples at a coarse time resolution.

Thank you for your valuable feedback. Our intent was not to suggest that DV muscles regenerate into longitudinal fibers. Our observations focused on the wound site, where DV muscle fibers appear to reconnect, and longitudinal fibers, along with other muscle types, gradually regenerate to restore the structure of the injured area. We have revised the our statement as:“During the regeneration process, DV muscle fibers reconnect at the wound site, with longitudinal fibers and other muscle types gradually restoring the structure at the anterior tip and later integrating with circular and diagonal fibers through small DV fiber branches (Figure S5O1-O3).”

(5) Line 423: The manuscript lacks evidence to claim glia guide muscle fiber branching.

We agree with your concerns that our statement may be overestimated. We have removed this statement from the revised version. Instead, we focused on describing our observations of the connections between glial cells and muscle fibers. We have revised the section as follows: “Considering the interaction between glial and muscle cells, the localization of estrella⁺ glia and muscle fibers is further investigated. By dual-staining of anti-Phospho (Ser/Thr) and 6G10 in inr-1 RNAi and β-catenin-1 RNAi planarians, we found that the morphologies of neurons are normal, and they have close contact with muscle fibers (Figure 6D, E). However, by dual staining of estrella and 6G10, we found that the structure of glial cells is star-shaped in egfp RNAi planarian, however, glial cells in inr-1 RNAi and β-catenin-1 RNAi planarians have shorter cytoplasmic projections, and their sizes are smaller, lacking the major projection onto the muscles (Figure 6D, E, Figure S6E-K). Especially, in the posterior head of β-catenin-1 RNAi planarians, the glial cell has few axons and can hardly connect with muscle fibers (Figure 6E). These results indicated that proper neuronal guidance and muscle fiber distribution could potentially contribute to facilitating accurate glial-to-muscle projections.

(6) Lines 432/478: The conclusion about neuronal and muscle guidance on glial projections is similarly speculative, lacking functional evidence. It is possible that the morphological defects of estrella+ cells after bcat1 RNAi are caused by Wnt signaling directly acting on estrella+ cells independent of muscles or neurons.

We understand that this approach is insufficient and we have revised the this section as follows: “Further investigation is required to distinguish the cell-autonomous and non-autonomous effects of inr-1 RNAi and β-catenin-1 RNAi on muscle and glial cells.”

(7) Finally, several technical issues make the results difficult to interpret. For example, in line 125, cell boundaries appear to be determined using nucleus images; in line 136, the current resolution seems insufficient to reliably trace neural connections, at least based on the images presented.

We use two setups for imaging cells and neuron projections. For cellular resolution imaging, we utilized a 1× air objective with a numerical aperture (NA) of 0.25 and a working distance of 60 mm (OLYMPUS MV PLAPO). The voxel size used was 0.8×0.8×2.5 μm³. This configuration resulted in a resolution of 2×2×5 μm³ and a spatial resolution of 0.5×0.5×1.25 μm³ with 4.5× isotropic expansion. Alternatively, for sub-cellular imaging, we employed a 10×0.6 SV MP water immersion objective with 0.8 NA and a working distance of 8 mm (OLYMPUS). The voxel size used in this configuration was 0.26×0.26×0.8 μm³. As a result of this configuration, we achieved a resolution of 0.5×0.5×1.6 μm³ and a spatial resolution of 0.12×0.12×0.4 μm³ with a 4.5× isotropic expansion. The higher resolution achieved with sub-cellular imaging allows us to observe finer structures and trace neural connections.

Regarding your question about cell boundaries, we have revised the manuscript to specify that the boundaries we identified are those of each nucleus.

Reviewer #3 (Public review):

Weaknesses:

(1) The work would have been strengthened by a more careful consideration of previous literature. Many papers directly relevant to this work were not cited. Such omissions do the authors a disservice because in some cases, they fail to consider relevant information that impacts the choice of reagents they have used or the conclusions they are drawing.

For example, when describing the antibody they use to label muscles (monoclonal 6G10), they do not cite the paper that generated this reagent (Ross et al PMCID: PMC4307677), and instead, one of the papers they do cite (Cebria 2016) that does not mention this antibody. Ross et al reported that 6G10 does not label all body wall muscles equivalently, but rather "predominantly labels circular and diagonal fibers" (which is apparent in Figure S5A-D of the manuscript being reviewed here). For this reason, the authors of the paper showing different body wall muscle populations play different roles in body patterning (Scimone et al 2017, PMCID: PMC6263039, also not cited in this paper) used this monoclonal in combination with a polyclonal antibody to label all body wall muscle types. Because their "pan-muscle" reagent does not label all muscle types equivalently, it calls into question their quantification of the different body wall muscle populations throughout the manuscript. It does not help matters that their initial description of the body wall muscle types fails to mention the layer of thin (inner) longitudinal muscles between the circular and diagonal muscles (Cebria 2016 and citations therein).

Ipsilateral and contralateral projections of the visual axons were beautifully shown by dye-tracing experiments (Okamoto et al 2005, PMID: 15930826). This paper should be cited when the authors report that they are corroborating the existence of ipsilateral and contralateral projections.

Thank you for your feedback. We have incorporated these citations and clarifications into the revised manuscript. We acknowledge the limitations of this approach and have added a statement for this limitation in the revised manuscript “It is noted that previous studies reported that 6G10 does not label all body wall muscles equivalently with the limitation of predominantly labeling circular and diagonal fibers (Scimone et al., 2017; Ross et al., 2015). Our observation may be limited by this preference.”

(2) The proportional decrease of neurons with growth in S. mediterranea was shown by counting different cell types in macerated planarians (Baguna and Romero, 1981; https://link.springer.com/article/10.1007/BF00026179) and earlier histological observations cited there. These results have also been validated by single-cell sequencing (Emili et al, bioRxiv 2023, https://www.biorxiv.org/content/10.1101/2023.11.01.565140v). Allometric growth of the planaria tail (the tail is proportionately longer in large vs small planaria) can explain this decrease in animal size. The authors never really discuss allometric growth in a way that would help readers unfamiliar with the system understand this.

Thank you for your feedback. We have incorporated these citations and clarifications into the revised manuscript “These findings provide evidence to support the previous prediction and consistency between different planarian species (Baguñà et al., 1981; Emili et al.,2023). Because the tail is proportionately longer in large than in small planarians, the allometric growth of the planarians can be one possibility for this decrease along with the increase in animal size. The phenomenon may also suggest the existence of a threshold in the increase of planarian neuron numbers, which may ultimately contribute to some physiological changes, such as planarian fission.”

(3) In some cases, the authors draw stronger conclusions than their results warrant. The authors claim that they are showing glial-muscle interactions, however, they do not provide any images of triple-stained samples labeling muscle, neurons, and glia, so it is impossible for the reader to judge whether the glial cells are interacting directly with body wall muscles or instead with the well-described submuscular nerve plexus. Their conclusion that neurons are unaffected by beta-cat or inr-1 RNAi based on anti-phospho-Ser/Thr staining (Fig. 6E) is unconvincing. They claim that during regeneration "DV muscles initially regenerate into longitudinal fibers at the anterior tip" (line 373). They provide no evidence for such switching of muscle cell types, so it is unclear why they say this.

We acknowledge that some of our conclusions were overclaimed given the current data, and we appreciate the opportunity to clarify and refine these claims in the revised manuscript. Due the technique reason, we have not achieved the triple-staining to address this concern. We hope to make a progress in our future studies. Regarding the statement that "DV muscles initially regenerate into longitudinal fibers at the anterior tip" (line 373), as addressed in our previous response, this statement was unclear. Our intent was not to imply that DV muscles switch into longitudinal fibers. Instead, we observed that muscle fibers reconnect at the wound site, with longitudinal fibers and other muscle types gradually restoring the structure. We have revised this section: “During the regeneration process, DV muscle fibers reconnect at the wound site, with longitudinal fibers and other muscle types gradually restoring the structure at the anterior tip and later integrating with circular and diagonal fibers through small DV fiber branches (Figure S5O1-O3).”

(4) The authors show how their automated workflow compares to manual counts using PI-stained specimens (Figure S1T). I may have missed it, but I do not recall seeing a similar ground truth comparison for their muscle fiber counting workflow. I mention this because the segmented image of the posterior muscles in Figure 4I seems to be missing the vast majority of circular fibers visible to the naked eye in the original image.

Thank you for raising this important point. We have included a ground truth comparison of our automated muscle fiber segmentation with the original image in the revised Figure S6. The original Figure S6 has been changed as Figure S7. Regarding the observation of missing circular fibers in Figure 4I, we agree that the segmentation appears to have missed a significant number of circular fibers in this particular image. This may have been due to limitations in the current parameters of the segmentation algorithm, especially in distinguishing fibers in regions of varying intensity or overlap.

(5) It is unclear why the abstract says, "We found the rate of neuron cell proliferation tends to lag..." (line 25). The authors did not measure proliferation in this work and neurons do not proliferate in planaria.

Thank you for pointing out this mistake. What we intended to convey was the increase in neuron number during homeostasis. We have revised the abstract “We found that the increase in neuron cell number tends to lag behind the rapid expansion of somatic cells during the later phase of homeostasis.”

(6) It is unclear what readers are to make of the measurements of brain lobe angles. Why is this a useful measurement and what does it tell us?

The measurement of brain lobe angles is intended to provide a quantitative assessment of the growth and morphological changes of the planarian brain during regeneration. Additionally, the relevance of brain lobe angles has been explored in previous studies, such as Arnold et al., Nature, 2016, further supporting its use as a meaningful parameter.

(7) The authors repeatedly say that this work lets them investigate planarians at the single-cell level, but they don't really make the case that they are seeing things that haven't already been described at the single-cell level using standard confocal microscopy.

Thank you for your comment. We agree that single-cell level imaging has been previously achieved in planarians using conventional confocal microscopy. However, our goal was to extend the application of expansion microscopy by combining C-MAP with tiling light sheet microscopy (TLSM), which allows for faster and high-resolution 3D imaging of whole-mount planarians. We have added in the discussion section: “This combination offers several key advantages over standard techniques. For example, it enables high-throughput imaging across entire organisms with a level of detail and speed that is not easily achieved using confocal methods. This approach allows us to investigate the planarian nervous system at multiple developmental and regenerative stages in a more comprehensive manner, capturing large-scale structures while preserving fine cellular details. The ability to rapidly image whole planarians in 3D with this resolution provides a more efficient workflow for studying complex biological processes.”

eLife Assessment

This study makes the fundamental discovery of the first natural animal rhodopsin that uses a chloride ion instead of an amino acid side chain as a counterion. Using a combination of biochemical and spectroscopic experiments together with QM/MM simulations, the authors identify the spectral tuning mechanism in the dark state and in the photoproduct state. The methods are sound and the results are convincing. This work will be of interest to biologists working on visual proteins and it also raises new questions about how environmental factors might affect coral opsins.

Reviewer #1 (Public review):

The chromophore molecule of animal and microbial rhodopsins is retinal which forms a Schiff base linkage with a lysine in the 7-th transmembrane helix. In most cases, the chromophore is positively charged by protonation of the Schiff base, which is stabilized by a negatively charged counterion. In animal opsins, three sites have been experimentally identified, Glu94 in helix 2, Glu113 in helix 3, and Glu181 in extracellular loop 2, where a glutamate acts as the counterion by deprotonation. In this paper, Sakai et al. investigated molecular properties of anthozoan-specific opsin II (ASO-II opsins), as they lack these glutamates. They found an alternative candidate, Glu292 in helix 7, from the sequences. Interestingly, the experimental data suggested that Glu292 is not the direct counterion in ASO-II opsins. Instead, they found that ASO-II opsins employ a chloride ion as the counterion. In the case of microbial rhodopsin, a chloride ion serves as the counterion of light-driven chloride pumps. This paper reports the first observation of a chloride ion as the counterion in animal rhodopsin. Theoretical calculation using a QM/MM method supports their experimental data. The authors also revealed the role of Glu292, which serves as the counterion in the photoproduct, and is involved in G protein activation.

The conclusions of this paper are well supported by data, while the following aspects should be considered for the improvement of the manuscript.

(1) Information on sequence alignment only appears in Figure S2, not in the main figures. Figure S2 is too complicated by so many opsins and residue positions. It will be difficult for general readers to follow the manuscript because of such an organization. I recommend the authors show key residues in Figure 1 by picking up from Figure S2.

(2) Halide size dependence. The authors observed spectral red-shift for larger halides. Their observation is fully coincident with the chromophore molecule in solution (Blatz et al. Biochemistry 1972), though the isomeric states are different (11-cis vs all-trans). This suggests that a halide ion is the hydrogen-bonding acceptor of the Schiff base N-H group in solution and ASO-II opsins. A halide ion is not the hydrogen-bonding acceptor in the structure of halorhodopsin, whose halide size dependence is not clearly correlated with absorption maxima (Scharf and Engelhard, Biochemistry 1994). These results support their model structure (Figure 4), and help QM/MM calculations.

(3) QM/MM calculations. According to Materials and Methods, the authors added water molecules to the structure and performed their calculations. However, Figure 4 does not include such water molecules, and no information was given in the manuscript. In addition, no information was given for the chloride binding site (contact residues) in Figure 4. More detailed information should be shown with additional figures in Figure SX.

(4) Figure 5 clearly shows much lower activity of E292A than that of WT, whose expression levels are unclear. How did the authors normalize (or not normalize) expression levels in this experiment?

(5) The authors propose the counterion switching from a chloride ion to E292 upon light activation. A schematic drawing on the chromophore, a chloride ion, and E292 (and possible surroundings) in Antho2a and the photoproduct will aid readers' understanding.

Reviewer #2 (Public review):

Summary:

This work reports the discovery of a new rhodopsin from reef-building corals that is characterized experimentally, spectroscopically, and by simulation. This rhodopsin lacks a carboxylate-based counterion, which is typical for this family of proteins. Instead, the authors find that a chloride ion stabilizes the protonated Schiff base and thus serves as a counterion.

Strengths:

This work focuses on the rhodopsin Antho2a, which absorbs in the visible spectrum with a maximum at 503 nm. Spectroscopic studies under different pH conditions, including the mutant E292A and different chloride concentrations, indicate that chloride acts as a counterion in the dark. In the photoproduct, however, the counterion is identified as E292.

These results lead to a computational model of Antho2a in which the chloride is modeled in addition to the Schiff base. This model is improved using the hybrid QM/MM simulations. As a validation, the absorption maximum is calculated using the QM/MM approach for the protonated and deprotonated E292 residue as well as the E292A mutant. The results are in good agreement with the experiment. However, there is a larger deviation for ADC(2) than for sTD-DFT. Nevertheless, the trend is robust since the wt and E292A mutant models have similar excitation energies. The calculations are performed at a high level of theory that includes a large QM region.

Weaknesses:

I have a couple of questions about this study:

(1) I find it suspicious that the absorption maximum is so close to that of rhodopsin when the counterion is very different. Is it possible that the chloride creates an environment for the deprotonated E292, which is the actual counterion?

(2) The computational protocol states that water molecules have been added to the predicted protein structure. Are there water molecules next to the Schiff base, E292, and Cl-? If so, where are they located in the QM region?

(3) If the E292 residue is the counterion in the photoproduct state, I would expect the retinal Schiff base to rotate toward this side chain upon isomerization. Can this be modeled based on the recent XFEL results on rhodopsin?

Reviewer #3 (Public review):

Summary:

The paper by Saito et al. studies the properties of anthozoan-specific opsins (ASO-II) from organisms found in reef-building coral. Their goal was to test if ASO-II opsins can absorb visible light, and if so, what the key factors involved are.

The most exciting aspect of this work is their discovery that ASO-II opsins do not have a counterion residue (Asp or Glu) located at any of the previously known sites found in other animal opsins.

This is very surprising. Opsins are only able to absorb visible (long wavelength light) if the retinal Schiff base is protonated, and the latter requires (as the name implies) a "counter ion". However, the authors clearly show that some ASO-II opsins do absorb visible light.

To address this conundrum, they tested if the counterion could be provided by exogenous chloride ions (Cl-). Their results find compelling evidence supporting this idea, and their studies of ASO-II mutant E292A suggest E292 also plays a role in G protein activation and is a counterion for a protonated Schiff base in the light-activated form.

Strengths:

Overall, the methods are well-described and carefully executed, and the results are very compelling.

Their analysis of seven ASO-II opsin sequences undoubtedly shows they all lack a Glu or Asp residue at "normal" (previously established) counter-ion sites in mammalian opsins (typically found at positions 94, 113, or 181). The experimental studies clearly demonstrate the necessity of Cl- for visible light absorbance, as do their studies of the effect of altering the pH.

Importantly, the authors also carried out careful QM/MM computational analysis (and corresponding calculation of the expected absorbance effects), thus providing compelling support for the Cl- acting directly as a counterion to the protonated retinal Schiff base, and thus limiting the possibility that the Cl- is simply altering the absorbance of ASO-II opsins through some indirect effect on the protein.

Altogether, the authors achieved their aims, and the results support their conclusions. The manuscript is carefully written, and refreshingly, the results and conclusions are not overstated.

This study is impactful for several reasons. There is increasing interest in optogenetic tools, especially those that leverage G protein-coupled receptor systems. Thus, the authors' demonstration that ASO-II opsins could be useful for such studies is of interest.

Moreover, the finding that visible light absorbance by an opsin does not absolutely require a negatively charged amino acid to be placed at one of the expected sites (94, 113, or 181) typically found in animal opsins is very intriguing and will help future protein engineering efforts. The argument that the Cl- counterion system they discover here might have been a preliminary step in the evolution of amino acid based counterions used in animal opsins is also interesting.

Finally, given the ongoing degradation of coral reefs worldwide, the focus on these curious opsins is very timely, as is the authors' proposal that the lower Schiff base pKa they discovered here for ASO-II opsins may cause them to change their spectral sensitivity and G protein activation due to changes in their environmental pH.

eLife Assessment

This paper reports the analysis of coevolutionary patterns and dynamical information for identifying functionally relevant sites. These findings are considered important due to the broad utility of the unified framework and network analysis capable of revealing communities of key residues that go beyond the residue-pair concept. The data are solid and the results are clearly presented.

Reviewer #1 (Public review):

Summary:

As reported above, this paper by Xu et al reports on a new method to combine the analysis of coevolutionary patterns with dynamic profiles to identify functionally important residues and reveal correlations between binding sites.

Strengths:

In general, coevolutionary analysis and MD analysis are carried out separately and while there have been attempts to compare the information provided by the two, no unified framework exists. Here, the authors convincingly demonstrate that integrating signals from Dynamics and coevolution gives information that substantially overcomes the one provided by either method in isolation. While other methods are useful, they do not capture how dynamics is fundamental to define function and thus sculpts coevolution, via the 3D structure of the protein. At the same time, the authors demonstrate how coevolution in turn also influences internal dynamics. The Networks they rebuild unveil information at an even higher level: the model starts pairwise but through network representation the authors arrive to community analysis, reporting on interaction patterns that are larger than simple couples.

Comments on latest version:

I have nothing to add to this revision. The paper looks excellent and very interesting.

Reviewer #2 (Public review):

Summary:

The authors introduced a computational framework, DyNoPy, that integrates residue coevolution analysis with molecular dynamics (MD) simulations to identify functionally important residues in proteins. DyNoPy identifies key residues and residue-residue coupling to generate an interaction graph and attempts to validate using two clinically relevant β-lactamases (SHV-1 and PDC-3).

Strengths:

DyNoPy could not only show clinically relevance of mutations but also predict new potential evolutionary mutations. Authors have provided biologically relevant insights into protein dynamics which can have potential applications in drug discovery and understanding molecular evolution.

Comments on latest version:

I appreciate the efforts of the authors to address my comments.

Reviewer #3 (Public review):

Summary:

In this paper, Xu, Dantu and coworkers report a protocol for analyzing coevolutionary and dynamical information to identify a subset of communities that capture functionally relevant sites in beta-lactamases.

Strengths:

The combination of coevolutionary information and metrics from MD simulations is interesting for capturing functionally relevant sites, which can have implications in the fields of drug discovery but also in protein design.

Comments on latest version:

The authors have successfully addressed all my previous comments/concerns. I am happy with the current version of the manuscript.

Author response:

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

Reviewer #1 (Public review):

Summary:

As reported above, this paper by Xu et al reports on a new method to combine the analysis of coevolutionary patterns with dynamic profiles to identify functionally important residues and reveal correlations between binding sites.

Strengths:

In general, coevolutionary analysis and MD analysis are carried out separately and while there have been attempts to compare the information provided by the two, no unified framework exists. Here, the authors convincingly demonstrate that integrating signals from Dynamics and coevolution gives information that substantially overcomes the one provided by either method in isolation. While other methods are useful, they do not capture how dynamics is fundamental to define function and thus sculpts coevolution, via the 3D structure of the protein. At the same time, the authors demonstrate how coevolution in turn also influences internal dynamics. The Networks they rebuild unveil information at an even higher level: the model starts pairwise but through network representation the authors arrive to community analysis, reporting on interaction patterns that are larger than simple couples.

Weaknesses:

The authors should

- Make an effort in suggesting/commenting the limits of applicability of their method;

We have added a sentence on Page 17, line 15 that describes the limitation of our method.

- Expand discussion on how DyNoPy compares to other methods;

A paragraph has been added to explain the comparison with other models (Page 3, line 18)

- Dynamic is not essential in all systems (structural proteins): The authors may want to comment on possible strategies they would use for other systems where their framework may not be suitable/applicable.

We agree with the reviewer that dynamics is not essential in all systems. In systems where there is limited role of dynamics in the function, the analysis done with DyNoPy is equivalent to conventional coevolution analysis, which can be consider one limitation of our method. Conversely, for dynamic proteins, combining functional dynamics descriptors with coevolution analysis using DyNoPy, helps in denoising information by deconvolution of communities. We have included this in the manuscript to highlight the suitability/applicability of the method.

Further, we have added a paragraph in the Introduction and conclusions highlighting the main difference between DyNoPy and existing computational tools like DCCM, KIN, and SPM and for your convenience it is provided below:

“Functional sites are often regulated by both, local and global interactions. Changes in these interactions are instrumental for functional events like substrate binding, catalysis, and conformational changes (18). The development of physical models of protein dynamics and the increase in available computational power has stimulated the adoption of computational techniques (19, 20) to investigate the conformational dynamics of proteins, an essential component of the many biological functions (21, 22). Different models have been proposed to describe the interactions between residues during simulations and network models have been particularly popular,  including methods on single structures and MD simulations data built by analysing the response to external forces on residue networks (23), by estimating the prevalence of non-covalent energy interaction networks in homologous proteins (24), or by analysing linear or non-linear correlation in atomic fluctuations (25, 26). These techniques have demonstrated their usefulness in extracting allosteric networks from structural data with applications in enzyme design (26).”

Reviewer #2 (Public review):

Summary:

Authors introduced a computational framework, DyNoPy, that integrates residue coevolution analysis with molecular dynamics (MD) simulations to identify functionally important residues in proteins. DyNoPy identifies key residues and residue-residue coupling to generate an interaction graph and attempts to validate using two clinically relevant β-lactamases (SHV-1 and PDC-3).

Strengths:

DyNoPy could not only show clinically relevance of mutations but also predict new potential evolutionary mutations. Authors have provided biologically relevant insights into protein dynamics which can have potential applications in drug discovery and understanding molecular evolution.

Weaknesses:

Although DyNoPy could show the relevance of key residues in active and non-active site residues, no experiments have been performed to validate their predictions.

We thank the reviewer for highlighting this point. We acknowledge that direct experimental validation of our predictions for DyNoPy has not yet been performed. However, we have provided explanations and evidence from experiments conducted on closely related homologs to support the relevance of key residues. These homologs share significant structural and functional similarity, which strengthens the reliability of our predictions.

In addition, they should compare their method with conventional techniques and show how their method could be different.

We thank all the reviewers for highlighting this oversight on our behalf. In Introduction and conclusion, we have added the following paragraphs:

“Functional sites are often regulated by both, local and global interactions. Changes in these interactions are instrumental for functional events like substrate binding, catalysis, and conformational changes (18). The development of physical models of protein dynamics and the increase in available computational power has stimulated the adoption of computational techniques (19, 20) to investigate the conformational dynamics of proteins, an essential component of the many biological functions (21, 22). Different models have been proposed to describe the interactions between residues during simulations and network models have been particularly popular,  including methods on single structures and MD simulations data built by analysing the response to external forces on residue networks (23), by estimating the prevalence of non-covalent energy interaction networks in homologous proteins (24), or by analysing linear or non-linear correlation in atomic fluctuations (25, 26). These techniques have demonstrated their usefulness in extracting allosteric networks from structural data with applications in enzyme design (26). ”

An explanation of "communities" divided in the work and how these communities are relevant to the article should be provided. In addition, choice of collective variables and their relevance in residue coupling movement is also not very well explained. Dynamics cross correlation map can also be a good method for understanding the residue movements and can explain the residue-residue coupling, it is not explained how DyNoPy is different from the conventional methods or can perform better.

The following sentences have been included in the manuscript to address the questions raised by the reviewer:

On Community Definition and relevance

DyNoPy identified coevolving residue pairs (scaled coevolution score >1) with interactions strongly correlated with protein functional motions (i.e., J values larger than zero). Applying network analysis on the combined dynamics-coevolution matrix helps us extracting higher-order interactions beyond pairwise coupling and detecting critical residues, which show multiple interactions with each other. Moreover, indirect long-range relationships, which would be hard to identify from numerical data, could be detected through community clustering. Community-based analysis offers a more comprehensive understanding of residue relationships and enables the visualization of residue couplings on the protein structure.

On Choice of collective variables:

DyNoPy works on the assumption that time-dependent interactions between critical residues, either having significant structural change or not will correlate with functional conformational motions. Since MD simulation data is high-dimensional, a time-dependent dynamic descriptor is required to extract the most relevant information for the process under study. A good collective variable (CV) should appropriately describe protein functional motions. Thus, a CV that detects the highest number of residue couplings is expected to be the most suitable descriptor (Mentioned in Page 22 Line 14). In our study, we tested 12 CVs, either focusing on the entire protein or on selected regions. And the best performed CV (the one identified the most residue couplings) was selected for further analysis. In practical applications, users can decide whether to focus on the most relevant global or local dynamics descriptor  depending on the dynamics of their specific system.

We have added a paragraph in the Introduction differentiating DyNoPy with other methods including DCCM. DCCM differs from DyNoPy in two aspects 1) it does not account for inter-residue coevolution 2) the correlation matrix captures correlations of atomic/residue movements associated with the whole intrinsic dynamics of the system, without filtering for the contributions to the important motions involved in the biological function. Additionally, any residue pair contributing to functional motion without itself undergoing any structural change will not be visible in this approach.

In the sentence "DyNoPy identified eight significant communities of strongly coupled residues within SHV-1 (Supporting Fig. S4A)" I could not find a clear description of eight significant communities.

The following sentences have been included in the results, methods and figure legends that define ‘significant community’:

‘DyNoPy identified eight meaningful communities, each consisting of at least three strongly coupled residues within SHV-1 (Supplementary Fig. S4A). All crucial catalytic residues and critical substitution sites previously mentioned participating in one of these communities with the exceptions of R₄₃, R₂₀₂, and S₁₃₀.’ (Page 8 Line 28)

‘A meaningful community should contain at least three residues.’ (Page 21 Line 2)

‘A reasonable residue community should contain at least three residues.’ (SI Page 11)

Again the description of communities is not clear to me in the following sentence "Detailed description of the other three communities is provided in the supporting information (Fig. S6)."

This following sentence has been rewritten.

‘Detailed description of communities with secondary importance for protein function (community 3, 8, and 9) is provided in the supplementary information (Supplementary Fig. S6).’ (Page 9, line 8)

In the sentence "N170 acts as an intermediary between N136 and E166". Kindly cite the reference figure to show N179 as intermediate residue.

This sentence has been rewritten to avoid any confusion.

‘Although DyNoPy did not detect this direct interaction between N136 and E166, the established relationship between N136 and N170 highlights the role of N136 in influencing E166.’ (Page 10 Line 8)

Please be careful with the numbers. In the sentence "These residues not only interact with each other directly but are also indirectly coupled via 21 other residues." I could count 22 other residues and not 21.

We thank the reviewer for spotting this error. This has now been corrected. All the communities are counted again.

‘These residues not only interact with each other directly but are also indirectly coupled via 22 other residues.’ (Page 12 Line 14)

In the sentence "Unlike other substitution sites that are adjacent to the active site, R₂₀₅ is situated more than 16 Å away from catalytic serine S₇₀". Please add this label somewhere in the figure.

The figure legends have been updated to include this. Distances have been added to community 4 Fig. 3 and community 6 Fig. 4. Residue index in the legend of Fig.3 has been included as subscript. Distance in the main text has been changed to be more accurate.

‘G₁₅₆ and A₁₄₆ are two functional important residues distant from the active site. G₁₅₆ is 21.3Å away from the catalytic S₇₀. A₁₄₆ is 16.8Å away from S₇₀.’ (Page 12 Line 2)

‘R₂₀₅ is a functional important residue that is 20.6Å away from the active site S₇₀.’ (Page 13 Line 10)

Please cite a reference in the sentence "This indicates that mutations on G238 would result in an alteration on protein catalytic function, as well as an increased flexibility of the protein, which strongly aligns with previous finding."

The citation has been added

‘This indicates that mutations on G238 would result in an alteration on protein catalytic function, as well as an increased flexibility of the protein, which strongly aligns with previous finding (62).’ (Page 15 Line 2)

Reviewer #3 (Public review):

Summary:

In this paper, Xu, Dantu and coworkers report a protocol for analyzing coevolutionary and dynamical information to identify a subset of communities that capture functionally relevant sites in beta-lactamases.

Strengths:

The combination of coevolutionary information and metrics from MD simulations is interesting for capturing functionally relevant sites, which can have implications in the fields of drug discovery but also in protein design.

Weaknesses:

The combination of coevolutionary information and metrics from MD simulations is not new as other protocols have been proposed along the years (the current version of the paper neglects some of them, see below), and there are a few parameters of the protocol that, in my opinion, should be better analyzed and discussed.

(1) As mentioned, the introduction of the paper lacks some important publications in the field of using graph theory to represent important interaction networks extracted from MD simulations (DOI: 10.1002/pro.4911), and also combining MD data with MSA to identify functionally relevant sites for enzyme design (doi: 10.1021/acscatal.4c04587, 10.1093/protein/gzae005).

We are very grateful for pointing us to these references. We have added a paragraph in the Introduction mentioning these and other computational tools similar to DyNoPy. Further, in conclusion we have highlighted the differences between DyNoPy and existing tools.

(2) The matrix used to apply graph theory (J_ij) is built from summing the scaled coevolution and degree of correlation values. The alpha and beta weights are defined, and the authors mention that alpha is set to 0.5, thus beta as well to fulfil with the alpha + beta = 1. Why a value of 0.5 has been selected? How this affects the overall results and conclusions extracted? The finding that many catalytically relevant residues are identified in the communities is not surprising given that such sites usually present a high conservation score.

This is an excellent question. Our present formulation allows the user to easily assess the influence of coevolution and dynamic couplings on the output. Setting alpha to 0.5, weights both evolutionary and dynamics information equally and has shown promising results in SHV-1 and PDC-3. As it has been presented in the manuscript, setting alpha to 1, i.e., purely utilising coevolution data does not let us identify critical residues effectively as all residues are included in the set (Supplementary Fig. S4 and S5). In future work, we would like to investigate the effect of scanning alpha from 0 to 1 on the final residue list, possibly on a larger set of proteins and protein families.

We would also like to point out that some of the residue pairs with coevolution scores in the top 1% have J-scores set to 0, as they lacked significant coupling to the functional dynamics.

(3) Another important point that needs further explanation is the selection of the relevant descriptor of protein dynamics. In this study two different strategies have been used (one more global the other more local), but more details should be provided regarding their choice. What is the best strategy according to the authors? Why not using the same strategy for both related systems? The obtained results using one methodology or the other will have a large impact on the dynamical score. Another related point is: what is the impact of the MD simulation length, how the MSA is generated and number of sequences used for MSA construction?

As in the case of many complex proteins, the flow of information occurs in β-lactamases via structural interactions (https://doi.org/10.7554/eLife.66567). These interactions occur both on a local level, as in the case of binding site residues or residues immediately surrounding the binding site; however, there are interactions far away (>20Å) from the binding site that have the ability to alter function. We have obtained this information from extensive surveys of clinical isolates and experimental data. To account for such interactions, a more global approach has to be taken. To answer the reviewer’s question: each system is unique and there is no one-fixed strategy. In short, the method used should be able to denoise information and the user is advised to fine-tune their findings by corroborating with experimental and clinical information.

The length of MD simulations is also system specific. Some systems effectively sample the functional dynamics within a shorter simulation time, while others take a long timescale MD simulation to converge. The results won’t change as long as the simulation has effectively sampled the functional dynamics associated with biological function.

The MSA is generated by the HH-Suite package as mentioned on Page 19 Line 19. More specifically, the MSA is constructed based on the UniRef30 database, where sequences are clustered, and each cluster contains sequences with at least 30% sequence identity. This provides a non-redundant set of protein sequences. Our package allows the automatic generation of MSAs from the database. For SHV-1, the alignment contains 18,175 protein sequences and for PDC-3, the alignment consists of 27,892 protein sequences. Full details of this protocol are published in Bibik et al. (https://doi.org/10.1093/bioinformatics/btae166). We have revised the methods section to include these details.

Other Minor Alterations

‘Fig. S1 and S2’ has been changed to ‘Supplementary Fig. S1 and S2’ for consistency (Page 6 Line 12)

(1) ‘Figure 5B’ has been changed to ‘Fig. 5B’ for consistency (Page 16 Line 11)

(2) All the ‘Figure’ has been changed to ‘Fig.’ in the SI for consistency

(3) Just as the suggestion, an alteration has been made on the Step 1 of Fig.1.

eLife Assessment

CellDetective is a useful software package for segmentation, tracking, and analysis of time‐lapse microscopy datasets, specifically designed to be accessible to researchers without coding expertise. The authors provide solid evidence of its capabilities through comprehensive validations and well‐executed comparisons across immunological assays. However, the current implementation is limited to 2D widefield imaging and presents technical challenges - including occasional crashes, restricted flexibility in defining multiple cell populations, and some interface issues that hinder the full user experience. Overall, this work will be of significant interest to the bioimaging community, especially those in immunology and cell biology, and promises to evolve into a more robust tool with further development.

Reviewer #1 (Public review):

Summary:

In this manuscript, Torro et al. presented CellDetective, an open-source software designed for a user-friendly execution of single-cell segmentation, tracking, and analysis of time-lapse microscopy data. The authors demonstrated the applications of the software by measuring NK cell spreading events acquired with reflection interference contrast microscopy (RICM), as well as detecting target cell death events and their interaction with neighboring NK cells in a multichannel widefield microscopy dataset.

Strengths:

The segmentation (StarDist, Cellpose) and tracking (bTrack) modules implemented were based on existing and published software packages. The authors added the event detection, classification, and analysis modules to enable an end-to-end time-lapse microscopy data processing and analysis pipeline, complete with a graphical user interface (GUI). This minimizes the coding experience required from the user. The documentation that accompanies CellDetective is also adequate.

Weaknesses:

Given that the software was designed to improve user experience, such an approach also limits its scope and functionality and is currently capable of handling very specific types of experiments. Additionally, this reviewer has also encountered many technical difficulties (see documented bugs/crashes below) that have prevented an extensive exploration of all the functionality of CellDetective.

Specifics:

(1) The software can only handle 2D 'widefield' time-lapse imaging datasets. It should be noted that many studies that examine cell-cell interactions in vitro also used confocal microscopy and acquired the time-lapse images in 3D z-stacks to enable the reconstruction of entire cell volumes from multiple optical sections along the z-axis.

Given that almost all of the implemented segmentation (StarDist, Cellpose) and tracking (bTrack) packages already support the handling of 3D datasets, it is unclear why CellDetective was designed to only work with 2D datasets.

As noted above, extending the support for 3D images would allow the scope and utility of this software to be further extended for imaging studies acquired in z-stacks. As an example, the dense clustering of effector cells in Figure 4 had prevented accurate segmentation due to the 2D nature of the experimental dataset. More importantly, support for a 3D dataset could also allow for the tracking of fluorescent protein-based sub-cellular as well as membrane protein localization during cell-cell interactions.

Furthermore, it also widens the potential applicability for analyzing datasets from 3D organoid imaging and perhaps even intravital two-photon microscopy.

(2) The software in its current form only allows the broad demarcation of the cells examined into two populations: targets and effectors. This limits the number of cell populations that can be examined for their interactions. It might be more useful to just allow multiple user-defined populations instead of restricting the populations to target and effector cells only.

(3) Similarly, subsetting of each of the populations could be made more intuitive. Although it is possible to define subsets of cells using the "Custom classification" function under the "Measure" module with user-defined parameters, visualization of multiple groups remains unintuitive and it appears that only one custom classified group can be selected and visualized at any given time in the Signal Annotator under Measurement instead of allowing visualization of multiple (custom defined) groups of cells in different colors. It is also unclear how, if possible at all, to visualize a custom group of cells in the Signal Annotator under the Detect Events module.

Software issues:

(4) When initially tested on v1.3.9, the Segment module could not be initiated (with the error message AttributeError: 'WindowsPath' object has no attribute 'endswith' when attempting to run segmentation).<br /> Update: this has been fixed in v1.3.9.post4 dated February 7th, 2025.

(5) Further testing was then performed by downgrading the software to v1.3.1. While testing the ADCC demo experiment (https://celldetective.readthedocs.io/en/latest/adcc-example.html), the workflow was stuck at attempts to initiate the Detect Events step:

AssertionError: No signal matches with the requirements of the model ['dead_nuclei_channel_mean', 'area']. Please pass the signals manually with the argument selected_signals or add measurements. Abort.

(Update: fixed in the latest v1.3.9.post4 version dated February 7th, 2025)

(6) Random bugs causing the software to crash. Example: switching characteristic to 'status_color' in the Signal Annotator under Measurement caused the software to crash (v1.3.9.post4):

TypeError: ufunc 'isnan' is not supported for the input types, and the inputs could not be safely coerced to any supported types according to the casting rule 'safe'

(7) Overall, when exploring the functionality of the software, there have been multiple instances of software crashes when clicking/switching around to show different parameters, etc.

This reviewer understands the difficulties and time involved in bug fixing and hopes that the experience could have been much smoother and that the software behaves much more stably in order to maximize its useability.

Reviewer #2 (Public review):

Summary:

Immune assays enable the analysis of immune responses in vitro. These assays generate time series image data across several experimental conditions. The imaging parameters such as the imaging modality and the number of channels can vary across experiments. A challenge in the field is the lack of (open source) tools to process and analyze these data. R. Torro, et. al. developed an open source end-to-end pipeline for the analysis of image data from these immune assays. The pipeline is designed with a GUI and is suited for experimental biologists with no coding experience. The authors have incorporated several existing methods and tools for individual tasks such as for segmentation and cell tracking, and incorporated them with custom methods where necessary such as for tracking cell state transitions.

Strengths:

(1) The tool is extremely well-documented and easy to install.

(2) Applicable to a wide variety of imaging modalities and analysis.

(3) There are several different options for each step, such as segmentation using traditional methods or deep learning methods, and all the analysis steps are integrated in one place with a GUI. The no-coding requirement makes this a very powerful tool for biologists and has the potential to enable a wide variety of analyses.

Weakness:

(1) It would be good to provide documentation on how to make the tool applicable for applications and analysis other than for immune profiling since most methods integrated here are applicable well beyond immune profiling. For example, a user might want to use the tool just for the segmentation of their IF microscopy-images.

(2) They applied Celldetective to two immune assays. The authors present the results from these assays and use the results to validate their assay. However, they have not included data that demonstrates results obtained via this pipeline are comparable to results obtained with other pipelines and/or if these results are consistent with what is expected in the literature.

Author response:

In view of the suggestions of the referees, we wish to underline that a user can interact with celldetective at two levels: a non-coder can analyse data and train models without coding, but is necessarily offered pre-determined choices and flexibility. An advanced user however has practically limitless flexibility to extend the fully-open source celldetective, aided by its modularity and detailed manual.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Torro et al. presented CellDetective, an open-source software designed for a user-friendly execution of single-cell segmentation, tracking, and analysis of time-lapse microscopy data. The authors demonstrated the applications of the software by measuring NK cell spreading events acquired with reflection interference contrast microscopy (RICM), as well as detecting target cell death events and their interaction with neighboring NK cells in a multichannel widefield microscopy dataset.

Strengths:

The segmentation (StarDist, Cellpose) and tracking (bTrack) modules implemented were based on existing and published software packages. The authors added the event detection, classification, and analysis modules to enable an end-to-end time-lapse microscopy data processing and analysis pipeline, complete with a graphical user interface (GUI). This minimizes the coding experience required from the user. The documentation that accompanies CellDetective is also adequate.

Weaknesses:

Given that the software was designed to improve user experience, such an approach also limits its scope and functionality and is currently capable of handling very specific types of experiments. Additionally, this reviewer has also encountered many technical difficulties (see documented bugs/crashes below) that have prevented an extensive exploration of all the functionality of CellDetective.

We apologize for the technical difficulties and bugs; the ones mentioned have been already corrected. New users have also tested the installation and reported it to be bug-free.

We fully agree on the compromise that has to be found between user experience and versatility. We have already tested celldetective in other biological contexts, such as microbiology, but made a choice to showcase it in the article for immunological applications. We invite the reader to consult the software documentation and online examples to learn about more options.

Specifics:

(1) The software can only handle 2D 'widefield' time-lapse imaging datasets. It should be noted that many studies that examine cell-cell interactions in vitro also used confocal microscopy and acquired the time-lapse images in 3D z-stacks to enable the reconstruction of entire cell volumes from multiple optical sections along the z-axis.

Given that almost all of the implemented segmentation (StarDist, Cellpose) and tracking (bTrack) packages already support the handling of 3D datasets, it is unclear why CellDetective was designed to only work with 2D datasets.

As noted above, extending the support for 3D images would allow the scope and utility of this software to be further extended for imaging studies acquired in z-stacks. As an example, the dense clustering of effector cells in Figure 4 had prevented accurate segmentation due to the 2D nature of the experimental dataset. More importantly, support for a 3D dataset could also allow for the tracking of fluorescent protein-based sub-cellular as well as membrane protein localization during cell-cell interactions.

Furthermore, it also widens the potential applicability for analyzing datasets from 3D organoid imaging and perhaps even intravital two-photon microscopy.

We thank the reviewer for this suggestion. Indeed, extension to 3-dimensions is a natural development, since we have chosen segmentation and tracking methods which are compatible with 3D. However, two important strengths of celldetective are: harnessing statistical power of cell populations together with multiplexing biological conditions, and dynamic analysis of fast events.

For both, 2D is advantageous. Our own focus is on analyzing cellular events with minute time resolution, relevant in immunology. By our estimate (experience and literature), 3D timelapse acquisition would reduce the time resolution, as well as throughput (in terms of events and conditions) to below acceptable level. While we don’t envisage this upgrade in the immediate future, we encourage advanced users to contribute to further develop the open-source code in this direction. As a mitigation solution, a 2.5D approach on a flat sample by combining two z planes (in order to address issues of cell superposition for example), could be readily implemented with minimal change.

(2) The software in its current form only allows the broad demarcation of the cells examined into two populations: targets and effectors. This limits the number of cell populations that can be examined for their interactions. It might be more useful to just allow multiple user-defined populations instead of restricting the populations to target and effector cells only.

We thank the reviewer for this suggestion. There is little architectural limitation to its implementation; this will be proposed in the future version. This updated version will allow more than two user-defined populations, labelled directly by the user, which will also facilitate the natural extension to more varied biological applications. Three-way interactions are much more complex, and, to our knowledge, not currently addressed by biologists. The interactions will for the moment be limited to 2 populations interactions, as multipartite ones involve a higher level of code modifications, not immediately envisaged.

(3) Similarly, subsetting of each of the populations could be made more intuitive. Although it is possible to define subsets of cells using the "Custom classification" function under the "Measure" module with user-defined parameters, visualization of multiple groups remains unintuitive and it appears that only one custom classified group can be selected and visualized at any given time in the Signal Annotator under Measurement instead of allowing visualization of multiple (custom defined) groups of cells in different colors. It is also unclear how, if possible at all, to visualize a custom group of cells in the Signal Annotator under the Detect Events module.

The simultaneous visualization of several classes poses problems in the choice of colors and symbols, and may render the tool difficult to use. The time propagation option in the classification tool allows to define event classes as opposed to groups, that are compatible with the Signal Annotator. For more complex classifications, a simple solution is to work with composite classifications, which are already supported by using logical AND/OR operators on the condition defining the class. We believe that this feature is sufficient to address this issue.

Software issues:

(4) When initially tested on v1.3.9, the Segment module could not be initiated (with the error message AttributeError: 'WindowsPath' object has no attribute 'endswith' when attempting to run segmentation).

Update: this has been fixed in v1.3.9.post4 dated February 7th, 2025.

(5) Further testing was then performed by downgrading the software to v1.3.1. While testing the ADCC demo experiment (https://celldetective.readthedocs.io/en/latest/adcc-example.html), the workflow was stuck at attempts to initiate the Detect Events step:

AssertionError: No signal matches with the requirements of the model ['dead_nuclei_channel_mean', 'area']. Please pass the signals manually with the argument selected_signals or add measurements. Abort.

(Update: fixed in the latest v1.3.9.post4 version dated February 7th, 2025)

(6) Random bugs causing the software to crash. Example: switching characteristic to 'status_color' in the Signal Annotator under Measurement caused the software to crash (v1.3.9.post4):

TypeError: ufunc 'isnan' is not supported for the input types, and the inputs could not be safely coerced to any supported types according to the casting rule 'safe'

(7) Overall, when exploring the functionality of the software, there have been multiple instances of software crashes when clicking/switching around to show different parameters, etc.

This reviewer understands the difficulties and time involved in bug fixing and hopes that the experience could have been much smoother and that the software behaves much more stably in order to maximize its useability.

We apologize again for the various technical issues encountered during the review process, and thank the reviewer for mentioning that several bugs were already fixed in the last software release. The open source and software maintenance protocol enabled by github should help to resolve any further emerging issue.

Reviewer #2 (Public review):

Summary:

Immune assays enable the analysis of immune responses in vitro. These assays generate time series image data across several experimental conditions. The imaging parameters such as the imaging modality and the number of channels can vary across experiments. A challenge in the field is the lack of (open source) tools to process and analyze these data. R. Torro, et. al. developed an open source end-to-end pipeline for the analysis of image data from these immune assays. The pipeline is designed with a GUI and is suited for experimental biologists with no coding experience. The authors have incorporated several existing methods and tools for individual tasks such as for segmentation and cell tracking, and incorporated them with custom methods where necessary such as for tracking cell state transitions.

Strengths:

(1) The tool is extremely well-documented and easy to install.

(2) Applicable to a wide variety of imaging modalities and analysis.

(3) There are several different options for each step, such as segmentation using traditional methods or deep learning methods, and all the analysis steps are integrated in one place with a GUI. The no-coding requirement makes this a very powerful tool for biologists and has the potential to enable a wide variety of analyses.

Weakness:

(1) It would be good to provide documentation on how to make the tool applicable for applications and analysis other than for immune profiling since most methods integrated here are applicable well beyond immune profiling. For example, a user might want to use the tool just for the segmentation of their IF microscopy-images.

This is an important suggestion that we will implement as short demonstrations using data from the public domain. These will be proposed as examples in the online documentation.

(2) They applied Celldetective to two immune assays. The authors present the results from these assays and use the results to validate their assay. However, they have not included data that demonstrates results obtained via this pipeline are comparable to results obtained with other pipelines and/or if these results are consistent with what is expected in the literature.

In the final version of the article, we shall compare celldetective with existing literature, including our previous work, when possible. However, we emphasize that most of the presented data are original and don’t have any published equivalent in the literature. Concerning the immunotherapy assays, data presented already show expected trends (see for example Fig. 2 and Fig. 5). We reserve for future publications the systematic comparison with traditional (non microscopy-based) methods, as we consider it out-of-scope here. Additionally, there is, to our knowledge no existing open pipeline performing the full end-to-end analysis.

eLife Assessment

This manuscript describes the characterization of the conformational dynamics of two chemokine receptors at the single-molecule level using FRET. The authors make a convincing case for attributing the distinct interaction and pharmacology of the two receptors to differences in their conformational energy landscape. These important findings will be of interest to scientists working on activation mechanisms of GPCRs and signal transduction.

Joint Public Review:

Summary

This manuscript uses single-molecule fluorescence resonance energy transfer (smFRET) to identify differences in the molecular mechanisms of CXCR4 and ACKR3, two 7-transmembrane receptors that both respond to the chemokine CXCL12 but otherwise have very different signaling profiles. CXCR4 is highly selective for CXCL12 and activates heterotrimeric G proteins. In contrast, ACKR3 is quite promiscuous and does not couple to G proteins, but like most G protein-coupled receptors (GPCRs), it is phosphorylated by GPCR kinases and recruits arrestins. By monitoring FRET between two positions on the intracellular face of the receptor (which highlight the movement of transmembrane helix 6 [TM6], a key hallmark of GPCR activation), the authors show that CXCR4 remains mostly in an inactive-like state until CXCL12 binds and stabilizes a single active-like state. ACKR3 rapidly exchanges among four different conformations even in the absence of ligand, and agonists stabilize multiple activated states.

Strengths

The core method employed in this paper, smFRET, can reveal dynamic aspects of these receptors (the breadth of conformations explored and the rate of exchange among them) that are not evident from static structures or many other biophysical methods. smFRET has not been broadly employed in studies of GPCRs. Therefore, this manuscript makes important conceptual advances in our understanding of how related GPCRs can vary in their conformational dynamics.

Weaknesses

The probes used cannot reveal conformational changes in other positions besides transmembrane helix 6 (TM6). GPCRs are known to exhibit loose allosteric coupling, so the conformational distribution observed at TM6 may not fully reflect the global conformational distribution of receptors. This could mask important differences that determine the ability of intracellular transducers to couple to specific receptor conformations.

While it is clear that CXCR4 and ACKR3 have very different conformational dynamics, the data do not definitely show that this is the main or only mechanism that contributes to their functional differences.

The extent to which conformational heterogeneity is a characteristic feature of ACKRs that contributes to their promiscuity and arrestin bias is unclear. The key residue the authors find promotes ACKR3 conformational heterogeneity is not conserved in most other ACKRs, but alternative mechanisms could generate similar heterogeneity.

An inherent limitation of the approach is that mutagenesis, purification, and labeling of the receptors could affect their conformational distributions. The cysteine mutations in ACKR3 required to site-specifically install fluorophores substantially increase its ligand-induced activity (Fig. S1D). There are no data to confirm that the two receptors retain the same functional profiles observed in cell-based systems following in vitro manipulations (purification, labeling, nanodisc reconstitution).

Author response:

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

Reviewer #1 (Public Review):

Summary:

This paper uses single-molecule FRET to investigate the molecular basis for the distinct activation mechanisms between 2 GPCR responding to the chemokine CXCL12 : CXCR4, that couples to G-proteins, and ACKR3, which is G-protein independent and displays a higher basal activity.

Strengths:

It nicely combines the state-of-the-art techniques used in the studies of the structural dynamics of GPCR. The receptors are produced from eukaryotic cells, mutated, and labeled with single molecule compatible fluorescent dyes. They are reconstituted in nanodiscs, which maintain an environment as close as possible to the cell membrane, and immobilized through the nanodisc MSP protein, to avoid perturbing the receptor's structural dynamics by the use of an antibody for example.

The smFRET data are analysed using the HHMI technique, and the number of states to be taken into account is evaluated using a Bayesian Information Criterion, which constitutes the state-of-the-art for this task.

The data show convincingly that the activation of the CXCR4 and ACKR3 by an agonist leads to a shift from an ensemble of high FRET states to an ensemble of lower FRET states, consistent with an increase in distance between the TM4 and TM6. The two receptors also appear to explore a different conformational space. A wider distribution of states is observed for ACKR3 as compared to CXCR4, and it shifts in the presence of agonists toward the active states, which correlates well with ACKR3's tendency to be constitutively active. This interpretation is confirmed by the use of the mutation of Y254 to leucine (the corresponding residue in CXCR4), which leads to a conformational distribution that resembles the one observed with CXCR4. It is correlated with a decrease in constitutive activity of ACKR3.

Weaknesses:

Although the data overall support the claims of the authors, there are however some details in the data analysis and interpretation that should be modified, clarified, or discussed in my opinion

Concerning the amplitude of the changes in FRET efficiency: the authors do not provide any structural information on the amplitude of the FRET changes that are expected. To me, it looks like a FRET change from ~0.9 to ~0.1 is very important, for a distance change that is expected to be only a few angstroms concerning the movement of the TM6. Can the authors give an explanation for that? How does this FRET change relate to those observed with other GPCRs modified at the same or equivalent positions on TM4 and TM6?

The large FRET change in our system was initially unexpected. However, the reviewer is mistaken that the expected distance change is only a few angstroms. Crystal structures of the homologous beta2 adrenergic receptor (β₂AR) in inactive and active conformations reveal that the cytoplasmic end of TM6 moves outwards by 16 angstroms during activation (Rasmussen et al., 2011, ref 47).  Consistent with this, smFRET studies of β₂AR labeled in TM4 and TM6 (as here) showed that the donor-acceptor (D-A) distance was 14 angstroms longer in the active conformation (Gregorio et al., ref 38).  Surprisingly, the apparent distance change in our system (calculated for our FRET probes, A555/Cy5, using FPbase.com) is almost 30 angstroms. A possible explanation is that the fluorophore attached to TM6 interacts with lipids within the nanodisc when TM6 moves outwards, which could stretch the fluorophore linker and thereby increase the D-A distance (lipids were absent in the β₂AR study). Such an interaction could also constrain the fluorophore in an unfavorable orientation for energy transfer, also leading to lower than expected FRET efficiencies and inflated distance calculations. Regardless, it is important to emphasize that none of the interpretations or conclusions of our study are based on computed D-A distances. Rather, we resolved different receptor conformations and quantified their relative populations based on the measured FRET efficiency distributions.

Finally, we note that a recent smFRET study of the glucagon receptor (labeled in TM4 and TM6, as here) also revealed a large difference in apparent FRET efficiencies between inactive (E_app = 0.83) and active (E_app = 0.32) conformations (Kumar et al., ref. 39). Thus, the large change in FRET efficiency observed in our study is not unprecedented.

Concerning the intermediate states: the authors observe several intermediate states.

(1) First I am surprised, looking at the time traces, by the dwell times of the transitions between the states, which often last several seconds. Is such a long transition time compatible with what is known about the kinetic activation of these receptors?

We too were surprised by the apparent kinetics of the receptors in our system. However, it was previously noted that purified systems, including nanodiscs, lead to slower activation times for GPCRs compared to cellular membrane systems (Lohse et al, Curr. Opin. Cell Biology, 27, 8792, 2014). Indeed, slow transitions among different FRET states (dwell times in the seconds range) were also observed in recent smFRET studies of the mu opioid receptor (Zhao et al., 2024, ref. 41) and the glucagon receptor (Kumar et al., 2023, ref. 39). These studies are consistent with the observed time scale of the FRET transitions reported here.

(2) Second is it possible that these “intermediate” states correspond to differences in FRET efficiencies, that arise from different photophysical states of the dyes? Alexa555 and Cy5 are Cyanines, that are known to be very sensitive to their local environment. This could lead to different quantum yields and therefore different FRET efficiencies for a similar distance. In addition, the authors use statistical labeling of two cysteines, and have therefore in their experiment a mixture of receptors where the donor and acceptor are switched, and can therefore experience different environments. The authors do not speculate structurally on what these intermediate states could be, which is appreciated, but I think they should nevertheless discuss the potential issue of fluorophore photophysics effects.

The reviewer is correct that the intermediate FRET states could, in principle, arise from a conformational change of the receptor that alters the local environment of the donor and/or acceptor fluorophores, rather than a change in donor-acceptor distance. This caveat is now included in the discussion on Pg. 10:

“In principle, the intermediates in CXCR4 and ACKR3 could represent partial movements of TM6 from the inactive to active conformation or more subtle conformational changes altering the photophysical characteristics of the probes without drastically altering the donor-acceptor distance. Either possibility leads to detectable changes in apparent FRET efficiency and reflect discrete conformational steps on the activation pathway; however, it is not possible to resolve specific structural changes from the data.”

Regarding the second possibility, it is true that our labeling methodology leads to a statistical mixture of labeled species (D on TM6 and A on TM4, D on TM4 and A on TM6). If the photophysical properties of the fluorophores were markedly different for the two labeling orientations, this would produce two different FRET efficiencies for a given receptor conformation. Assuming two receptor conformations, this scenario would produce four distinct FRET states: E₁ (inactive receptor, labeling configuration 1), E₂ (active receptor, labeling configuration 1), E₃ (inactive receptor, labeling configuration 2) and E₄ (active receptor, labeling configuration 2), with two cross peaks in the TDP plots, corresponding to E₁ ↔ E₂ and E₃ ↔ E₄ transitions. Notably, E₂ ↔ E₃ cross peaks would not be present, since states E₂ and E₃ exist on separate molecules. Instead, we see all states inter-connected sequentially, R ↔ R’ ↔ R* in CXCR4 and R ↔ R’ ↔ R*’ ↔ R* in ACKR3 (Fig. 2), suggesting that the resolved FRET states represent interconnected conformational states.

We added the following text to the Results section on Pg. 6:

“Two-dimensional transition density probability (TDP) plots revealed that the three FRET states were connected in a sequential fashion (Figs. 2A & B), indicating that the transitions occurred within the same molecules. Notably, these observations exclude the possibility that the midFRET state arises from different local fluorophore environments (hence FRET efficiencies) for the two possible labeling orientations of the introduced cysteines: assuming two receptor conformations, this model would produce four distinct FRET states, but only two cross peaks in the TDP plot.”

(3) It would also have been nice to discuss whether these types of intermediate states have been observed in other studies by smFRET on GPCR labeled at similar positions.

Intermediate states have also been reported in previous smFRET studies of other GPCRs. For example, in the glucagon receptor (also labeled in TM4 and TM6), a third FRET state (E_app =  0.63) was resolved between the inactive (E_app  = 0.85) and active (E_app  = 0.32) states (Kumar et al., Ref. 39).  Discrete intermediate receptor conformations were also observed in the A_2AR labeled in TM4 and TM6 (Fernandes et al., Ref 40). These examples are now cited in the Discussion.

On line 239: the authors talk about the R↔R' transitions that are more probable. In fact it is more striking that the R'↔R* transition appears in the plot. This transition is a signature of the behavior observed in the presence of an agonist, although IT1t is supposed to be an inverse agonist. This observation is consistent with the unexpected (for an inverse agonist) shift in the FRET histogram distribution. In fact, it appears that all CXCR4 antagonists or inverse agonists have a similar (although smaller) effect than the agonist. Is this related to the fact that these (antagonist or inverse agonist) ligands lead to a conformation that is similar to the agonists, but cannot interact with the G-protein ?? Maybe a very interesting experiment would be here to repeat these measurements in the presence of purified G-protein. G-protein has been shown to lead to a shift of the conformational space explored by GPCR toward the active state (using smFRET on class A and class C GPCR). It would be interesting to explore its role on CXCR4 in the presence of these various ligands. Although I am aware that this experiment might go beyond the scope of this study, I think this point should be discussed nevertheless.

We thank the reviewer for this observation and the possible explanation offered.  In response, we have added the following text to the Results section on Pg. 7:

“The small-molecule ligand IT1t is reported to act as an inverse agonist of CXCR4 (54-56). However, the conformational distribution of CXCR4 showed little change to the overall apparent

FRET profile, although R’ ↔ R* transitions appeared in the TDP plot (Figs. 3A & B, Fig. S8). This suggests that the small molecule does not suppress CXCR4 basal signaling by changing the conformational equilibrium. Instead IT1t appears to increase transition probabilities which may impair G protein coupling by CXCR4.”

We have also added the following text to the Results on Pg. 8:

“Despite the ability of CXCL12_P2G and CXCL12_LRHQ to stabilize the active R* conformation of CXCR4, both variants are known to act as antagonists (20). This suggests that the CXCL12 mutants inhibit CXCR4 coupling to G proteins not by suppressing the active receptor population but rather by increasing the dynamics of the receptor state transitions. Our results suggest that the helical movements considered classic signatures of the active state may not be sufficient for CXCR4 to engage productively with G proteins.”

In addition, we have added the following text to the Discussion on Pg. 11:

“The chemokine variants CXCL12_P2G and CXCL12_LRHQ are reported to act as antagonists of CXCR4 (19, 20), and the small molecule IT1t acts as an inverse agonist (54-56). Surprisingly, none of these ligands inhibit formation of the active R* conformation of CXCR4. In fact, the chemokine variants both stabilize and increase this state to some degree, although less effectively than CXCL12_WT. Thus, the antagonism and inverse agonism of these ligands does not appear to be linked exclusively to receptor conformation, suggesting that the ligands inhibit coupling of G proteins to CXCR4 or disrupt the ligand-receptor-G protein interaction network required for signaling (Fig. S10) (21, 23).  Interestingly, these ligands also increase the probabilities of state-to-state transitions (Figs. 3B & 4B), suggesting that enhanced conformational exchange prevents the receptor from productively engaging G proteins. Similarly, ACKR3 is naturally dynamic and lacks G protein coupling, suggesting a common mechanism of G protein antagonism.”

Finally, we also agree that experiments with G proteins could be informative. In fact, we initiated such experiments during the course of this study.  However, it soon became apparent that significant optimization would be required to identify fluorophore labeling positions that report receptor conformation without inhibiting G protein coupling. Accordingly, we decided that G protein experiments would be the subject of future studies.

However, we added the following text to the Discussion on Pg. 12:

“Future smFRET studies performed in the presence of G proteins should be informative in this regard”.

The authors also mentioned in Figure 6 that the energetic landscape of the receptors is relatively flat ... I do not really agree with this statement. For me, a flat conformational landscape would be one where the receptors are able to switch very rapidly between the states (typically in the submillisecond timescale, which is the timescale of protein domain dynamics). Here, the authors observed that the transition between states is in the second timescale, which for me implies that the transition barrier between the states is relatively high to preclude the fast transitions.

We thank the reviewer for the comment. We have modified the description of the energy landscapes of ACKR3 and CXCR4 in the discussion on Pg. 10 as follows:

“These observations imply that ACKR3 has a relatively flat energy landscape, with similar energy minima for the different conformations, whereas the energy landscape of CXCR4 is more rugged (Fig. 6). For both receptors, the energy barriers between states are sufficiently high that transitions occur relatively slowly with seconds long dwell times (Figs. 1C and S2).”

Reviewer #2 (Public Review):

Summary:

his manuscript uses single-molecule fluorescence resonance energy transfer (smFRET) to identify differences in the molecular mechanisms of CXCR4 and ACKR3, two 7transmembrane receptors that both respond to the chemokine CXCL12 but otherwise have very different signaling profiles. CXCR4 is highly selective for CXCL12 and activates heterotrimeric G proteins. In contrast, ACKR3 is quite promiscuous and does not couple to G proteins, but like most G protein-coupled receptors (GPCRs), it is phosphorylated by GPCR kinases and recruits arrestins. By monitoring FRET between two positions on the intracellular face of the receptor (which highlights the movement of transmembrane helix 6 [TM6], a key hallmark of GPCR activation), the authors show that CXCR4 remains mostly in an inactive-like state until CXCL12 binds and stabilizes a single active-like state. ACKR3 rapidly exchanges among four different conformations even in the absence of ligands, and agonists stabilize multiple activated states.

Strengths:

The core method employed in this paper, smFRET, can reveal dynamic aspects of these receptors (the breadth of conformations explored and the rate of exchange among them) that are not evident from static structures or many other biophysical methods. smFRET has not been broadly employed in studies of GPCRs. Therefore, this manuscript makes important conceptual advances in our understanding of how related GPCRs can vary in their conformational dynamics.

Weaknesses:

(1) The cysteine mutations in ACKR3 required to site-specifically install fluorophores substantially increase its basal and ligand-induced activity. If, as the authors posit, basal activity correlates with conformational heterogeneity, the smFRET data could greatly overestimate the conformational heterogeneity of ACKR3.

The change in basal ACKR3 activity with the Cys introductions are modest in comparison and insignificantly different as determined by extra-sum-of-squares F test (P=0.14).

(2) The probes used cannot reveal conformational changes in other positions besides TM6. GPCRs are known to exhibit loose allosteric coupling, so the conformational distribution observed at TM6 may not fully reflect the global conformational distribution of receptors. This could mask important differences that determine the ability of intracellular transducers to couple to specific receptor conformations.

We agree that the overall conformational landscape of the receptors has not been investigated and we have added this caveat to the discussion on Pg. 12.

“An important caveat is that our study does not report on the dynamics of the other TM helices and H8, some of which are known to participate in arrestin interactions.”

(3) While it is clear that CXCR4 and ACKR3 have very different conformational dynamics, the data do not definitively show that this is the main or only mechanism that contributes to their functional differences. There is little discussion of alternative potential mechanisms.

The main functional difference between CXCR4 and ACRK3 is their effector coupling: CXCR4 couples to G proteins, whereas ACKR3 only couples to arrestins (following phosphorylation of the C-terminal tail by GRKs). As currently noted in the discussion, ACKR3 has many features that may contribute to its lack of G protein coupling, including lack of a well-ordered intracellular pocket due to conformational dynamics, lack of an N-term-ECL3 disulfide, different chemokine binding mode, and the presence of Y257. Steric interference due to different ICL loop structures may also interfere with G protein activation. No one thing has proven to confer ACKR3 with G protein activity including swapping all of the ICLs to those of canonical chemokine receptor, suggesting it is a combination of these different factors. The following has been added to the discussion on Pg. 13 to clearly note that any one feature is unlikely to drive the atypical behavior of ACKR3:

“The atypical activation of ACKR3 does not appear to be dependent on any singular receptor feature and is likely a combination of several factors.”

(4) The extent to which conformational heterogeneity is a characteristic feature of ACKRs that contributes to their promiscuity and arrestin bias is unclear. The key residue the authors find promotes ACKR3 conformational heterogeneity is not conserved in most other ACKRs, but alternative mechanisms could generate similar heterogeneity.

Despite the commonalities in the roles of the ACKRs, they all appear to have evolved independently. Thus, we do not believe that all features observed and described for one ACKR will explain the behavior of another. We have carefully avoided expanding our observations to other ACKRs to avoid suggesting common mechanisms.

(5) There are no data to confirm that the two receptors retain the same functional profiles observed in cell-based systems following in vitro manipulations (purification, labeling, nanodisc reconstitution).

We agree this is an important point. All labeled receptors responded to agonist stimulation as expected. As only properly folded receptors are able to make the extensive interactions with ligands necessary for conformational changes (for instance, CXCL12 interacts with all TMs and ECLs), this suggests that the proteins are folded correctly and functional following all manipulations.

Reviewer #3 (Public Review):

Summary:

This is a well-designed and rigorous comparative study of the conformational dynamics of two chemokine receptors, the canonical CXCR4 and the atypical ACKR3, using single-molecule fluorescence spectroscopy. These receptors play a role in cell migration and may be relevant for developing drugs targeting tumor growth in cancers. The authors use single-molecule FRET to obtain distributions of a specific intermolecular distance that changes upon activation of the receptor and track differences between the two receptors in the apo state, and in response to ligands and mutations. The picture emerging is that more dynamic conformations promote more basal activity and more promiscuous coupling of the receptor to effectors.

Strengths:

The study is well designed to test the main hypothesis, the sample preparation and the experiments conducted are sound and the data analysis is rigorous. The technique, smFRET, allows for the detection of several substates, even those that are rarely sampled, and it can provide a "connectivity map" by looking at the transition probabilities between states. The receptors are reconstituted in nanodiscs to create a native-like environment. The examples of raw donor/acceptor intensity traces and FRET traces look convincing and the data analysis is reliable to extract the sub-states of the ensemble. The role of specific residues in creating a more flat conformational landscape in ACKR3 (e.g., Y257 and the C34-C287 bridge) is well documented in the paper.

Weaknesses:

The kinetics side of the analysis is mentioned, but not described and discussed. I am not sure why since the data contains that information. For instance, it is not clear if greater conformational flexibility is accompanied by faster transitions between states or not.

The reviewer is correct that kinetic information is available, in principle, from smFRET experiments. However, a detailed kinetic analysis will require a much larger data set than we currently possess, to adequately sample all possible transitions and the dwell times of each FRET state. We intend to perform such an analysis in the future as more data becomes available. The purpose of this initial study was to explore the conformational landscapes of CXCR4 and ACKR3 and to reveal differences between them. To this end, we have documented major differences in conformational preferences and response to ligands of the two receptors that are likely relevant to their different biological behavior. Future kinetic information will add further detail, but is not expected to alter the conclusions drawn here.

The method to choose the number of states seems reasonable, but the "similarity" of states argument (Figures S4 and S6) is not that clear.

We thank the reviewer for noting a need for further clarification. We qualitatively compared the positions of the various FRET peaks across treatments to gain insight into the consistency of the conformations and avoid splitting real states by overfitting the data. For instance, fitting the ACKR3 treatments with three states leads to three distinct FRET populations for the R’ intermediate. Adding a fourth state results in two intermediates that are fairly well overlapping. In contrast, the two-intermediate model for CXCR4 appears to split the R* state of the CXCL12 treated sample and causes a general shift in both intermediate states to lower FRET values when CXCL12 is present. As we assume that the conformations are consistent throughout the treatments, we conclude that this represents an overfitting artifact and not a novel CXCL12CXCR4 R*’ state. Additional sentences have been added to the supplemental figure legend to better describe the comparative analysis.

“(Top) With the 3-state model, the R’ states for apo-CXCR4 and for CXCL12- and IT1t-bound receptor overlapped well with similar apparent FRET values across all of the tested conditions. In the case of the four-state model, the R*’ (Middle) and R’ (Bottom) states were substantially different across the ligand treatments. In particular, the R*’ state with CXCL12 treatment appears to arise from a splitting of the R* conformation, indicating that the model was overfitting the data.”

Also, the "dynamics" explanation offered for ACKR3's failure to couple and activate G proteins is not very convincing. In other studies, it was shown that activation of GPCRs by agonists leads to an increase in local dynamics around the TM6 labelling site, but that did not prevent G protein coupling and activation.

We agree with the reviewer that any single explanation for ACKR3 bias, including the dynamics argument presented here, is insufficient to fully characterize the ACKR3 responses. As noted by the reviewer, the TM6 movement and dynamics is generally correlated with G protein coupling, whereas other dynamics studies (Wingler et al. Cell 2019) have noted that arrestinbiased ligands do not lead to the same degree of TM6 movement. We have added the following statement to the discussion on Pg. 13:

“The atypical activation of ACKR3 does not appear to be dependent on any singular receptor feature and is likely a combination of several factors.” 

Recommendations for the authors:  

Reviewer #1 (Recommendations For The Authors):

I would like to raise a technical point about the calculation and reporting of the FRET efficiency. The authors report the FRET efficiency as E=IA/(IA+ID). There is now a strong recommendation from the FRET community (https://doi.org/10.1038/s41592-018-0085-0) to use the term “FRET efficiency” only when a proper correction procedure of all correction factors has been applied, which is not the case here (gamma factor has not been calculated). The authors should therefore use the term “Apparent FRET Efficiency” and  E_app in all the manuscripts.

Also, it would be nice to indicate directly on the figures whether a ligand that is used is an agonist, antagonist, inverse agonist, etc...

We thank the reviewer for suggesting this clarification in terminology. We now refer to apparent FRET efficiency (or E_app) throughout the manuscript and in the figures. In addition, we have added ligand descriptions to the relevant figures.

Reviewer #2 (Recommendations For The Authors):

(1) M159(4.40)C/Q245(6.28)C ACKR3 appears to have higher constitutive activity than ACKR3 Wt (Fig. S1). While the vehicle point itself is likely not significant due to the error in the Wt, the overall trend is clear and arguably even stronger than the effect of Y257(6.40)L (Fig. S9). While this is an inherent limitation of the method used, it should be clearly acknowledged; the comment in lines 162-164 seems to skirt the issue by only saying that arrestin recruitment is retained. It would be helpful and more rigorous to report the curve fit parameters (basal, E_max, EC50) for the arrestin recruitment experiments and the associated errors/significance (see https://www.graphpad.com/guides/prism/latest/statistics/stat_qa_multiple_comparisons_ after_.htm for a discussion).

The Emin, E_max, and EC50 for M159⁴.⁴⁰C/Q245⁶.²⁸C ACKR3 were compared against the values for WT ACKR3 from Fig. S1 and only the E_max was determined to be significantly different by the extra sum of squares F test. A note has been added to the text to reflect these results on Pg. 5.

“Only the E_max for arrestin recruitment to CXCL12-stimulated ACKR3 was significantly altered by the mutations, while all other pharmacological parameters were the same as for WT receptors.”

(2) The methods do not specify the reactive group of the dyes used for labeling (i.e., AlexaFluor 555-maleimide and Cy5-maleimide?).

We regret the omission and have added the necessary details to the materials and methods.

(3) Were any of the native Cys residues removed from ACKR3 and CXCR4 in the constructs used for smFRET? ACKR3 appears to have two additional Cys residues in the N-terminus besides the one involved in the second disulfide bridge, and these would presumably be solvent-exposed. If so, please specify in the Methods and clarify whether the constructs tested in functional assays included these. (Also, please specify if the human receptors were used.)

No additional cysteine residues were mutated in either receptor. All exposed cysteines are predicted to form disulfides. The residues in the N-terminus that the reviewer alludes to, C21 and C26, form a disulfide (Gustavsson et al. Nature Communications 2017) and are thus protected from our probes. Consistent with these expectations, neither WT CXCR4 nor ACKR3 exhibited significant fluorophore labeling (now mentioned in the text on Pg. 5). The species of origin has been added to the material and methods.

(4) There are a few instances where the data seem to slightly diverge from the proposed models that may be helpful to comment on explicitly in the text:

- Figure 4E (ACKR3/CXCL12(P2G)): As noted in the legend, despite stabilizing R*/R*', CXCL12(P2G) reduces transitions between these states compared to Apo. This is more similar to the effects of VUF16840 (Figure 3D) than the other ACKR3 agonists. The authors note the difference between CXCL12(LHRQ) and CXCL12(P2G) (but not vs Apo) in this regard. There might be some other information here regarding the relative importance of the conformational equilibrium vs transition rates for receptor activity.

Although the TDPs for CXCL12_P2G and VUF16840 are similar, as noted by the reviewer, the overall FRET envelopes are drastically different.

The differences in transition probabilities for R ↔ R’ and R*’ « R* transitions observed in the presence of CXCL12_P2G or CXCL12_LRHQ relative to the apo receptor are now explicitly noted in the Results.

- The conformational distributions of ACKR3 apo and ACKR3 Y257L CXCL12 are very similar (Figure 5A,D). However, there is a substantial difference in the basal activity of WT vs CXCL12stimulated Y257L (Figure S9).

The mutation Y257L appears to promote the highest and lowest FRET states at the expense of the intermediates. Although the distribution appears similar between Apo-WT and CXCL12Y257L, the depopulation of the R’ state may lead to the observed activation in cells.

(5) There are inconsistent statements regarding the compatibility of G protein binding to the "active-like" ACKR3 conformation observed in the authors' previous structures (Yen et al, Sci Adv 2022). In the introduction, the authors seem to be making the case that steric clashes cannot account for its lack of coupling; in the discussion, they seem to consider it a possibility.

The introduction to previous research on the molecular mechanisms governing the lack of ACKR3-G protein coupling was not intended to be all encompassing, but rather to highlight previous efforts to elucidate this process and justify our study of the role  of dynamics. Due to the positions of the probes, we can only comment on the impact on TM6 movements and not other conformational changes. The steric clash reported in Yen et al. was in ICL2 and not directly tested here, so our observations do not preclude changes occurring in this region. We also do not claim that the active-like state resolved in our previous structures matches any specific state isolated here by smFRET.

(6) Line 83-85: "Having excluded other mechanisms we therefore surmised that the inability of ACKR3 to activate G proteins may be due to differences in receptor dynamics."

Line 400-402: "It is possible that the active receptor conformation clashes sterically with the G protein as suggested by docking of G proteins to structures of ACKR3."

As mentioned above, we suspect the mechanisms governing the inability of  ACKR3 to couple to G proteins may be more complex than one particular feature but instead due to a combination of several factors. Accordingly, we have not completely eliminated a contribution of steric hindrance as we described in Yen et al. Sci Adv 2022 and instead include it as a possibility. Following the line highlighted here, we list several alternatives: 

“Alternatively, the receptor dynamics and conformational transitions revealed here may prevent formation of productive contacts between ACKR3 and G protein that are required for coupling, even though G proteins appear to constitutively associate with the receptor.”

And, at the end of the paragraph, we have added the following sentence: 

“The atypical activation of ACKR3 does not appear to be dependent on any singular receptor feature and is likely a combination of several factors.”

(7) If the authors believe that the various ligands/mutations are only altering the distribution/dynamics of the same 3/4 conformations of CXCR4/ACKR3, respectively, is there a reason each FRET efficiency histogram is fit independently instead of constraining the individual components to Gaussian components with the same centroids, and/or globally fitting all datasets for the same receptor?

We performed global analysis across all data sets for each sample and condition. Since the peak positions of the various FRET states recovered in this way were consistent across treatments (Fig. S4,S6), we did not feel it was necessary to perform a further global analysis across all samples for a given receptor.

Reviewer #3 (Recommendations For The Authors):

The manuscript is well-written, the arguments are easy to follow and the figures are helpful and clear. Here are a few questions/suggestions that the authors might want to address before the paper will be published:

(1) Include a table with kinetic rates between states in SI and have a brief discussion in the main text to support the trends observed in transition probabilities.

As noted above, determining rate constants for each of the state-to-state transitions will require a much larger set of experimental smFRET data than is currently available and will be the subject of future studies.

(2) The argument of state similarity (Figure S4 and S6)... why are the profiles not Gaussian, like in the fits on Figures S3 and S5, repectively? I would also suggest that once the number of states is chosen to do a global fit, where the FRET values of a certain sub-state across different conditions for one receptor are shared.

The state distributions presented in Figs. S4 and S6 (as well as throughout the rest of the paper) are derived from HMM fitting of the time traces themselves, and are not constrained to be Gaussian, whereas the GMM analysis in Figs. S3 and S5 are Gaussian fits to the final apparent FRET efficiency histograms.

Similar to our response to Review 2 above, due to the consistency of the fitted peak positions obtained across different conditions for a given sample, we did not feel that further global analysis was necessary.

(3) It is shown FRET changes from ~0.85 in the inactive (closed) state to ~0.25 in the active (open) state. How do these values match the expectations based on crystal structure and dye properties?

As noted in our response to Reviewer 1, translating the apparent FRET values using the assumed Förster distances for A555/Cy5 (per FPbase) suggest a change in D-A distance of ~30 angstroms, whereas the expected change from structures is ~16 Å. We suspect this discrepancy is due to the lipids immediately adjacent to the fluorophores, which may lead to the probes being constrained in an extended position when TM6 moves outwards, thus also reporting the linker length in the distance change. Additionally, such interactions may constrain the donor and acceptor in unfavorable orientations for energy transfer, which would also reduce the FRET efficiency in the active state. Since the calculated D-A distance changes appear too large for GPCR activation, we have opted to not make any structural interpretations. Instead, all of our conclusions are based on resolving individual conformational states and quantifying their relative populations, which is based directly on the measured FRET efficiency distributions, not computed distances.

(4) The results on the effect of CXCL12-P2G on CXCR4 are confusing...despite being an antagonist, this ligand stabilizes the "active state"...I am not sure if the explanation offered is sufficient that the opening of the intracellular cleft is not sufficient to drive the G protein coupling/activation.

We agree that the explanation related to the opening of the intracellular cleft being insufficient to drive G protein coupling/activation is speculative and we have removed that text. We now simply propose that the CXCL12 variants inhibit coupling of G proteins to CXCR4 or disrupt interactions necessary for signaling, as stated in the following text to the results on Pg. 8:

“Despite the ability of CXCL12_P2G and CXCL12_LRHQ to stabilize the active R* conformation of CXCR4, both variants are known to act as antagonists (20). This suggests that the CXCL12 mutants inhibit CXCR4 coupling to G proteins not by suppressing the active receptor population but rather by increasing the dynamics of the receptor state-to-state transitions. Our results suggest that the helical movements considered classic signatures of the active state may not be sufficient for CXCR4 to engage productively with G proteins.”

eLife Assessment

This manuscript focuses on understanding if and how the glycosylation of SARS-CoV2 spike protein affects a putative allosteric network of interactions controlled by the binding of a fatty acid. The main conclusion is that glycans do not significantly affect the network of allosteric interactions. This valuable information - albeit mainly consisting of negative results - is based on convincing evidence. It will be of interest to scientists focusing on SARS CoV2 protein structure and dynamics.

Reviewer #1 (Public Review):

Summary:

The investigation delves into allosteric modulation within the glycosylated SARS-CoV-2 spike protein, focusing on the fatty acid binding site. This study uncovers intricate networks connecting the fatty acid site to crucial functional regions, potentially paving the way for developing innovative therapeutic strategies.

Strengths:

This article's key strength lies in its rigorous use of dynamic nonequilibrium molecular dynamics (D-NEMD) simulations. This approach provides a dynamic perspective on how the fatty acid binding site influences various functional regions of the spike. A comprehensive understanding of these interactions is crucial in deciphering the virus's behavior and identifying potential targets for therapeutic intervention.

Reviewer #2 (Public Review):

This is a nice paper illustrating the use of equilibrium/non-equilibrium MD simulations to explore allosteric communication in the Spike protein. The results are described in detail and suggest a complex network of signal transmission patterns. The topic is not completely novel as it has been studied before by the same authors and the impact of glycosylation is moderated and localized at the furin site, so not many new conclusions emerge here. It is suggested that mutations are commonly found in the communication pathway which is interesting, but the authors fail to provide evidence that this is related to a positive selection and not simply to a random effect related to mutations at points that are not crucial for stability or function. One interesting point is the connection of the FA site with an additional site binding heme group. It will be interesting to see reversibility, i.e. removal of the ligand at this site is producing perturbation at the FA site?, does it produce other effects suggesting a cascade of allosteric effects? Finally, the paper lacks details to help reproducibility, in particular, I do not see details on D-NEMD calculations. One interesting point is the connection of the FA site with an additional site binding heme group.

Reviewer #3 (Public Review):

Summary:

In a previous study, the authors analyzed the dynamics of the SARS-CoV2 spike protein through lengthy MD simulations and an out-of-equilibrium sampling scheme. They identified an allosteric interaction network linking a lipid-binding site to other structurally important regions of the spike. However, this study was conducted without considering the impact of glycans. It is now known that glycans play a crucial role in modulating spike dynamics. This new manuscript investigates how the presence of glycans affects the allosteric network connecting the lipid binding site to the rest of the spike. The authors conducted atomistic equilibrium and out-of-equilibrium MD simulations and found that while the presence of glycans influences the structural responses, it does not fundamentally alter the connectivity between the fatty acid site and the rest of the spike.

Strengths:

The manuscript's findings are based on an impressive amount of sampling. The methods and results are clearly outlined, and the analysis is conducted meticulously.

Author response:

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

Reviewer #1:

We thank the Reviewer for being very supportive of the work and acknowledging how important it is to understand allosteric modulation in the spike and the potential of this knowledge to contribute to the design of novel therapeutic strategies (for example, disrupting or altering the allosteric networks within the spike can be a novel strategy for drug development against COVID-19). We address their comments below: 

(1) The Reviewer states that although the strategy used to extract the responses has been "previously validated", the complexity of the interactions investigated requires "a robust statistical analysis, which is not shown quantitatively". 

As the Reviewer points out, the D-NEMD approach has been previously validated in various protein systems ranging from soluble enzymes to integral membrane proteins, including the spike (e.g. [Kamsri et al. (2024) Biochem; Beer et al. (2024) Chem Sci; Oliveira et al. (2023) J Mol Cell Biol; Chan et al. (2023) JACS Au; Castelli et al. (2023) JACS; Castelli et al. (2023) Protein Sci; Oliveira et al. (2022) Comput Struct Biotechnol J; Gupta et al. (2022) Nat Comm; Oliveira et al. (2021) JACS; Galdadas et al. (2021) eLife; Abreu et al. (2019) Proteins; Oliveira et al. (2019) JACS; Oliveira et al. (2019) Structure]. The Kubo-Onsager relation is used to extract the evolution of the protein's response to a perturbation by comparing the equilibrium and nonequilibrium trajectories at equivalent points in time. The calculated responses at individual times are then averaged over all the repeats (210 repeats in the current work), and the standard error of the mean (SEM) is used to assess the significance of the average response. The SEM indicates how much the calculated mean deviates from the true population mean. Calculating the SEM allows us to determine how accurate the measured response is as an estimate of the population response and assess the convergence of our calculations. The evolution of the average C_α displacement and corresponding SEM values for each individual monomer can be visualised in detail in Figures S7-S9. We have added a new sentence to the Materials and Methods section in the Supporting Information, explicitly stating how the convergence and statistical significance of the responses were assessed.

(2) The Reviewer considers that the evidence presented in the paper "is compelling" but suggests performing a sequence analysis to facilitate the understanding of the results by the scientific community. 

We thank the Reviewer for their excellent suggestion to perform a sequence analysis of the FA site region and its allosteric connections. Indeed, this analysis (Figure S24) clearly shows that several of the mutations, deletions and insertions in the Alpha, Beta, Gamma, Delta, and Omicron variants are located either in or near the regions of the protein shown to respond to the removal of linoleate from the FA site. These sequence changes affect the protein's responses, and are responsible for the differences in allosteric behaviour observed between variants, as described previously for the non-glycosylated spike [Oliveira et al. (2023) J Mol Cell Biol]. Furthermore, some variants, such as Beta, Gamma, and Omicron, contain residue substitutions at the FA site. For example, the lysine in position 417 in the ancestral spike is mutated to asparagine in Beta and Omicron and threonine in the Gamma variant. Another example is arginine 408 in the original protein, which has been replaced by asparagine in several Omicron sub-variants. 

To summarise, the sequence analysis (Figure S24) supports our initial 3D analysis (Figure S25), indicating that many of the changes observed in the variants of concern are indeed in or close to the allosteric networks involving the FA site. We have now included the sequence analysis results in the current paper and added a new figure to Supporting Information showing the sequence alignments between the ancestral spike and different variants (Figure S24). 

(3) The Reviewer also has "minor considerations": first, they point to a discrepancy in the presentation of residue values S325 in the plots of Chains A, B, and C of Figure S3; second, they ask why several regions, such as RBM and Furin Site in figures S6, S7, and S8 show significant changes.

To answer both points raised by the Reviewer, we need to start by explaining that the spike typically features 22 N-glycosylation and at least two O-glycans sites per monomer. These sites have been found to be heterogeneously populated in different experimental studies (e.g. [Watanabe et al. (2020) Science; Shajahan et al. (2020) Glycobiology; Zhang et al. (2021) Mol Cell Proteomics]). Given this, the spike model used as the starting point for this work reflects this heterogeneity, with asymmetric site-specific glycosylation profiles derived from the glycoanalytic data reported by Watanable et al. for N-glycans [Watanabe et al. (2020) Science] and Shajahan et al. for O-glycans [Shajahan et al. (2020) Glycobiology]. This means that the glycan occupancy and composition for each site differ between the three monomers. For example, while monomer A contains the two O-glycans sites (linked to T323 and S325, respectively) fully occupied, monomers B and C only contain the T323 O-glycan. A detailed description of the glycosylation of the spike model is given in the supporting information of [Casalino et al. (2020) ACS Cent Sci].

Regarding the Reviewer's first minor point, the discrepancy in behaviour observed in Figure S3 for S325 is related to the fact that this glycosylation site is only occupied in monomer A, with no glycans present in this site in monomers B and C. 

Regarding the second point, the differences observed in the responses between the three monomers in Figures S7-S9 are probably due to asymmetries in the protein dynamics introduced by the different glycosylation patterns in the monomers. 

We have now added a new paragraph to the materials and methods section in the Supporting Information describing the asymmetric site-specific glycosylation profiles of the monomers.

(4) Due to the complexity of the allosteric interactions observed, the Reviewer suggests including in the paper a "diagram showing the flow of allosteric interactions" or a "vector showing how the perturbation done in the FA Active site takes contact with other relevant regions". 

This is an excellent suggestion to facilitate the visualisation of the allosteric networks. We have added a new figure to Supporting Information highlighting the allosteric pathways identified from the DNEMD simulations and the direction of the propagation of the structural changes (Figure S26).

Reviewer #2:

We thank the Reviewer for their time in evaluating our manuscript and providing suggestions for improving it and ideas for further work. We are happy that the Reviewer found this to be a "nice paper" with the calculations "well done" and interesting results. We address their comments below: 

(1) The Reviewer suggests improving the paper by adding a more detailed explanation of the DNEMD simulations approach, a method that, although proposed decades ago, is still generally unfamiliar to the community. They also asked for "information on the convergence of the observables".

As stated by the Reviewer, a dynamical approach to nonequilibrium molecular dynamics (D-NEMD) was first proposed in the seventies by Ciccotti et al. [Ciccotti et al. (1975) Phys Rev Lett; Ciccotti et al. (1979) J Stat Phys]. This approach combines MD simulations in equilibrium and nonequilibrium conditions. The rationale for the D-NEMD approach is simple and can be described as follows: if an external perturbation (e.g. binding/unbinding of a ligand) is added to a simulation sampling an equilibrium state and, by doing so, a parallel nonequilibrium simulation is started, the structural response of the protein to the perturbation can be directly measured by comparing the equilibrium and nonequilibrium trajectories at equivalent points in time by using the Kubo-Onsager relation as long as enough sapling is gathered (for more details, please see the reviews [Balega et al. (2024) Mol Phys; Oliveira et al. (2021) Eur Phys J B; Ciccotti et al. (2016) Mol Simul]). This approach, although conceptually simple, is very powerful as it allows for computing the evolution of the dynamic response of the protein to the external perturbation, while assessing the convergence and statistical significance of that response. This approach also has the advantage that the convergence and significance of the response can be easily evaluated, and the associated errors can be computed and made as small as desirable by increasing the number of nonequilibrium trajectories. Determining the statistical errors associated with the responses (through, e.g., the determination of the standard error of the mean, SEM) is essential to test if the sampling gathered is sufficient. In this paper, the SEM was calculated for each average C_α displacement value at times 0.1, 1 and 10 ns after the removal of linoleate, LA (see Figures S7-S9). The SEM indicates how accurate the measured response is as an estimate of the population response and allows us to assess the convergence of the results. 

Generally, multiple (tens to hundreds) D-NEMD simulations are needed to achieve statistically significant results for biomolecular systems (for examples, see [Balega et al. (2024) Mol Phys; Oliveira et al. (2021) Eur Phys J B]). As such, the length of the D-NEMD simulations (typically 5 to 10 ns) reflects the balance between the computational resources available and the number of replicates needed to achieve statistically significant responses from the system. Following the Reviewer's suggestion, we have now added a brief description of the D-NEMD approach to the main manuscript and expanded the D-NEMD section in the Supporting Information with a more detailed description of the method, including adding a new figure showing a schematic representation of the D-NEMD approach (Figure S5) as well as explicitly stating the settings used in these simulations and how the statistical significance of the responses was assessed. 

(2) The Reviewer suggests comparing the D-NEMD results with "more traditional analysis, such as correlation analysis, or community network analysis". 

We agree with the Reviewer that this is an important comparison, which can provide a broader, more articulate and coherent picture of spike allostery and have, therefore, performed additional analysis. The dynamic cross-correlation analysis suggested by the Reviewer is a valuable tool for identifying the regions in the protein influenced by the FA site in equilibrium conditions. However, such an approach is not straightforwardly applicable to D-NEMD simulations, as these simulations are not in equilibrium. Nevertheless, as suggested by the Reviewer, we have determined the cross-correlation matrices for both the equilibrium and D-NEMD simulations (Figure S22), similar to those in our previous work [Galdadas et al. (2021) eLife] and [Oliveira et al. (2022) J Mol Cell Biol]. The analysis of these matrices can provide information about possible allosteric networks. In Figure S22, the cyan and blue regions represent moderate and high negative correlations between C_α atoms, while orange and red regions correspond to moderate and high positive correlations. Negative correlations indicate residues moving in opposite directions (moving toward or away from each other). In contrast, positive values imply that the residues are moving in similar directions. We also note that, with collaborators, we have compared D-NEMD and other nonequilibrium and equilibrium MD analysis methods for allostery [Castelli et al.  (2023) JACS].

The cross-correlation maps depicted in Figure S22 show moderate to high positive correlations between the FA sites and two of the three RBDs in the protein. This happens because each FA site sits at the interface between two neighbouring RBDs. Low to moderate negative and mildly positive correlated motions can also be observed between the FA site and the NTDs and fusion peptide surrounding regions, respectively. To facilitate the visualisation of the above-described motions, we have also mapped the statistical correlations for R408 and K417 (two FA site residues able to directly form salt-bridge interactions with the carboxylate head group of LA) on the protein's three-dimensional structure (Figure S23). Figure S23 highlights the patterns of movement described above and allows us to identify the regions whose motions are coupled to the FA site.

Interestingly, some segments forming the signal propagation pathways, such as R454-K458 in all three monomers, and C525-K537 in monomers B and C, can also be identified from the cross-correlation matrices, showing moderate to high correlations with the FA site (Figures S22-S23). The crosscorrelation maps computed from the equilibrium trajectories (with FA sites occupied with LA) show a slight increase in the dynamic correlations, mainly for the RBDs, compared to the maps obtained from the nonequilibrium trajectories (Figure S22). This indicates that the presence of LA in the FA strengthens the connections between the FA site and other parts of the protein. 

We have updated the manuscript to include the cross-correlation analysis, with two new figures added to Supporting Information: one depicting the cross-correlation maps for the D-NEMD and equilibrium simulations (Figure S22), and the other showing the statistical correlations for R408 and K417 (Figure S23). 

(3) The Reviewer considers the observed connection between the fatty acid site and the heme/biliverdin site "interesting" and suggests "exploring the impact of ligand removal on this secondary site on the protein".

Similarly to the Reviewer, we find the connection between the FA and the heme/biliverdin site fascinating and worthy of further investigation. The observed connection between these two sites shows the complexity of the allosteric effects in the spike. It would be interesting and informative to perform new equilibrium simulations of the heme/biliverdin spike complex and a new set of D-NEMD simulations in which this site is perturbed (e.g. through the removal of the heme group) to map the networks connecting this allosteric site to other functionally important regions of the spike, including the FA site and potentially other allosteric sites. These new simulations would allow us to assess the reversibility of the connection between the FA and heme/biliverdin sites and enhance our understanding of allosteric modulation in the spike and the role of the heme/biliverdin site in this process. However, due to the large size of the system and the associated computational demands, such simulations are not possible within the timeframe of the revision of this paper. These simulations would take many months to complete using our HPC resources. We also note that an experimental structure of the spike containing both heme and linoleate is not available. Further simulation analysis of the communication pathways involving the heme/biliverdin site is an excellent idea for future work.

(4) The Reviewer "liked the mapping of existing mutations on the communication pathway" and suggested a more detailed study focusing on the effect of the mutations. 

We fully agree with the Reviewer and consider that a detailed study focusing on the effect of the mutations, insertions, and deletions in the different glycosylated variants of concern (including new emerging ones) would be of great interest. Our previous work using D-NEMD on the non-glycosylated ancestral, Alpha, Delta, Delta plus and Omicron BA.1 spikes revealed significant differences in the allosteric responses to LA removal, with the changes in the variants affecting both the amplitude of the structural responses and the rates at which these rearrangements propagate within the protein [Oliveira et al. (2023) J Mol Cell Biol]. 

Using the D-NEMD approach to systematically investigate the impact of each individual mutation and their contribution to the overall allosteric response of the glycosylated variants (similar to what we have done previously for the D614G mutation in the non-glycosylated protein [Oliveira et al. (2021) Comput Struct Biotechnol J]) would provide insights into the functional modulation of the spike. However, as noted above in point 3, spike simulations are highly computationally expensive, both in terms of processing and data storage requirements, because of the large size of the protein and the need for equilibrium and D-NEMD simulations. This makes the suggested mutational study unfeasible within the timeframe of the current revisions. It is, however, an excellent idea for future research.

Reviewer #3:

We thank the Reviewer for carefully reading and critically reviewing this work and recognising that the findings reported are "based on an impressive amount of sampling" and "meticulous" analysis. We address their comments below: 

(1) The Reviewer considers that this work "does not clearly show any new findings" as it shows that the glycans do not significantly impact the internal networks in the protein.

We respectfully disagree with the Reviewer. This work identifies new allosteric effects in the spike, specifically, the connection of the FA site with the heme binding site. The equilibrium simulations alone provide the first analysis of the effects of linoleate binding in the fully glycosylated spike. The finding that glycosylation does not significantly affect the allosteric pathways in the spike is in itself an important finding. Previous D-NEMD simulations investigated only the non-glycosylated spike ([Oliveira et al. (2021) Comput Struct Biotechnol J; Oliveira et al. (2022) J Mol Cell Biol] ) leading to questions of whether the allosteric effects pathways were changed by glycosylation; our results here show that the main conclusions are reinforced, but glycosylation does have some effect on networks, and also on the speed of the dynamical response. To the best of our knowledge, our work represents the first investigation to analyse the impact of glycosylation on the allosteric networks in the spike. We show that even though the presence of glycans in the exterior of the spike does not significantly alter the internal communication pathways in the protein, in some cases (for example, the glycans linked to N234, T373 and S375), they create direct connections between different regions, which may facilitate the propagation of the structural changes. 

(2) The Reviewer suggests adding a "clear and concise description" of the D-NEMD approach to the manuscript.

We appreciate that the use of the D-NEMD method to study biomolecular systems is relatively new, and so may be unfamiliar. As explained above in our response to Reviewer 2 (point 1), a brief description of the D-NEMD approach was now included in the main manuscript. A detailed description of the method was also added to Supporting Information, including a new figure representing the rationale for the approach (Figure S5). The interested reader is directed to previous applications and reviews for more details of the method (e.g. [Balega et al. (2024) Mol Phys; Oliveira et al. (2021) Eur Phys J B; Ciccotti et al. (2016) Mol Simul; Kamsri et al. (2024) Biochem; Beer et al. (2024) Chem Sci; Oliveira et al. (2023) J Mol Cell Biol; Chan et al. (2023) JACS Au; Castelli et al. (2023) JACS; Castelli et al. (2023) Protein Sci; Oliveira et al. (2022) Comput Struct Biotechnol J; Gupta et al. (2022) Nat Comm; Oliveira et al. (2021) JACS; Galdadas et al. (2021) eLife; Abreu et al. (2019) Proteins; Oliveira et al. (2019) JACS; Oliveira et al. (2019) Structure]). 

(3) The Reviewer invites us to "discuss the robustness of the findings with respect to forcefield choices".

The Reviewer raises an important but rather complex question, and one which can, of course, be posed for any molecular dynamics simulation study. The short answer is that we have chosen state-of-the-art forcefields, which have been shown to give results for the spike that are in good agreement with experiments; glycosylated spike simulations are rather computationally expensive, and constructing the models also requires significant human time and effort. Thus, while in principle interesting, it is not practical to repeat the current simulations with different forcefields. However, as detailed below, comparison of our simulations of the glycosylated and non-glycosylated [Oliveira et al. (2022) Comput Struct Biotechnol J] spike using different forcefields indicates that our conclusions are robust and are not dependent on the choice of forcefield. 

Comparing the performance and accuracy of different force fields is not straightforward, as the results depend on the system of interest, properties simulated and sampling. In this work, the CHARMM36m all-atom additive force field was used to describe the protein and glycans. CHARMM36m is a widely used force field that has previously been validated for the simulations of biological systems [Huang et al. (2013) J Comput Chem; Guvench et al. (2009) J Chem Theory Comput], including proteins, lipids and glycans, with many of studies adopting it in the literature. Additionally, the glycosylated models of the spike used in this work have also been successfully applied and tested before (e.g. [Dommer et al. (2023) Int J High Perform Comput Appl; Sztain et al. (2021) Nat Chem; Casalino et al. (2021) Int J High Perform Comput Appl; Casalino et al. (2020) ACS Cent Sci]), with their dynamics shown to correlate well with experimental data.   

It is also worth pointing out that, despite differences in the amplitude of the responses, the allosteric networks identified using the D-NEMD approach for the non-glycosylated [Oliveira et al. (2022) Comput Struct Biotechnol J] and glycosylated spikes are generally similar (Figure S13). While the responses for the non-glycosylated protein were extracted from simulations using the AMBER99SBILDN forcefield [Oliveira et al. (2022) Comput Struct Biotechnol J], those reported in this work were obtained from trajectories using the CHARMM36m forcefield. The similarity between the responses for the two systems (which were simulated using different forcefields) is a good indication that our findings are forcefield independent. 

(4) The Reviewer suggests comparing our findings with "alternative methods of analysing allostery". 

As stated above in our response to Reviewer 2 point 2, we consider the suggested comparison an excellent idea. We have therefore performed a dynamic cross-correlation analysis to identify the regions in the protein coupled to the FA site in both equilibrium and nonequilibrium conditions (see Figures S22-S23). Overall, this analysis shows that the FA site motions are strongly coupled to the RBDs and moderately to weakly connected to the NTDs and fusion peptide surrounding regions (please see a detailed description of the results of the correlation analysis in our response to Reviewer 2 point 2). The cross-correlation analysis performed was added to the manuscript, and two new figures were included in the Supporting Information (Figures S22-S23): the first, showing the cross-correlation maps for the D-NEMD and equilibrium simulations; the second, showing the statistical correlations for R408 and K417 (two residues forming the FA site and that can directly interact with the carboxylate head group of LA). 

We agree that comparing different allosteric analysis methods is interesting, informative and important. As noted above, we have compared D-NEMD and other nonequilibrium and equilibrium MD analysis methods for allostery in the well-characterised K-Ras system [Castelli et al.  (2023) JACS].

eLife Assessment

In this manuscript, Abd El Hay and colleagues use an innovative behavioral assay and analysis method, together with standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons, to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. Compelling evidence is provided for a role of TRPM2 channels in warmth avoidance behavior, but it remains unclear whether this involves channel activity in the periphery or in the brain. In contrast, TRPV1 is clearly implicated at the cellular level in warmth detection. These findings are important because there is substantial ongoing discussion regarding the contribution of TRP channels to different aspects of thermo-sensation.

Reviewer #3 (Public review):

A central question in the thermal system is which thermally responsive ion channels are responsible for warm evoked behaviors and DRG afferent neuron responses to warming. Recent work has shown evidence for TRPV1, TRPM2 and TRPM8. Here Abd El Hay and colleagues investigate the role of TRPM2 and TRPV1 in a novel warm preference behavior and in the thermal responses of cultured DRG neurons.

They develop a new thermal preference task, where both the floor and air temperature are controlled, which shows differences to the classic two-plate preference task. This is a central strength of the paper, as it will allow a new method to investigate how animals integrating floor and air temperature. They go on to use knockout mice and confirm a clear role for TRPM2 in warm preference behavior.

Using a new approach for culturing DRG neurons they investigate the involvement of both channels in warm responsiveness and dynamics. In apparent contrast to the role of TRPM2 on thermal behavior, it does not have a major effect on the responses of cultured DRG neurons to warm stimuli. Eliminating TRPV1 however has a stronger impact on DRG responses, particularly at low stimulus amplitudes. It will be important to discover how TRPM2 influences warm driven behaviors, if it is not via changes in afferent response properties.

Thanks to the authors for addressing my remaining questions in this updated version of the manuscript.

This is an interesting study with novel approaches that generates new information on the differing roles of TRPV1 and TRPM2 on thermal behavior.

Author response:

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

Public Reviews:  

Reviewer # 1 (Public Review): 

Summary:

The authors use an innovative behavior assay (chamber preference test) and standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. They find a profound effect of TRPM2 elimination in the behavioral assay, whereas the elimination of TRPV1 has the largest effect on the neuronal responses. These findings are very important, as there is substantial ongoing discussion in the field regarding the contribution of TRP channels to different aspects of thermosensation.

Strengths:

The chamber preference test is an important innovation compared to the standard two-plate test, as it depends on thermal information sampled from the entire skin, as opposed to only the plantar side of the paws. With this assay, and the detailed analysis, the authors provide strong supporting evidence for a role of TRPM2 in warmth avoidance. The conceptual framework using the Drift Diffusion Model provides a first glimpse of how this decision of a mouse to change between temperatures can be interpreted and may form the basis for further analysis of thermosensory behavior.

Weaknesses:

The authors juxtapose these behavioral data with calcium imaging data using isolated DRG neurons. As the authors acknowledge, it remains unclear whether the clear behavioral effect seen in the TRPM2 knockout animals is directly related to TRPM2 functioning as a warmth sensor in sensory neurons. The effects of the TRPM2 KO on the proportion of warmth sensing neurons are very subtle, and TRPM2 may also play a role in the behavioral assay through its expression in thermoregulatory processes in the brain. Future behavioral experiments on sensory-neuron specific TRPM2 knockout animals will be required to clarify this important point.

Reviewer # 1 (Recommendations for the authors):

(1) I have no further suggestions for the authors, and congratulate them with their excellent study.

For the authors information, ref. 42 does contain behavioral data from both male (Fig. 4 and Extended Figure 7) and female (Extended Figure 8) mice.

We thank the referee for pointing out that both males and female mice were tested in the Vandewauw et al. 2018 study. We deliberated whether to include this at the appropriate section of our manuscript (“Limitations of the Study”). But since Vandewauw et al. assessed noxious heat temperatures and we here assess innocuous warmth temperature, we felt that this reference would not add to the clarification whether there are sex differences in Trp channelbased warmth temperature sensing. In particular, we did not want to “use” the argument and to suggest that there are no sex temperature differences in the warmth range just because Vandewauw et al. did not observe major sex differences in the noxious temperature range. 

Reviewer #3 (Public Review):  

Summary and strengths:

In the manuscript, Abd El Hay et al investigate the role of thermally sensitive ion channels TRPM2 and TRPV1 in warm preference and their dynamic response features to thermal stimulation. They develop a novel thermal preference task, where both the floor and air temperature are controlled, and conclude that mice likely integrate floor with air temperature to form a thermal preference. They go on to use knockout mice and show that TRPM2-/- mice play a role in the avoidance of warmer temperatures. Using a new approach for culturing DRG neurons they show the involvement of both channels in warm responsiveness and dynamics. This is an interesting study with novel methods that generate important new information on the different roles of TRPV1 and TRPM2 on thermal behavior.

Comments on revisions:

Thanks to the authors for addressing all the points raised. They now include more details about the classifier, better place their work in context of the literature, corrected the FOVs, and explained the model a bit further. The new analysis in Figure 2 has thrown up some surprising results about cellular responses that seem to reduce the connection between the cellular and behavioral data and there are a few things to address because of this:

(1) TRPM2 deficient responses: The differences in the proportion of TRPM2 deficient responders compared to WT are only observed at one amplitude (39C), and even at this amplitude the effect is subtle. Most surprisingly, TRPM2 deficient cells have an enhanced response to warm compared to WT mice to 33C, but the same response amplitude as WT at 36C and 39C. The authors discuss why this disconnect might be the case, but together with the lack of differences between WT and TRPM2 deficient mice in Fig 3, the data seem in good agreement with ref 7 that there is little effect of TRPM2 on DRG responses to warm in contrast to a larger effect of TRPV1. This doesn't take away from the fact there is a behavioral phenotype in the TRPM2 deficient mice, but the impact of TRPM2 on DRG cellular warm responses is weak and the authors should tone down or remove statements about the strength of TRPM2's impact throughout the manuscript, for example:

"Trpv1 and Trpm2 knockouts have decreased proportions of WSNs."

"this is the first cellular evidence for the involvement of TRPM2 on the response of DRG sensory neurons to warm-temperature stimuli"

"we demonstrate that TRPV1 and TRPM2 channels contribute differently to temperature detection, supported by behavioural and cellular data"

"TRPV1 and TRPM2 affect the abundance of WSNs, with TRPV1 mediating the rapid, dynamic response to warmth and TRPM2 affecting the population response of WSNs."

"Lack of TRPV1 or TRPM2 led to a significant reduction in the proportion of WSNs, compared to wildtype cultures".

We agree with the referee that the somewhat surprising result of the subtle phenotype in Trpm2 knock-out DRG culture experiments, that became detectable in the course of the new analysis, was overemphasized in the previous version of the manuscript. Per suggestion, we have toned down or removed the statements in the revised manuscript (for the referee to find those changes easily, they are indicated in “track-changes mode” in the submitted document).  

(2) The new analysis also shows that the removal of TRPV1 leads to cellular responses with smaller responses at low stimulus levels but larger responses with longer latencies at higher stimulus levels. Authors should discuss this further and how it fits with the behavioral data.

Because these changes shown in Fig. 2E are also subtle (similar to the cellular Trpm2 phenotype discussed above), and because both the “% Responders” (Fig 2.D) and The AUC analysis (Fig. 2F) show a reduction in Trpv1 knock out cultures ––both, at lower and at higher stimulus levels–– we did not want to overstate this difference too much and therefore did not further discuss this aspect in the context of the behavioral differences observed in the Trpv1 knock-out animals.  

(3) Analysis clarification: authors state that TRPM2 deficient WSNs show "Their response to the second and third stimulus, however, are similar to wildtype WSNs, suggesting that tuning of the response magnitude to different warmth stimuli is degraded in Trpm2-/- animals." but is there a graded response in WT mice? It looks like there is in terms of the %responders but not in terms of response amplitude or AUC. Authors could show stats on the figure showing differences in response amplitude/AUC/responders% to different stimulus amplitudes within the WT group.

We have added the statistics in the main text, you find them on page 7 (also in “track changes mode”).

(4) New discussion point: sex differences are "similar to what has been shown for an operant-based thermal choice assay (11,56)", but in their rebuttal, they mention that ref 11 did not report sex differences. 56 does. Check this.

Thank you for pointing out this mishap. We have now corrected this in the “Limitations of the study” section of the discussion and have removed the Paricio-Montesions et al study from that section and slightly revised the text (see “track-changes” on page 16).

(5) The authors added in new text about the drift diffusion model in the results, however it's still not completely clear whether the "noise" is due to a perceptual deficit or some other underlying cause. Perhaps authors could discuss this further in the discussion.

We have now included more discussion concerning this (page 14):

“However, the increased noise in the drift-di3usion model points to a less reliable temperature detection mechanism. Although noise in drift di3usion models can encompass various sources of variability—ranging from peripheral sensory processing to central mechanisms like attention or motor initiation—the most parsimonious interpretation in our study aligns with a perceptual deficit, given the altered temperatureresponsive neuronal populations we observed. This implies that, despite the substantial loss of WSNs, the remaining neuronal population provides su3icient information for the detection of warmer temperatures, albeit with reduced precision”

Within the limits of the data that is available, we hope the referee agrees with us that we have now adequately discussed this aspect; we feel that any further discussion would be too speculative.

eLife Assessment

This is an important study that generates an inventory of accessible genomic regions bound by a transcription factor ZFHX3 within the suprachiasmatic nucleus in the hypothalamus and details the impact of its depletion on daily rhythms in behavior and gene expression patterns. Analysis using circadian phase-estimation algorithms makes the argument that gene regulatory networks are at play and changes in gene expression of a few clock genes cannot account for the observed animal behaviour. While the transcriptome analysis is compelling, the data on the activity of the TF in rhythmic gene expression is solid, and interpretations that allow for direct and/or indirect roles have been incorporated.

Reviewer #1 (Public review):

Summary:

Authors of this article have previously shown the involvement of the transcription factor Zinc finger homeobox-3 (ZFHX3) in the function of the circadian clock and the development/differentiation of the central circadian clock in the suprachiasmatic nucleus (SCN) of the hypothalamus. Here, they show that ZFHX3 plays a critical role in the transcriptional regulation of numerous genes in the SCN. Using inducible knockout mice, they further demonstrate that the deletion Of Zfhx3 induces a phase advance of the circadian clock, both at the molecular and behavioral levels.

Strengths:

- Inducible deletion of Zfhx3 in adults<br /> - Behavioral analysis<br /> - Properly designed and analyzed ChIP-Seq and RNA-Seq supporting the conclusion of the behavioral analysis

Comments on revisions:

The authors have properly addressed reviewers' issues.

Reviewer #2 (Public review):

Summary

ZFHX3 is a transcription factor expressed in discrete populations of adult SCN and was shown by the authors previously to control circadian behavioral rhythms using either a dominant missense mutation in Zfhx3 or conditional null Zfhx3 mutation using the Ubc-Cre line (Wilcox et al., 2017). In the current manuscript, the authors assess the function of ZFHX3 by using a multi-omics approach including ChIPSeq in wildtype SCNs and RNAseq of SCN tissues from both wildtype and conditional null mice. RNAseq analysis showed a loss of oscillation in Bmal1 and changes in expression levels of other clock output genes. Moreover, a phase advance gene transcriptional profile using the TimeTeller algorithm suggests the presence of a regulatory network that could underlie the observed pattern of advanced activity onset in locomotor behavior in knockout mice.

In Figure 1, the authors identified the ZFHX3 bound sites using ChIPseq and compared the loci with other histone marks that occur at promoters, TSS, enhancers and intergenic regions. And the analysis broadly points to a role for ZFHX3 in transcriptional regulation. The vast majority of nearly 40000 peaks overlapped H3K4me3 and K27ac marks, active promoters which also included genes falling under the GO category circadian rhythms. However, no significant differential ZFHX3 bound peaks were detected between ZT3 and ZT15. In these experiments, it is not clear if and how the different ChIP samples (ZFHX3 and histone PTM ChIPs) were normalized/downsampled for analysis. Moreover, it seems that ZFHX3 binding or recruitment has little to do with whether the promoters are active.

Based on an enrichment of ARNT domains next to K4Me3 and K27ac PTMs, the authors propose a model where the core-clock TFs and ZFHX3 interact. If the authors develop other assays beyond just predictions to test their hypothesis, it would strengthen the argument for a role in circadian transcription in the SCN. It would be important in this context to perform a ChIP-seq experiment for ZFHX3 in the knockout animal (described from Figure 2 onwards) to eliminate the possibility of non-specific enrichment of signal from "open chromatin'. Alternatively, a ChIPseq analysis for BMAL1 or CLOCK could also strengthen this argument to identify the sites co-occupied by ZFHX3 and core-clock TFs.

Next, they compared locomotor activity rhythms in floxed mice with or without tamoxifen treatment. As reported before in Wilcox et al 2017, the loss of ZFHX3 led to a shorter free running period and reduced amplitude and earlier onset of activity. Overall, the behavioral data in Figure 2 and supplementary figure 2 has been reported before and are not novel.

Next, the authors performed RNAseq at 4hr intervals on wildtype and knockout animals maintained in light/dark cycles to determine the impact of loss of ZFHX3. Overall transcriptomic analysis indicated changes in gene expression in nearly 36% of expressed genes, with nearly half being upregulated while an equal fraction was downregulated. Pathways affected included mostly neureopeptide neurotransmitter pathways. Surprisingly, there was no correlation between the direction in change in expression and TF binding since nearly all the sites were bound by ZFHX3 and the active histone PTMs. The ChIP-seq experiment for ZFHX3 in the UBC-Cre+Tam mice again could help resolve the real targets of ZFHX3 and the transcriptional state in knockout animals.

To determine the fraction of rhythmic transcripts, Using dryR, the authors categorise the rhythmic transcriptome (about 7% in all) into modules that include genes that lose rhythmicity in the KO, gain rhythmicity in the KO or remain unaffected or partially affected. The analysis indicates that a large fraction of the rhythmic transcriptome is affected in the KO model. However, among core-clock genes only Bmal1 expression is affected showing a complete loss of rhythm. The authors state a decrease in Clock mRNA expression (line 294) but the panel figure 4A does not show this data. Instead it depicts the loss in Avp expression - {{ misstated in line 321 ( we noted severe loss in 24-h rhythm for crucial SCN neuropeptides such as Avp (Fig. 3a).}}

However, core-clock genes such as Pers and Crys show minor or no change in expression patterns while Per2 and Per3 show a ~2hr phase advance. While these could only weakly account for the behavioral phase advance, the authors used TimeTeller to assess circadian phase in wildtype and ZFHX3 deficient mice. This approach clearly indicated that while the clock is not disrupted in the knockout animals, the phase advance can be correctly predicted from a network of gene expression patterns.

Strengths

The authors use a multiomic strategy in order to reveal the role of the ZFHX3 transcription factor with a combination of TF and histone PTM ChIPseq, time-resolved RNAseq from wildtype and knockout mice and modeling the transcriptomic data using TimeTeller. The RNAseq experiments are nicely controlled and the analysis of the data indicates a clear impact on gene-expression levels in the knockout mice and the presence of a regulatory network that could underlie the advanced activity onset behavior.

Weaknesses

It is not clear whether ZFHX3 has a direct role in any of the processes and seems to be a general factor that marks H3K4me3 and K27ac marked chromatin. Why it would specifically impact the core-clock TTFL clock gene expression or indeed daily gene expression rhythms is not clear either. Details for treatment of different ChIP samples (ZFHX3 and histone PTM ChIPs) on data normalization for analysis are needed. The loss of complete rhythmicity of Avp and other neuropeptides or indeed other TFs could instead account for the transcriptional deregulation noted in the knockout mice.

Comments on revisions:

The authors addressed the majority of my criticisms. They also explained that some requested experiments are beyond the scope of the current manuscript, while others are technically not feasible. I do not have any further concerns.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Authors of this article have previously shown the involvement of the transcription factor Zinc finger homeobox-3 (ZFHX3) in the function of the circadian clock and the development/differentiation of the central circadian clock in the suprachiasmatic nucleus (SCN) of the hypothalamus. Here, they show that ZFHX3 plays a critical role in the transcriptional regulation of numerous genes in the SCN. Using inducible knockout mice, they further demonstrate that the deletion Of Zfhx3 induces a phase advance of the circadian clock, both at the molecular and behavioral levels.

Strengths:

- Inducible deletion of Zfhx3 in adults

- Behavioral analysis

- Properly designed and analyzed ChIP-Seq and RNA-Seq supporting the conclusion of the behavioral analysis

Weaknesses:

- Further characterization of the disruption of the activity of the SCN is required.

(1) We thank the reviewer for their valuable inputs. Indeed, a comprehensive behavioral assessment of mice of this genotype was executed in Wilcox et al. ;2017 study. In Wilcox et al.; 2017, Figure 4, 6-h phase advance (jetlag) clearly showed faster reentrainment in ZFHX3-KO mice when compared to the controls.

- The description of the controls needs some clarification.

(2) We agree with the reviewer and have modified the text at line 211-212 to clearly describe the controls.

Reviewer #2 (Public review):

Summary:

ZFHX3 is a transcription factor expressed in discrete populations of adult SCN and was shown by the authors previously to control circadian behavioral rhythms using either a dominant missense mutation in Zfhx3 or conditional null Zfhx3 mutation using the Ubc-Cre line (Wilcox et al., 2017). In the current manuscript, the authors assess the function of ZFHX3 by using a multi-omics approach including ChIPSeq in wildtype SCNs and RNAseq of SCN tissues from both wildtype and conditional null mice. RNAseq analysis showed a loss of oscillation in Bmal1 and changes in expression levels of other clock output genes. Moreover, a phase advance gene transcriptional profile using the TimeTeller algorithm suggests the presence of a regulatory network that could underlie the observed pattern of advanced activity onset in locomotor behavior in knockout mice.

In figure1, the authors identified the ZFHX3 bound sites using ChIPseq and compared the loci with other histone marks that occur at promoters, TSS, enhancers and intergenic regions. And the analysis broadly points to a role for ZFHX3 in transcriptional regulation. The vast majority of nearly 40000 peaks overlapped H3K4me3 and K27ac marks, active promoters which also included genes falling under the GO category circadian rhythms. However, no significant differential ZFHX3 bound peaks were detected between ZT3 and ZT15. In these experiments, it is not clear if and how the different ChIP samples (ZFHX3 and histone PTM ChIPs) were normalized/downsampled for analysis. Moreover, it seems that ZFHX3 binding or recruitment has little to do with whether the promoters are active.

(3) We thank the reviewer for their valuable comment. Different ChIP samples (ZFHX3 and histone PTM ChIPs) were treated in the same manner from preprocessing (quality control by FastQC, adapter trimming, alignment to mm10 genome) and peak calling was performed using respective input samples as control using MACS2 as mentioned in Methods. The data was normalized using bamCoverage tools and bigwig files were generated for visual inspection using UCSC Genome Browser. These additional details are added to Methods at line 592. Finally, BEDTools was employed to study overlapping peaks between ZFHX3 and histone PTMs.

We agree that, alone, the current data does not make any claim for ZFHX3 being crucial for promoter to be active. Our data clearly suggests that a vast majority of ZFHX3 genomic binding in the SCN was observed at active promoters marked by H3K4me3 and H3K27ac and potentially regulating gene transcription.

Based on a enrichment of ARNT domains next to K4Me3 and K27ac PTMs, the authors propose a model where the core-clock TFs and ZFHX3 interact. If the authors develop other assays beyond just predictions to test their hypothesis, it would strengthen the argument for role in circadian transcription in the SCN. It would be important in this context to perform a ChIP-seq experiment for ZFHX3 in the knockout animal (described from Figure 2 onwards) to eliminate the possibility of non-specific enrichment of signal from "open chromatin'. Alternatively, a ChIPseq analysis for BMAL1 or CLOCK could also strengthen this argument to identify the sites co-occupied by ZFHX3 and core-clock TFs.

(4a) We agree that follow-up experiments such as BMAL1/CLOCK ChIPseq suggested by the reviewer will further confirm the proposed interaction of ZFHX3 with core-clock TFs. However, this is beyond the scope of the current study. 

(4b) Again, conducting complementary ChIPseq in ZFHX3 knockout mice will strengthen the findings, but conducting TF-ChIPseq in a specific brain tissue such as the SCN (unlike peripheral tissues such as liver) does not only warrant use of multiple animals per sample but is also technically challenging and time-consuming to ensure specificity of the sample. For these reasons, datasets such as ours on the SCN are uncommon. Furthermore, in this particular context, we are certain that, based on current dataset, the ZFHX3 peaks (narrow) we observed were well-defined and met the specified statistical criteria mitigating any risk of signal arising from non-specific enrichment from open-chromatin regions.

Next, they compared locomotor activity rhythms in floxed mice with or without tamoxifen treatment. As reported before in Wilcox et al 2017, the loss of ZFHX3 led to a shorter free running period and reduced amplitude and earlier onset of activity. Overall, the behavioral data in Figure 2 and supplementary figure 2 has been reported before and are not novel.

(5) We recognise that a detailed circadian behavior assessment from adult mice lacking ZFHX3 has been conducted previously by Nolan lab (Wilcox et al; 2017). In the current study, however, we used a separate cohort of mice, to focus on the behavioral advance noted in 24-h LD cycle and generated a more refined assessment. Importantly, these mice were also used for transcriptomic studies as detailed in Figure 3, which we consider to be a positive feature of our experimental design: behavior and molecular analyses were performed on the same animals.

Next, the authors performed RNAseq at 4hr intervals on wildtype and knockout animals maintained in light/dark cycles to determine the impact of loss of ZFHX3. Overall transcriptomic analysis indicated changes in gene expression in nearly 36% of expressed genes, with nearly half being upregulated while an equal fraction was downregulated. Pathways affected included mostly neureopeptide neurotransmitter pathways. Surprisingly, there was no correlation between the direction in change in expression and TF binding since nearly all the sites were bound by ZFHX3 and the active histone PTMs. The ChIP-seq experiment for ZFHX3 in the UBC-Cre+Tam mice again could help resolve the real targets of ZFHX3 and the transcriptional state in knockout animals.

(6) We agree with the reviewer that most of the differentially expressed genes showed ZFHX3 binding at active promoter sites. That said, the current dataset is in line with recently published ZFHX3-CHIPseq data by Baca et al; 2024 [PMID: 38412861] in human neural stem cells and Hu et al; 2024 [PMID: 38871709] in human prostate cancer cells that clearly suggests ZFHX3 binds at active promoters and act as chromatin remodellers/mediators that modulate gene transcription depending on the accessory TFs assembled at target genes. Therefore, finding no correlation in the direction of change in expression is not striking. 

To determine the fraction of rhythmic transcripts, Using dryR, the authors categorise the rhythmic transcriptome into modules that include genes that lose rhythmicity in the KO, gain rhythmicity in the KO or remain unaffected or partially affected. The analysis indicates that a large fraction of the rhythmic transcriptome is affected in the KO model. However, among core-clock genes only Bmal1 expression is affected showing a complete loss of rhythm. The authors state a decrease in Clock mRNA expression (line 294) but the panel figure 4A does not show this data. Instead it depicts the loss in Avp expression - {{ misstated in line 321 ( we noted severe loss in 24-h rhythm for crucial SCN neuropeptides such as Avp (Fig. 3a).}}

(7a) Indeed, among the core-clock genes rhythmic expression is lost after ZFHX3 knockout only for Bmal1. However, given the mice were rhythmic (as assessed by wheel-running activity) in LD conditions, the observed 24-h gene expression rhythm in the majority of core-clock genes (Pers and Crys) is consistent with behavior data, and suggests towards an altered molecular clock with plausible scenarios as explained at line 439. That said, the unique and well-defined changes (amplitude and phase) observed as demonstrated in Figure 5 highlights a model in which ZFHX3 exerts differential control, for example in case of Per2 noted advance in molecular rhythm (~2-h), but no such change in Cry, presents an opportunity to delineate further the regulation of TTFL genes.

(7b) Line 294 revised as – “Bmal1 demonstrating a complete loss of 24-h rhythm (Fig. 4A), and its counterpart Clock mRNA showing overall reduced expression levels (Supplementary Table 3)”.

7c) Line 321 is referring to loss of Avp expression and the typo has been corrected from “Figure 3a to 4a”. Thank you. 

However, core-clock genes such as Pers and Crys show minor or no change in expression patterns while Per2 and Per3 show a ~2hr phase advance. While these could only weakly account for the behavioral phase advance, the authors used TimeTeller to assess circadian phase in wildtype and ZFHX3 deficient mice. This approach clearly indicated that while the clock is not disrupted in the knockout animals, the phase advance can be correctly predicted from a network of gene expression patterns.

Strengths:

The authors use a multiomic strategy in order to reveal the role of the ZFHX3 transcription factor with a combination of TF and histone PTM ChIPseq, time-resolved RNAseq from wildtype and knockout mice and modeling the transcriptomic data using TimeTeller. The RNAseq experiments are nicely controlled and the analysis of the data indicates a clear impact on gene-expression levels in the knockout mice and the presence of a regulatory network that could underlie the advanced activity onset behavior.

Weaknesses:

It is not clear whether ZFHX3 has a direct role in any of the processes and seems to be a general factor that marks H3K4me3 and K27ac marked chromatin. Why it would specifically impact the core-clock TTFL clock gene expression or indeed daily gene expression rhythms is not clear either. Details for treatment of different ChIP samples (ZFHX3 and histone PTM ChIPs) on data normalization for analysis are needed. The loss of complete rhythmicity of Avp and other neuropeptides or indeed other TFs could instead account for the transcriptional deregulation noted in the knockout mice.

(8) We thank the reviewer for the constructive feedback.  The current data suggests ZFHX3 acts as a mediating factor, occupying targeted active promoter sites and regulating gene expression by partnering with other key TFs in the SCN. Please see point 6 for clarification. The binding sites of ZFHX3 clearly showed enrichment for E-box(CACGTG) motif bound by CLOCK/BMAL1 along with binding sites for key SCN-specific TFs such as RFX (please see Supplementary Fig1). Our data thereby shows that it affects both core-clock and clock output genes (at varied levels) thereby exercising a pervasive control over the SCN transcriptome.

For treatment of ChIP samples please see point 3. We followed ENCODE guidelines strictly. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

- The early activity onset associated with a short photoperiod is a phenotype found in mice with a perturbed function of the SCN like Per2 mutant (PMID: 17218255), or Clock KO (PMID: 22431615). Such disruption of the SCN function also leads to a faster synchronization to day feeding (PMID: 23824542) or jetlag (PMID: 25063847; PMID: 24092737). Therefore, authors should study the synchronizing function of these mice to day feeding and/or jetlag.

(9) Please see our response to point 1.

- The description of the negative controls needs clarification. While the "Method" suggests that both Cre- and Cre+ mice are treated with Tamoxifen, the text rather suggest that the controls are Cre- and Cre+ animals non-treated by Tamoxifen. Because of the potential effect of Tamoxifen on gene expression, Cre- treated animals are a required control.

(10) We thank the reviewer. As detailed in Methods, both Cre- and Cre+ mice were treated with Tamoxifen and compared. The text had been revised at line 212. In addition to this, another genetic control (-Tamoxifen) was also used (Figure 2 and 3).

- On line 486, authors wrote "It is important to note that although in the present study we used adult-specific Zfhx3 null mutants resulting in global loss of ZFHX3, the effects observed both at molecular and behavioural levels are independent of its functional role(s) in other tissues." On what evidence is this statement based? Using global KO rather suggest a potential role of other tissues.

(11) We agree with the reviewer, but at line 486 we refer to the effects observed at circadian behavior and daily gene expression in the SCN to be independent of pleiotropic roles of ZFHX3 such as involvement in angiogenesis, spinocerebellar ataxia etc. We have revised the text.

Reviewer #2 (Recommendations for the authors):

It is not clear whether the behavioral experiments presented in this study were performed on a new set of animals - different from the cohort used in the Wilcox et al 2017 paper. For example, the proportion of total activity graphed in Figure 2C look strikingly similar to activity counts in Figure 3A in the prior publication (doi: 10.1177/0748730417722631)- down to the small burst in activity after ZT20 in the control (-Tam) group.

(12) The behavioral experiments presented in this study were performed on a completely new cohort of mice to those used in Wilcox et al.; 2017. The mice used for behavioral assessment. In the current study were later used for molecular experiments. Please see point 5.

Information on ChIP-seq such as read length, PE or SE seq, number of reads/replicate/condition/sample is missing. Versions of the softwares used should be indicated if known.

(13) The details are added as:

(13a) “Briefly, SCN punches were pooled from 80 mice at each. designated times (ZT3, ZT15) corresponding to one biological replicate per timepoint” at line 567.

(13b) “24 ug sheared chromatin sample collected from each time point (ZT3, ZT15)” at line 571.

(13c) “75-bp single end sequencing : 30 million reads/sample” at line 577.  

(13d) “At line 584 – MACS algorithm v2.1.0 added”

Versions of other softwares used were already mentioned.

eLife Assessment

This work presents a useful resource combining scRNA-seq and spatial transcriptomics studies to map mouse pre-clinical models of colorectal cancer, identifying distinct cellular programs and microenvironments that could enhance patient stratification and therapeutic approaches in colorectal cancer. While the novelty of the biological findings remains limited and incompletely supported by the evidence provided in the manuscript, the data were collected and analyzed using a validated methodology that will be of interest to the community in future studies.

Reviewer #1 (Public review):

Summary:

The authors conducted a spatial analysis of dysplastic colon tissue using the Slide-seq method. Their main objective is to build a detailed spatial atlas that identifies distinct cellular programs and microenvironments within dysplastic lesions. Next, they correlated this observation with clinical outcomes in human colorectal cancer.

Strengths:

The work is a good example of utilising spatial methods to study different tumour models. The authors identified a unique stem cell program to understand tumours gently and improve patient stratification strategies.

Weaknesses:

However, the study's predominantly descriptive nature is a significant limitation. Although the spatial maps and correlations between cell states are interesting observations, the lack of functional validation-primarily through experiments in mouse models-weakens the causal inferences regarding the roles these cellular programs play in tumour progression and therapy resistance.

The authors also missed an opportunity to link the mutational status of malignant cells with the cellular neighbourhoods.

Overall, the study contributes to profiling the dysplastic colon landscape. The methodologies and data will benefit the research community, but further functional validation is crucial to validate the biological and clinical implications of the described cellular interactions.

Reviewer #2 (Public review):

In their study, Avraham-Davidi et al. combined scRNA-seq and spatial mapping studies to profile two preclinical mouse models of colorectal cancer: Apcfl/fl VilincreERT2 (AV) and Apcfl/fl LSL-KrasG12D Trp53fl/fl Rosa26LSL-tdTomato/+ VillinCreERT2 (AKPV). In the first part of the manuscript, the authors describe the analysis of the normal colon and dysplastic lesions induced in these models following tamoxifen injection. They highlight broad variations in immune and stromal cell composition within dysplastic lesions, emphasizing the infiltration of monocytes and granulocytes, the accumulation of IL-17+gdT cells, and the presence of a distinct group of endothelial cells. A major focus of the study is the remodeling of the epithelial compartment, where the most significant changes are observed. Using non-negative matrix factorization, the authors identify molecular programs of epithelial cell functions, emphasizing stemness, Wnt signaling, angiogenesis, and inflammation as major features associated with dysplastic cells. They conclude that findings from scRNA-seq analyses in mouse models are transposable to human CRC. In the second part of the manuscript, the authors aim to provide the spatial context for their scRNA-seq findings using Slide-seq and TACCO. They demonstrate that dysplastic lesions are disorganized and contain tumor-specific regions, which contextualize the spatial proximity between specific cell states and gene programs. Finally, they claim that these spatial organizations are conserved in human tumors and associate region-based gene signatures with patient outcomes in public datasets. Overall, the data were collected and analyzed using solid and validated methodology to offer a useful resource to the community.

Main comments:

(1) Clarity<br /> The manuscript would benefit from a substantial reorganization to improve clarity and accessibility for a broad readership. The text could be shortened and the number of figure panels reduced to emphasize the novel contributions of this work while minimizing extensive discussions on general and expected findings, such as tissue disorganization in dysplastic lesions. Additionally, figure panels are not consistently introduced in the correct order, and some are not discussed at all (e.g., Figure S1D; Figure 3C is introduced before Figure 3A; several panels in Figure 4 are not discussed). The annotation of scRNA-seq cell states is insufficiently explained, with no corresponding information about associated genes provided in the figures or tables. Multiple annotations are used to describe cell groups (e.g., TKN01 = γδ T and CD8 T, TKN05 = γδT_IL17+), but these are not jointly accessible in the figures, making the manuscript challenging to follow. It is also not clear what is the respective value of the two mouse models and time points of tissue collection in the analysis.

(2) Novelty<br /> While the study is of interest, it does not present major findings that significantly advance the field or motivate new directions and hypotheses. Many conclusions related to tissue composition and patient outcomes, such as the epithelial programs of Wnt signaling, angiogenesis, and stem cells, are well-established and not particularly novel. Greater exploration of the scRNA-seq data beyond cell type composition could enhance the novelty of the findings. For instance, several tumor microenvironment clusters uniquely detected in dysplastic lesions (e.g., Mono2, Mono3, Gran01, Gran02) are identified, but no further investigation is conducted to understand their biological programs, such as applying nNMF as was done for epithelial cells. Additional efforts to explore precise tissue localization and cellular interactions within tissue niches would provide deeper insights and go beyond the limited analyses currently displayed in the manuscript.

(3) Validation<br /> Several statements made by the authors are insufficiently supported by the data presented in the manuscript and should be nuanced in the absence of proper validation. For example:<br /> (a) RNA velocity analyses: The conclusions drawn from these analyses are speculative and need further support.<br /> (b) Annotations of epithelial clusters as dysplastic: These annotations could have been validated through morphological analyses and staining on FFPE slides.<br /> (c) Conservation of mouse epithelial programs in human tumors: The data in Figure S5B does not convincingly demonstrate the enrichment of stem cell program 16 in human samples. This should be more explicitly stated in the text, given the emphasis placed on this program by the authors.<br /> (d) Figure S6E: Cluster Epi06 is significantly overrepresented in spatial data compared to scRNA-seq, yet the authors claim that cell type composition is largely recapitulated without further discussion, which reduces confidence in other conclusions drawn.<br /> Furthermore, stronger validation of key dysplastic regions (regions 6, 8, and 11) in mouse and human tissues using antibody-based imaging with markers identified in the analyses would have considerably strengthened the study. Such validation would better contextualize the distribution, composition, and relative abundance of these regions within human tumors, increasing the significance of the findings and aiding the generation of new pathophysiological hypotheses.

Author response:

We thank the reviewers for their appreciation of our work and the recommendations to improve the manuscript. We have included a point-by-point response below. To summarize, for revision we plan to:

• Clarify the manuscript to improve readability and coherence,

• Ensure that all figures are thoroughly discussed in the text,

• Tone down biological claims based on RNA velocity where applicable.

While we agree with the reviewer that functional validation and/or spatial proteomics data accompanying this study could provide additional insights and broader contextualization, this is unfortunately beyond the scope of the study.

Reviewer #1 (Public review):

Summary:

The authors conducted a spatial analysis of dysplastic colon tissue using the Slide-seq method. Their main objective is to build a detailed spatial atlas that identifies distinct cellular programs and microenvironments within dysplastic lesions. Next, they correlated this observation with clinical outcomes in human colorectal cancer.

Strengths:

The work is a good example of utilising spatial methods to study different tumour models. The authors identified a unique stem cell program to understand tumours gently and improve patient stratification strategies.

Weaknesses:

However, the study's predominantly descriptive nature is a significant limitation. Although the spatial maps and correlations between cell states are interesting observations, the lack of functional validation-primarily through experiments in mouse models-weakens the causal inferences regarding the roles these cellular programs play in tumour progression and therapy resistance.

We thank the reviewer for this comment. Indeed, functional validation to pin down causal dependencies and a more thorough investigation of tumor progression and therapy resistance both in mouse model as well as human patients and/or patient derived samples would broaden the insights to be gained from this work. Unfortunately, this is beyond the scope of this study.

The authors also missed an opportunity to link the mutational status of malignant cells with the cellular neighbourhoods.

The data reported in this study only contains spatial data for one mouse model (AV). As spatial data for the other model (AKPV) is missing, it is not possible to link the mutational type of the model with the cellular neighborhoods. We did investigate whether there is extra "somatic" mutational heterogeneity in the AV data, both regarding single nucleotide variations (SNVs) and copy number variations (CNVs). But at the time when the mice were sacrificed (after 3 weeks) there was no significant mutational heterogeneity discoverable.

Overall, the study contributes to profiling the dysplastic colon landscape. The methodologies and data will benefit the research community, but further functional validation is crucial to validate the biological and clinical implications of the described cellular interactions.

Reviewer #2 (Public review):

In their study, Avraham-Davidi et al. combined scRNA-seq and spatial mapping studies to profile two preclinical mouse models of colorectal cancer: Apcfl/fl VilincreERT2 (AV) and Apcfl/fl LSL-KrasG12D Trp53fl/fl Rosa26LSL-tdTomato/+ VillinCreERT2 (AKPV). In the first part of the manuscript, the authors describe the analysis of the normal colon and dysplastic lesions induced in these models following tamoxifen injection. They highlight broad variations in immune and stromal cell composition within dysplastic lesions, emphasizing the infiltration of monocytes and granulocytes, the accumulation of IL-17+gdT cells, and the presence of a distinct group of endothelial cells. A major focus of the study is the remodeling of the epithelial compartment, where the most significant changes are observed. Using non-negative matrix factorization, the authors identify molecular programs of epithelial cell functions, emphasizing stemness, Wnt signaling, angiogenesis, and inflammation as major features associated with dysplastic cells. They conclude that findings from scRNA-seq analyses in mouse models are transposable to human CRC. In the second part of the manuscript, the authors aim to provide the spatial context for their scRNA-seq findings using Slide-seq and TACCO. They demonstrate that dysplastic lesions are disorganized and contain tumor-specific regions, which contextualize the spatial proximity between specific cell states and gene programs. Finally, they claim that these spatial organizations are conserved in human tumors and associate region-based gene signatures with patient outcomes in public datasets. Overall, the data were collected and analyzed using solid and validated methodology to offer a useful resource to the community.

Main comments:

(1) Clarity

The manuscript would benefit from a substantial reorganization to improve clarity and accessibility for a broad readership. The text could be shortened and the number of figure panels reduced to emphasize the novel contributions of this work while minimizing extensive discussions on general and expected findings, such as tissue disorganization in dysplastic lesions. Additionally, figure panels are not consistently introduced in the correct order, and some are not discussed at all (e.g., Figure S1D; Figure 3C is introduced before Figure 3A; several panels in Figure 4 are not discussed). The annotation of scRNA-seq cell states is insufficiently explained, with no corresponding information about associated genes provided in the figures or tables. Multiple annotations are used to describe cell groups (e.g., TKN01 = γδ T and CD8 T, TKN05 = γδT_IL17+), but these are not jointly accessible in the figures, making the manuscript challenging to follow. It is also not clear what is the respective value of the two mouse models and time points of tissue collection in the analysis.

We thank the reviewer for this suggestion. For the revision we plan to clarify the manuscript to improve readability and coherence in text and figures, and expand on the cell type nomenclature.

(2) Novelty

While the study is of interest, it does not present major findings that significantly advance the field or motivate new directions and hypotheses. Many conclusions related to tissue composition and patient outcomes, such as the epithelial programs of Wnt signaling, angiogenesis, and stem cells, are well-established and not particularly novel. Greater exploration of the scRNA-seq data beyond cell type composition could enhance the novelty of the findings. For instance, several tumor microenvironment clusters uniquely detected in dysplastic lesions (e.g., Mono2, Mono3, Gran01, Gran02) are identified, but no further investigation is conducted to understand their biological programs, such as applying nNMF as was done for epithelial cells. Additional efforts to explore precise tissue localization and cellular interactions within tissue niches would provide deeper insights and go beyond the limited analyses currently displayed in the manuscript.

We thank the reviewer for this comment. Our study aimed to spatially characterize the tumor microenvironment, with scRNA-seq analysis serving to support this spatial characterization.<br /> Due to technical limitations—such as the number of samples and the limited capture efficiency of Slide-seq—the resolution of immune cell identification in our spatial analysis is constrained. Additionally, while immune and stromal cells formed distinct clusters, epithelial cells exhibited a continuum that was better captured using nNMF.

Lastly, our manuscript provides a general characterization of monocyte and granulocyte populations in scRNA-seq (line 142) and their spatial microenvironments (line 390). We believe that additional analyses of these populations would be beyond the scope of this study and could place an unnecessary burden on the reader. Instead, we suggest that such analyses be explored in future studies.

We remark that we analyzed tissue localization for two entirely different spatial transcriptomics assays (Slide-seq and Cartana) to the resolution of cell types and programs, which was feasible within the constraints of the sparsity and gene panel and sample size in the experiments. A path to further increase the resolution of investigation in this dataset is to include other datasets, e.g. by the emerging transformer-based spatial transcriptomics integration methods, which unfortunately is outside the scope of the current study.

We also remark that the current manuscript already includes an investigation of cellular interactions within tissue niches based on COMMOT (Fig 4k, Fig S8i, Supp Item 4).

(3) Validation

Several statements made by the authors are insufficiently supported by the data presented in the manuscript and should be nuanced in the absence of proper validation. For example:<br /> (a) RNA velocity analyses: The conclusions drawn from these analyses are speculative and need further support.

We thank the reviewer for this comment. We will clarify that our conclusions from the RNA velocity analysis need further support by experimental validation, which is out of the scope of the study.

(b) Annotations of epithelial clusters as dysplastic: These annotations could have been validated through morphological analyses and staining on FFPE slides.

We thank the reviewer for this comment. While this could have been a possible approach, our study primarily relies on scRNA-seq, which does not preserve tissue morphology, and Slide-seq of fresh tissue, where such an analysis is particularly challenging.

(c) Conservation of mouse epithelial programs in human tumors: The data in Figure S5B does not convincingly demonstrate the enrichment of stem cell program 16 in human samples. This should be more explicitly stated in the text, given the emphasis placed on this program by the authors.

We thank the reviewer for pointing this out. Indeed, Figure S5B does not demonstrate the program 16 enrichment in human samples. We will clarify this in the manuscript.

(d) Figure S6E: Cluster Epi06 is significantly overrepresented in spatial data compared to scRNA-seq, yet the authors claim that cell type composition is largely recapitulated without further discussion, which reduces confidence in other conclusions drawn.

We thank the reviewer for this remark. Indeed, Epi06 was a cluster which drew our attention during early analyses for its mixed expression profiles with contributions of vastly different cell types. We concluded that this is best explained by doublets and excluded it from further analysis. In the current manuscript we only briefly hinted at this in figure legend 2A ("Cluster Epi06: doublets (not called by Scrublet)"), and we will expand on this in the revised manuscript. The observation that this cluster is significantly overrepresented in the annotation of the spatial data is not surprising in this context as this annotation comes from the decomposition of compositional data which contains contributions of multiple cells per Slide-seq bead which are structurally very similar to doublets. We will add this point as well to the revised manuscript.

Furthermore, stronger validation of key dysplastic regions (regions 6, 8, and 11) in mouse and human tissues using antibody-based imaging with markers identified in the analyses would have considerably strengthened the study. Such validation would better contextualize the distribution, composition, and relative abundance of these regions within human tumors, increasing the significance of the findings and aiding the generation of new pathophysiological hypotheses.

We agree with the reviewer with their assessment that validation by antibody-based imaging (or other spatial proteomics data) would have been useful follow-up experiments to the experiments and results presented in our manuscript, yet these are beyond the scope of the current study.

eLife Assessment

This is an important study linking olfactory bulb activity not only to sniffing parameters but also to movement and place. The evidence for odor sampling is mostly solid, but the analysis supporting the potentially exciting result on the encoding of place is currently incomplete.

Reviewer #1 (Public review):

In this manuscript, Sterrett et al. assess whether and how the olfactory system may integrate odor-driven activity with contextual, egocentric variables such as instantaneous location in space and active odor sampling. To address this, they co-record respiration and the spiking activity of principal output neurons of the mouse olfactory bulb (OB), while mice explore a small arena in the absence of any explicit reward or task structure. The authors find that mice exploring the arena breathe in bouts, switching between discrete states of particular breathing rates that persist over varying time scales (seconds to minutes). This state-like activity is also apparent in the OB population activity. Zooming into the activity of individual OB neurons, the authors show that OB activity in this setting is primarily modulated by respiration. In general, while the response times of individual neurons remain tightly locked to the inhalation onset, the overall response amplitude is modulated by the instantaneous sniff frequency. The authors further suggest that a subset of OB neurons appear to show place-selectivity, in a manner that is not explained simply by respiratory or olfactory variables.

Overall this work addresses an important question regarding the basic temporal structuring of odor sampling behavior and activity patterns in the mouse OB. A good understanding of these features is essential to further investigate how stimulus and/or task-driven activity may add on top of this already ongoing modulation. The authors do a commendable job of analyzing the behavior and neuronal activity using a variety of analysis methods. However, in its current form, the results presented are high-level summary figures that are largely comparative (role of parameter A vs B) and hard to assess quantitatively (how well does a given parameter/model explain the responses to begin with). This makes it hard to build a clear model of the underlying mechanisms and to evaluate alternative hypotheses. These concerns can largely be addressed by some additional analyses and by presenting more intermediate-stage output of their existing analyses. In addition, the authors report that a small fraction of OB neurons show spatially selective firing patterns, akin to those observed in the Hippocampus. While this is a very exciting possibility, in my opinion, the data and analysis presented currently are not sufficient to conclude this and additional experiments would be required to test this rigorously.

Major concerns:

A) Regarding the claim about Spatial selectivity in OB neuron responses:

i) From the data presented, it is very hard to assess whether a simple modulation of sniff rate, selectively in some parts of the arena can explain apparent spatial selectivity. The authors attempt to address this concern with Figure 8 - Figure Supplement 1, but the presented combinatorial color maps are hard to interpret. A simpler format would be to show the sniff-aligned raster of the given unit in question along with a heatmap (location distribution) of the actual sniff rates in the arena (not the behavioral states).

If the authors allow the mice to explore the arena over large periods, such that the sniff rates are relatively uniform in space, are the place fields still apparent? A complementary control is to compare responses in the 'place field' with other parts in the arena with comparable sniff rate distributions.

ii) The analysis shown in Figure 8 suggests that sniff parameters are the main predictors of individual neuron responses. The authors point out that there is however a small, but significant fraction of cells that are better predicted by place than by the sniff parameters. It would be useful to provide more raw data to get a better sense of what distinguishes these cells from the rest. Are spatially selective cells typically less sniff-aligned on average? Do they tend to be less or more frequency-modulated?

iii) The authors compare the decoding performance of OB and hippocampal neurons. While it appears space can indeed be decoded from OB neurons, it would be useful to know how the performance scales with the number of neurons and number of traversals in the arena in the two brain regions. Further, the authors should provide some analysis of the robustness of these apparent 'place fields' within a session.

iv) The floor rotation control is underwhelming. First, the arena is quite small and one would generally expect this to impact much more so the 'place fields' that are biased towards the corners than in the center. Second, olfactory cues on the walls may be as important - why did the authors not rotate the entire arena?

Considering the possibility that floor rotation rules out trivial olfactory explanations, what would happen if the authors rotated the entire arena? If these are truly place fields, then one should expect that while they are robust to floor rotation, they should reformat if the distal cues change. Without these additional analyses, I find it hard to conclude the presence of spatial selectivity in the OB.

Moderate concerns:

B) Regarding the lack of state-like structure during head-fixation:

While it is clear that overall sniff rates are lower and that mice do not typically sniff at peak rates during head-fixation, it is unclear if the transitions in breathing rhythm are necessarily less structured, and further whether this can be attributed to head-fixation alone. For example, if the mice are head-fixed but in a floating-platform arena or VR that is non-static - the sniffing distributions may change dramatically.

i) The breathing patterns shown in Figure 1E, in particular during the second head-fixation phase do not appear fundamentally different from the freely moving stretch (20-30 minute window). If one subsamples the free-moving data to match overall sniff distributions, will the long-timescale autocorrelation still be more apparent in freely moving stretches than in the head-fixation periods?

ii) Are the mice on a running wheel? How does the overall distribution of sniff rates and temporal structure change if the mice are head-fixed but simply allowed to run?

Minor concerns:

C) Regarding the parsing of breathing and movement into 3 distinct behavioral states:<br /> The authors show breathing patterns of freely exploring mice are temporally structured with extended bouts of sniffing at select rates. They use a HMM model to show that this structure can be captured by a 3 state-model wherein each state can be thought of as a joint distribution of movement and sniff rate. While the approach is interesting and the data are well presented, I have some minor concerns regarding the exact interpretation.

i) While the relationship between movement and sniffing is indeed non-trivial, it is unclear if the statelike partitioning requires the incorporation of the movement variable at all in the HMM model. The state-like patterns are also apparent if one focuses exclusively on the instantaneous sniff rate while ignoring movement velocities (Figure 1 - Figure Supplement 1) or the inferred HMM states (Figure 1E). Have the authors tried modeling the breathing activity alone using an HMM with each state just being a biased distribution of sniff rates, from which the instantaneous sniff rate is drawn? Will the authors' conclusions be fundamentally different from such a model?

ii) While it is clear that there are at least 2 distinct states a) resting (mice are generally uninterested and sniff at 2-3 Hz) and b) exploration (mice are interested in their local environment and sniff rapidly). It is hard to assess whether there is indeed a third distinct and behaviorally interpretable state that the authors call grooming or are there simply intervening periods where it is unclear what's driving the variability in sniff rates - change in movement speed, moderate curiosity, boredom, etc. From the movement velocities shown in the supplement (Figure 1 - Figure Supplement 1), it appears that the movement speed during this 'grooming' state is significantly higher than at rest. It is not obvious why a mouse should move around more while grooming. It would help if the authors provide supporting data, perhaps from behavioral pose analysis to better justify the classification of this state as grooming or alternatively choose a different name to avoid confusion.

iii) Insufficient analysis of state transition matrices: The authors do not show the transition matrices for individual sessions and/or mice. This limits what one can learn about the behavior from the 3 state modeling of breathing states. Do individual mice have stereotypical transition patterns across sessions? How well does the model perform: can one predict the expected sniff rate in one part of the session from knowing sniff patterns in another part of the session?

D) Regarding the dependence of individual neuron responses on sniff and movement parameters:

i) Could the authors report the relative proportions of sniff frequency insensitive vs. frequency sensitive neurons in their data?

ii) Could some of the striking frequency modulation the authors show in Figure 3A result from the fact that mice selectively sniffed at high or low rates in different parts of the arena? While it is unlikely that all of the modulation the authors see results from the location/presence of trace odors in different parts of the arena, it would be informative to perform the same analysis on the data recorded during head-fixation where its external environment is less variable.

iii) Comparison of SnF latency profiles between head-fixed and freely moving conditions:<br /> The SnF latency profiles of a given OB neuron appear strikingly similar during head-fixed and freely moving conditions. It would be useful if the authors could explicitly quantify this.

iv) Comparison of SnF frequency profiles between head-fixed and freely moving conditions: The authors comment that SnF frequency profiles are different across the head-fixed versus freely moving conditions and that they do not observe the 3 distinct clusters present in the freely moving state in their head-fixed data. If true, this is an interesting observation. Together with the observation of relatively similar SnF latency profiles in both head-fixed and freely moving conditions, this implies that sniff frequency dependence is selectively enhanced during free-moving behavior perhaps through a top-down signal.

However, this is hard to conclude from the current data as the overall distribution of sniff rates is very different in the two conditions, with a clear underrepresentation of high-frequency sniffs in the head-fixed periods. To enable a fair comparison, the authors should undersample the sniffs in the freely moving period and compare sniff fields constructed from frequency-matched distributions.

v) The authors suggest that the 2 types of SnF latency profiles may putatively map onto tufted and mitral cells. While this is an interesting possibility, it would be nice to support the claim with auxiliary analysis of other features such as recording depth, baseline firing rates, spike shapes, etc that indicate that these are indeed two different cell types.

Reviewer #2 (Public review):

In this study, the authors investigate the structure of breathing rhythms in freely moving mice during exploratory behaviour in the absence of explicit cues or tasks. Additionally, they link behavioural states, derived from sniffing frequency and speed movement data, to the neural activity recorded in the olfactory bulb (OB). To further characterize OB neuronal responses, the authors introduce the concept of "sniff fields" which consider the joint distribution of sniff frequency and the latency from inhalation. Lastly, they explore how OB neurons encode spatial information, and they compare this finding with previously known spatially encoding cells in the hippocampus.

The authors successfully establish that breathing in freely moving mice is structured even in the absence of explicit olfactory cues. By simultaneously recording sniffing and movement data, they find that this structure is associated with movement in a non-linear manner and can be modelled using a Hidden Markov Model (HMM). Interestingly, they demonstrate that neuronal activity in the OB tracks this behavioural structure by showing that HMM states can effectively cluster the neural data. Additionally, they describe OB activity using sniff fields, advancing our understanding of how individual neurons encode sniffing properties such as frequency and phase. Furthermore, they report unprecedented findings showing that some OB neurons encode place independently of the sniffing field contribution. Overall, the authors provide valuable insights regarding the contribution of different behavioural variables to OB activity.

However, some of the conclusions presented by the authors are not fully supported by the data provided. Quantitative analysis and statistical tests are missing from the description of the breathing structure. Regarding spatial encoding, the authors claim in the abstract that "at the population level, a mouse's location can be decoded from olfactory bulb with similar accuracy to hippocampus". However, they show that place was significantly decoded in only 18/31 sessions from OB activity, and in 12/13 sessions from hippocampal activity. No further comparison of decoding accuracy between OB and HPC is provided. Moreover, it is unclear whether place contributes independently of movement, which was previously shown in this study to influence neuronal activity.

Additionally, there is a lack of methodological detail regarding the experimental procedures, which could affect the interpretation of the data. Specifically, information is missing on aspects such as head-fixed conditions, the number of mice used per experiment, and the number of sessions per mouse.

Studying mice behaviour in more naturalistic conditions, without explicit tasks, is a very interesting approach that provides new insights into the structure of sniffing and its neuronal representation. The fact that some OB neurons encode spatial information is highly relevant beyond the field of olfaction, even though this information was not as accessible as in the hippocampus. I believe the manuscript would benefit from a revision to ensure the text aligns more closely with the data presented in the figures.

Author response:

We thank the editor and reviewers for recognizing the value of studying neural dynamics and behavior in naturalistic, task-free conditions and the importance of linking olfactory bulb activity to movement and place.  We appreciate the suggestions for analyses and edits to further quantify these relationships and clarify our interpretation.

The primary sticking point regards our result that olfactory bulb neurons are selective for place:

“analysis supporting the potentially exciting result on the encoding of place is currently incomplete”

In this paper, we report evidence for spatial selectivity in the olfactory bulb, make relative comparisons with canonical “place cells” in the hippocampus, and control for alternative hypotheses such as odor- or behavior-driven sources, to motivate future experiments which can more precisely identify the mechanistic basis of these responses. Throughout the reviews, our result on the correlation of OB activity with place is not questioned, but rather whether we can better determine how much behavior or odor explain this result. Regarding the concern about behavior, we are confident that the spatial non-uniformities of breathing rhythms do not explain OB spatial selectivity based on the analyses included in the paper. We thank the reviewers for suggestions of additional analyses with which we can further test this claim and will incorporate several, as we will detail below.

Regarding the points about odor, indeed we do not claim that we have entirely ruled out odors as an explanation of place selectivity in the bulb. Rather, our claim is that our analyses show that scent marks on the floor, the most obvious olfactory place cue, cannot fully explain place selectivity.  We acknowledge that our experiments do not exclude the possibility that other odors in the environment may also contribute. Odors are invisible and difficult to measure, and the odor sensitivity of rodents vastly outstrips that of any device known to humanity. Indeed, no study of which we are aware can fully rule out odor as a cue to the animal’s internal model of place. However, encoding of place, even if explained by odor, is still encoding of place. We will clarify our interpretation of the data, and we thank the reviewers for proposing ideas for further analysis, some of which we are implementing. However, experiments such as effects of distal cues on spatially selective olfactory bulb neurons are beyond the scope of this paper.

We will further test whether neurons in the olfactory bulb are spatially selective by reporting additional statistical analyses including:

- More completely quantifying the spatial distribution of sniffing patterns (visualized in Figure 8 - Sup 1) by plotting sniff-frequency distributions across locations in the arena.

- Demonstrating independent contribution of place over speed in GLMs

- Characterizing the temporal stability of spatially selective cells across a session (1st half vs second half)

- reporting mean decoding errors for olfactory bulb and hippocampal decoders (visualized in Fig 7C)

We will add to the analyses of behavioral state models by:

- Comparing the performance of hidden Markov models fit to breathing frequency alone with those fit to breathing frequency and movement speed

- Quantifying individual differences in state-transition matrices

Further, we address the question around the use of “grooming” as a descriptor of the intermediate sniff frequency state. We used the term ‘grooming’ based on extensive video observation. During this state, ‘Speed’ is significantly non-zero because we defined speed as the movement of the head keypoint which moves substantially during grooming. We will make this point more explicit in the figures and text, and we will provide additional video documentation of these and the other behavioral states.

Lastly, we will further discuss the fact stated in the first paragraph of the Results section that mice are placed in “head-fixation on a stationary platform” and thus inhibited from running. While different breathing states than those observed in our stationary platform may occur during head-fixation with a treadmill, we believe the differences between head-fixed running and free moving running are beyond the scope of this paper. Nevertheless, it’s an important point that we will more explicitly discuss in our revision.

We appreciate these constructive comments and hope these additional analyses and textual edits will help clarify our interpretations and motivate future experiments to further test and refine them.

eLife Assessment

This valuable manuscript presents a potentially novel mechanism by which the phospholipid scramblase, PLSCR1, defends against influenza A virus infection. The paper was based on solid findings involving knockout and lung-specific over-expressing Plscr1 mice, airway tissue expression, and mechanistic studies to show Plscr1 enhances type III interferon-mediated viral clearance. The study is extensive and overall well performed.

Reviewer #1 (Public review):

This manuscript by Yang et al. presents a potentially novel mechanism by which Plscr1 defends against influenza virus infection. Using a global knockout (KO) and a tissue-specific overexpression mouse model, the authors demonstrate that Plscr1-KO mice exhibit increased susceptibility and inflammation following IAV infection. In contrast, overexpression of Plscr1 in ciliated epithelial cells protects mice from infection. Through transcriptomic analysis in mice and mechanistic studies in cell culture models, the authors reveal that Plscr1 transcriptionally upregulates Ifnlr1 expression and physically interacts with this receptor on the plasma membrane, thereby enhancing IFN-λ-mediated viral clearance.

Overall, it's a well-performed study, however, causality between Plscr1 and Ifnlr1 expression needs to be more firmly established. This is because two recent studies of PLSCR1 KO cells infected with different viruses found no major differences in gene expression levels compared with their WT controls (Xu et al. Nature, 2023; LePen et al. PLoS Biol, 2024). There were also defects in the expression of other cytokines (type I and II IFNs plus TNF-alpha) so a clear explanation of why Ifnlr1 was chosen should also be given.

While Plscr1 has long been recognized as a cell-intrinsic antiviral restriction factor, few studies have explored its broader physiological role. This study thus provides interesting insights into a specific function of Plscr1 in IAV-permissive airway epithelial cells and its contribution to whole-body anti-viral immunity. There are three important issues that should be addressed, and several minor points should also be considered.

(1) The authors propose that Plscr1 restricts IAV infection by regulating the type III IFN signaling pathway. While the data show a positive correlation between Ifnlr1 and Plscr1 levels in both mouse and cell culture models, additional evidence is needed to establish causality between the impaired type III IFN pathway, and the increased susceptibility observed in Plscr1-KO mice. To strengthen this conclusion, the following experiments could be undertaken: (i) Measure IAV titers in WT, Plscr1-KO, Ifnlr1-KO, and Plscr1/ Ifnlr1-double KO cells. If the antiviral activity of Plscr1 is highly dependent on Ifnlr1, there should be no further increase in IAV titers in double KO cells compared to single KO cells; (ii) over-express Plscr1 in Ifnlr1-KO cells to determine if it still inhibits IAV infection. If Plscr1's main action is to upregulate Ifnlr1, then it should not be able to rescue susceptibility since Ifnlr1 cannot be expressed in the KO background. If Plscr1 over-expression rescues viral susceptibility, then there are Ifnlr1-independent mechanisms involved. These experiments should help clarify the relative contribution of the type III IFN pathway to Plscr1-mediated antiviral immunity.

(2) Transcriptional activation of IFNLR1 by Plscr1 is a central mechanistic conclusion of this manuscript. A ChIP assay was used to demonstrate direct binding between Plscr1 and the Ifnrl1 promoter region. This single evidence does not sufficiently prove the role of Plscr1 in transcriptional activation. Other forms of evidence would help make this mechanistic explanation more compelling. For example, nuclear un-on experiments would demonstrate Ifnrl1 mRNA synthesis in addition to promoter binding.

(3) In Figure 4, the authors demonstrate the interaction between Plscr1 and Ifnlr1. They suggest that this interaction modulates IFN-λ signaling. However, Figures 5C-E show that the 5CA mutant, which lacks surface localization and the ability to bind Ifnlr1, exhibits similar anti-flu activity to WT Plscr1. Does this mean the interaction between Plscr1 and Ifnlr1 is dispensable for Plscr1-mediated antiviral function? Can the authors compare the activation of IFN-λ signaling pathway in Plscr1-KO cells expressing empty vector, WT Plscr1, and 5CA mutant? This could be done by measuring downstream ISG expression or using an ISRE-luciferase reporter assay upon IFN-λ treatment.

Reviewer #2 (Public review):

This nice study explores the role of phospholipid scramblase 1 (PLSCR1) in regulating antiviral immunity and host morbidity during influenza A virus (IAV) infection. The authors identify PLSCR1 as a critical regulator of interferon-lambda receptor 1 (IFNLR1) expression, acting through enzymatic-independent mechanisms. Using PLSCR1-deficient and conditional overexpression mouse models, the study demonstrates that PLSCR1 enhances antiviral responses and mitigates inflammation, potentially through modulating type III interferon (IFN-λ) signaling. While the findings underline the importance of PLSCR1 in early viral control and tissue homeostasis, they also highlight its cell-specific functions, particularly in ciliated airway epithelial cells. This work contributes to understanding the interplay between host factors and antiviral pathways, paving the way for novel therapeutic strategies targeting host proteins.

Specific Comments:

(1) The statement that type I interferons are expressed by "almost all cells" is inaccurate (line 61). Type I IFN production is also context-dependent and often restricted to specific cell types upon infection or stimulation.

(2) The antiviral response is assessed solely through flu M gene expression. Incorporating infectious virus titers (e.g., TCID50 or plaque assay) would provide a more robust and direct measure of antiviral activity.

(3) While mRNA expression of interferons is measured, protein levels (e.g., through ELISA) should also be quantified to establish the functional relevance of IFN expression changes.

(4) It is unclear whether reduced IFNLR1 expression translates to defective downstream signaling or antiviral responses after IFN-λ treatment in PLSCR1-deficient cells. This is particularly pertinent given the increase in IFN-λ ligand in vivo, which might compensate for receptor downregulation.

(5) Detailed gating strategies for immune cell subsets are absent and should be included for clarity and reproducibility.

(6) The study does not definitively establish that reduced IFN-λ signaling causes the observed in vivo phenotype. Increased morbidity and mortality in PLSCR1-deficient mice could also stem from elevated TNF-α levels and lung damage, as proinflammatory cytokines and/or enhanced lung damage are known contributors to influenza morbidity and mortality. This point warrants detailed discussions.

Reviewer #3 (Public review):

Summary:

Yang et al. have investigated the role of PLSCR1, an antiviral interferon-stimulated gene (ISG), in host protection against IAV infection. Although some antiviral effects of PLSCR1 have been described, its full activity remains incompletely understood.

This study now shows that Plscr1 expression is induced by IAV infection in the respiratory epithelium, and Plscr1 acts to increase Ifn-λr1 expression and enhance IFN-λ signaling possibly through protein-protein interactions on the cell membrane.

Strengths:

The study sheds light on the way Ifnlr1 expression is regulated, an area of research where little is known. The study is extensive and well-performed with relevant genetically modified mouse models and tools.

Weaknesses:

There are some issues that need to be clarified/corrected in the results and figures as presented.

Also, the study does not provide much information about the role of PLSCR1 in the regulation of Ifn-λr1 expression and function in immune cells. This would have been a plus.

Author Response:

We are proceeding without revisions as the first author has chosen to withdraw from the project and will not be contributing further.

eLife Assessment

This study investigates the conditions under which abstract knowledge transfers to new learning. It presents convincing evidence across a number of behavioral experiments that when explicit awareness of learned statistical structure is present, knowledge can transfer immediately, but that otherwise similar transfer requires sleep-dependent consolidation. The valuable results provide new constraints on theories of transfer learning and consolidation.

Reviewer #1 (Public review):

Summary:

This paper investigates the effects of the explicit recognition of statistical structure and sleep consolidation on the transfer of learned structure to novel stimuli. The results show a striking dissociation in transfer ability between explicit and implicit learning of structure, finding that only explicit learners transfer structure immediately. Implicit learners, on the other hand, show an intriguing immediate structural interference effect (better learning of novel structure) followed by successful transfer only after a period of sleep.

Strengths:

This paper is very well written and motivated, and the data are presented clearly with a logical flow. There are several replications and control experiments and analyses that make the pattern of results very compelling. The results are novel and intriguing, providing important constraints on theories of consolidation. The discussion of relevant literature is thorough. In sum, this work makes an exciting and important contribution to the literature.

Reviewer #2 (Public review):

Summary:

Sleep has not only been shown to support the strengthening of memory traces but also their transformation. A special form of such transformation is the abstraction of general rules from the presentation of individual exemplars. The current work used large online experiments with hundreds of participants to shed further light on this question. In the training phase participants saw composite items (scenes) that were made up of pairs of spatially coupled (i.e., they were next to each other) abstract shapes. In the initial training, they saw scenes made up of six horizontally structured pairs and in the second training phase, which took place after a retention phase (2 min awake, 12 hour incl. sleep, 12 h only wake, 24 h incl. sleep), they saw pairs that were horizontally or vertically coupled. After the second training phase, a two-alternatives-forced-choice (2-AFC) paradigm, where participants had to identify true pairs versus randomly assembled foils, was used to measure performance on all pairs. Finally, participants were asked five questions to identify, if they had insight into the pair structure and post-hoc groups were assigned based on this. Mainly the authors find that participants in the 2 minute retention experiment without explicit knowledge of the task structure were at chance level performance for the same structure in the second training phase, but had above chance performance for the vertical structure. The opposite was true for both sleep conditions. In the 12 h wake condition these participants showed no ability to discriminate the pairs from the second training phase at all.

Strengths:

All in all, the study was performed to a high standard and the sample size in the implicit condition was large enough to draw robust conclusions. The authors make several important statistical comparisons and also report an interesting resampling approach. There is also a lot of supplemental data regarding robustness.

Weaknesses:

My main concern regards the small sample size in the explicit group and the lack of experimental control.

Reviewer #3 (Public review):

In this project, Garber and Fiser examined how the structure of incidentally learned regularities influences subsequent learning of regularities, that either have the same structure or a different one. Over a series of six online experiments, it was found that the structure (spatial arrangement) of the first set of regularities affected learning of the second set, indicating that it has indeed been abstracted away from the specific items that have been learned. The effect was found to depend on the explicitness of the original learning: Participants who noticed regularities in the stimuli were better at learning subsequent regularities of the same structure than of a different one. On the other hand, participants whose learning was only implicit had an opposite pattern: they were better in learning regularities of a novel structure than of the same one. However, when an overnight sleep separated the first and second learning phases, this opposite effect was reversed and came to match the pattern of the explicit group, suggesting that the abstraction and transfer in the implicit case were aided by memory consolidation.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper investigates the effects of the explicit recognition of statistical structure and sleep consolidation on the transfer of learned structure to novel stimuli. The results show a striking dissociation in transfer ability between explicit and implicit learning of structure, finding that only explicit learners transfer structure immediately. Implicit learners, on the other hand, show an intriguing immediate structural interference effect (better learning of novel structure) followed by successful transfer only after a period of sleep.

Strengths:

This paper is very well written and motivated, and the data are presented clearly with a logical flow. There are several replications and control experiments and analyses that make the pattern of results very compelling. The results are novel and intriguing, providing important constraints on theories of consolidation. The discussion of relevant literature is thorough. In sum, this work makes an exciting and important contribution to the literature.

Weaknesses:

There have been several recent papers which have identified issues with alternative forced choice (AFC) tests as a method of assessing statistical learning (e.g. Isbilen et al. 2020, Cognitive Science). A key argument is that while statistical learning is typically implicit, AFC involves explicit deliberation and therefore does not match the learning process well. The use of AFC in this study thus leaves open the question of whether the AFC measure benefits the explicit learners in particular, given the congruence between knowledge and testing format, and whether, more generally, the results would have been different had the method of assessing generalization been implicit. Prior work has shown that explicit and implicit measures of statistical learning do not always produce the same results (eg. Kiai & Melloni, 2021, bioRxiv; Liu et al. 2023, Cognition).

The authors argued in their response to this point that this issue could have quantitative but not qualitative impacts on the results, but we see no reason that the impact could not be qualitative. In other words, it should be acknowledged that an implicit test could potentially result in the implicit group exhibiting immediate structure transfer.

We thank the reviewer for their feedback and added a statement in our discussion section acknowledging the possible effects of alternative measures of learning.

Given that the explicit/implicit classification was based on an exit survey, it is unclear when participants who are labeled "explicit" gained that explicit knowledge. This might have occurred during or after either of the sessions, which could impact the interpretation of the effects and deserves discussion.

We agree with the mentioned shortcoming in principle, although there are good methodological reasons for this, as discussed in our previous response. We added a statement on this topic to our discussion to make the potential issues and our reasoning in the design decision more transparent for the reader.

Reviewer #2 (Public review):

Summary:

Sleep has not only been shown to support the strengthening of memory traces, but also their transformation. A special form of such transformation is the abstraction of general rules from the presentation of individual exemplars. The current work used large online experiments with hundreds of participants to shed further light on this question. In the training phase participants saw composite items (scenes) that were made up of pairs of spatially coupled (i.e., they were next to each other) abstract shapes. In the initial training, they saw scenes made up of six horizontally structured pairs and in the second training phase, which took place after a retention phase (2 min awake, 12 hour incl. sleep, 12 h only wake, 24 h incl. sleep), they saw pairs that were horizontally or vertically coupled. After the second training phase, a two-alternativesforced-choice (2-AFC) paradigm, where participants had to identify true pairs versus randomly assembled foils, was used to measure performance on all pairs. Finally, participants were asked five questions to identify, if they had insight into the pair structure and post-hoc groups were assigned based on this. Mainly the authors find that participants in the 2 minute retention experiment without explicit knowledge of the task structure were at chance level performance for the same structure in the second training phase, but had above chance performance for the vertical structure. The opposite was true for both sleep conditions. In the 12 h wake condition these participants showed no ability to discriminate the pairs from the second training phase at all.

Strengths:

All in all, the study was performed to a high standard and the sample size in the implicit condition was large enough to draw robust conclusions. The authors make several important statistical comparisons and also report an interesting resampling approach. There is also a lot of supplemental data regarding robustness.

Weaknesses:

My main concern regards the small sample size in the explicit group and the lack of experimental control.

We thank the reviewer for the valuable feedback throughout the review process. The issues mentioned here have been addressed in our previous response.

Reviewer #3 (Public review):

In this project, Garber and Fiser examined how the structure of incidentally learned regularities influences subsequent learning of regularities, that either have the same structure or a different one. Over a series of six online experiments, it was found that the structure (spatial arrangement) of the first set of regularities affected learning of the second set, indicating that it has indeed been abstracted away from the specific items that have been learned. The effect was found to depend on the explicitness of the original learning: Participants who noticed regularities in the stimuli were better at learning subsequent regularities of the same structure than of a different one. On the other hand, participants whose learning was only implicit had an opposite pattern: they were better in learning regularities of a novel structure than of the same one. However, when an overnight sleep separated the first and second learning phases, this opposite effect was reversed and came to match the pattern of the explicit group, suggesting that the abstraction and transfer in the implicit case were aided by memory consolidation.

In their revision the authors addressed my major comments successfully and I commend them for that.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

We would encourage the authors to add text to the manuscript that acknowledges/discusses the two issues pointed out in our review.

We added relevant passages to the discussion section of the manuscript.

Reviewer #2 (Recommendations for the authors):

The authors have improved some sections of the manuscript and this is reflected in my assessment. The major weaknesses remain unchanged. Since my review is published alongside the paper, readers can make up their own mind regarding their severity.

My only hard ask would be to add that the study was not preregistered into the main manuscript as I asked before! I am surprised that the authors are so reluctant to honestly state this fact....

We have not stated this fact in our manuscript until now since our understanding is that papers that report preregistered studies state and cite their preregistration in their method section, while any omission of such a statement by default conveys that no preregistration occurred. In fact, we cannot recall encountering papers with statements of no-preregistration in the literature. Nevertheless, we have no issue stating that our study was not preregistered and per the reviewer's request, we have added such an explicit statement in our manuscript.

Reviewer #3 (Recommendations for the authors):

*  I strongly urge the authors to remove the Results sub-sections from Methods.

We thank the reviewer for highlighting this issue arising from our previous layout, which we decided to handle the following way. We re-labeledl the subsections in question as “Additional Analyses” to avoid confusion, we removed any redundant findings already reported in Results of the main text, and we moved a small number of more substantial findings from the Methods Section to the main text Results as requested. We believe that this solution constitutes the most readable option, as we do not clutter the main results with extensive sanity checks and results

of minor interest, while we also do not need to establish experiment-wise result sections in the Supplementary Materials, which would further disperse information interested readers might look for.

*  Authors report that in Experiment 4 "Participants with explicit knowledge (n=23) show the same pattern of results as they did in Experiment 1", but that seems inaccurate, as they did learn novel pairs in Exp4 whereas they did not in Exp1. This can be seen in the figure and also in Methods-Results: "performing above chance for ... pairs of a novel structure (M=69.6, SE=5.9, d=0.69, t(22)=3.33 p=0.012, BF=13.6) in the second training phase"

We thank the reviewer for pointing out this error in our interpretation of the results and adjusted the section in question to better align with what our result actually shows.

eLife Assessment

This important study demonstrates that screening by artificial intelligence can identify relevant novel compounds for interacting with KATP channels. The experimental work is compelling. The broader significance of this work relates to the possibility that KATP channel mutations linked to congenital hyperinsulinism may be effectively rescued to the cell surface with a drug, which could normalize insulin secretion or enhance the effectiveness of existing KATP channel activators such as diazoxide.

Reviewer #1 (Public review):

Summary:

Multiple compounds that inhibit ATP-sensitive potassium (KATP) channels also chaperone channels to the surface membrane. The authors used an artificial intelligence (AI)-based virtual screening (AtomNet) to identify novel compounds that exhibit chaperoning effects on trafficking-deficient disease-causing mutant channels. One compound, which they named Aekatperone, acts as a low affinity, reversible inhibitor and effective chaperone. A cryoEM structure of KATP bound to Aekatperone showed that the molecule binds at the canonical inhibitory site.

Strengths and weaknesses:

The details of the AI screening itself are inevitably opaque, but appear to differ from classical virtual screening in not involving any physical docking of test compounds into the target site. The authors mention criteria that were used to limit the number of compounds, so that those with high similarity to known binders and 'sequence identity' (does this mean structural identity) were excluded. The identified molecules contain sulfonylurea-like moieties. How different are they from other sulfonylureas?

The experimental work confirming that Aekatperone acts to traffic mutant KATP channels to the surface and acts as a low affinity, reversible, inhibitor is comprehensive and clear, with very convincing cell biological and patch-clamp data, as is the cryoEM structural analysis, for which the group are leading experts. In addition to the three positive chaperone-effective molecules, the authors identified a large number of compounds that are predicted binders but apparently have no chaperoning effect.

The authors suggest that the novel compound may be a promising therapeutic for treatment of congenital hyperinsulinism due to trafficking defective KATP mutations. Because they are low affinity, reversible, inhibitors. This is a very interesting concept, and perhaps a pulsed dosing regimen would allow trafficking without constant channel inhibition (which otherwise defeats the therapeutic purpose), although it is unclear whether the new compound will offer advantages over earlier low-affinity sulfonylurea inhibitor chaperones. These include tolbutamide which has very similar affinity and effect to Aekatperone. As the authors point out this (as well as other sulfonlyureas) are currently out of favor because of potential adverse cardiovascular effects, but again, it is unclear why Aekatperone should not have the same concerns.

Comments on revised version:

The authors have been very responsive to the first reviews. No further comments.

Reviewer #2 (Public review):

Summary:

In their study 'AI-Based Discovery and CryoEM Structural Elucidation of a KATP Channel Pharmacochaperone', ElSheikh and colleagues undertake a computational screening approach to identify candidate drugs that may bind to an identified binding pocket in the SUR1 subunit of KATP channels. Other KATP channel inhibitors such as glibenclamide have been previously shown to bind in this pocket, and in addition to inhibition KATP channel function, these inhibitors can very effectively rescue cell surface expression of trafficking deficient KATP mutations that cause excessive insulin secretion (Congenital Hyperinsulinism). However, a challenge for their utility for treatment of hyperinsulinism has been that they are powerful inhibitors of the channels that are rescued to the channel surface. In contrast, successful therapeutic pharmacochaperones (eg. CFTR chaperones) permit function of the channels rescued to the cell membrane. Thus, a key criteria for the authors' approach in this case was to identify relatively low affinity compounds that target the glibenclamide binding site (and be washed off) - these could potentially rescue KATP surface expression, but also permit KATP function.

Strengths:

The main findings of the manuscript include:

(1) Computational screening of a large virtual compound library, followed by functional screening of cell surface expression, which identified several potential candidate pharmacochaperones that target the glibenclamide binding site.

(2) Prioritization and functional characterization of Aekatperone as a low affinity KATP inhibitor which can be readily 'washed off' in patch clamp, and cell based efflux assays. Thus the drug clearly rescues cell surface expression, but can be manipulated experimentally to permit function of rescued channels.

(3) Determination of the binding site and dynamics of this candidate drug by cryo-EM, and functional validation of several residues involved in drug sensitivity using mutagenesis and patch clamp.

The experiments are well-conceived and executed, and the study is clearly described. The results of the experiments are very straightforward and clearly support the conclusions drawn by the authors. I found the study to provide important new information about KATP chaperone effects of certain drugs, with interesting considerations in terms of ion channel biology and human disease.

Context and remaining challenges:

(1) The chaperones can effectively rescue KATP trafficking mutants, but clearly not as strongly as the higher affinity inhibitor glibenclamide. There is likely a challenging relationship between efficacy of trafficking rescue and channel inhibition (ie. rescued channels are inhibited and therefore non-functional) that will need to be overcome in terms of applying drugs of this class. This is recognized and clarified appropriately by the authors both in their experimental approaches and discussion. In experiments it is straightforward to wash off the chaperone, but this would not be the case in an organism.

(2) Recent developments with ion channel trafficking correctors in the CFTR field illustrate the importance of investigating underlying mechanisms. Development of pharmacological tools and approaches in other channel types (such as KATP or other transporters and channels) will build our understanding of pathways involved in regulating maturation of membrane proteins, and ways to manipulate them.

Comments on revised version:

I have no further suggestions, thank you for the detailed response.

Author response:

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

Reviewer #1 (Public review):

Summary:

Multiple compounds that inhibit ATP-sensitive potassium (KATP) channels also chaperone channels to the surface membrane. The authors used an artificial intelligence (AI)-based virtual screening (AtomNet) to identify novel compounds that exhibit chaperoning effects on trafficking-deficient disease-causing mutant channels. One compound, which they named Aekatperone, acts as a low affinity, reversible inhibitor and effective chaperone. A cryoEM structure of KATP bound to Aekatperone showed that the molecule binds at the canonical inhibitory site.

Strengths and weaknesses:

The details of the AI screening itself are inevitably opaque, but appear to differ from classical virtual screening in not involving any physical docking of test compounds into the target site. The authors mention criteria that were used to limit the number of compounds, so that those with high similarity to known binders and 'sequence identity' (does this mean structural identity) were excluded. The identified molecules contain sulfonylurea-like moieties. How different are they from other sulfonylure4as?

We thank the reviewers for the questions. As part of the library preparation, molecules with greater than 0.5 Tanimoto similarity in ECFP4 space to any known binders of the target protein and its homologs within 70% sequence identity were excluded to increase the possibility of identifying novel hits. After scoring and ranking the molecules by the AtomNet® technology, a diversity clustering was performed using the Butina algorithm (Butina D. Unsupervised Data Base Clustering Based on Daylight’s Fingerprint and Tanimoto Similarity: A Fast and Automated Way To Cluster Small and Large Data Sets, J. Chem. Inf. Comput. Sci. 1999, 39, 747–750) with a Tanimoto similarity cutoff of 0.35 in ECFP4 space to minimize selection of structurally similar scaffolds for the final compound buy-list. We have revised the results and methods sections to make this clear.

Sulfonylureas are defined by their core structure comprising a sulfonyl group (–S(=O)₂) and a urea moiety (–NH–CO–NH–). While some compounds identified in our study contain a sulfonamide group (R-S(=O) ₂-NR₂), they differ structurally from sulfonylureas by lacking the key urea group and by incorporating unique R-group substitutions (we have now added this to Figure 1A legend). For example, compound C27 (Z2068224500) includes a sulfonamide group but not a urea moiety. Likewise, C45 (Aekatperone, Z1620764636) contains a sulfonamide group along with an aromatic, nitrogen-rich heterocyclic ring, but no urea group. Additionally, the R-groups in these compounds are more complex than the simple aromatic or alkyl chains typical of sulfonylureas. They include heterocyclic aromatic systems and nitrogen-rich structures, which likely influence their binding properties and lipophilicity. These structural differences suggest distinct functional and pharmacological profiles as supported by our biochemical and functional studies.

The experimental work confirming that Aekatperone acts to traffic mutant KATP channels to the surface and acts as a low affinity, reversible, inhibitor is comprehensive and clear, with very convincing cell biological and patch-clamp data, as is the cryoEM structural analysis, for which the group are leading experts. In addition to the three positive chaperone-effective molecules, the authors identified a large number of compounds that are predicted binders but apparently have no chaperoning effect. Did any of them have inhibitory action on channels? If so, does this give clues to separating chaperoning from inhibitory effects?

This is an interesting question. Evidence from cryo-EM, biochemical and electrophysiology studies reveal a critical role of Kir6.2 N-terminus in K_ATP channel assembly and gating, and that pharmacological chaperones like glibenclamide, repaglinide, carbamazepine, and now aekatperone exert their chaperoning and inhibitory effects by stabilizing the interaction between Kir6.2 N-terminus and the SUR1-ABC core. This stabilization, while promoting the assembly of Kir6.2 and SUR1 to “chaperone” trafficking-impaired mutant channels to the cell surface, also inhibits the channel by restricting the Kir6.2 C-terminal domain from rotating to an open state. An additional mechanism by which these compounds inhibit channel activity is by preventing SUR1-NBD dimerization, which mediates physiological activation of the channel by MgADP (see review: Driggers CM, Shyng SL. Mechanistic insights on K_ATP channel regulation from cryo-EM structures. J Gen Physiol. 2023 Jan 2;155(1): e202113046, PMID: 36441147). From our compound screening, we did find some compounds that showed mild inhibition of the channel by electrophysiology but no obvious chaperone effects by western blots. It is possible that small chaperoning effects of some compounds showing mild channel inhibition effects were missed due to the lower sensitivity of the western blot assay compared to electrophysiology. Alternatively, these compounds could inhibit channels by preventing SUR1NBD dimerization without stabilizing the Kir6.2 N-terminus, which is required for the chaperone effect based on our model. Unfortunately, we did not find any compounds that show chaperone effects but no channel inhibition effects, which is consistent with our understanding of how this type of K_ATP chaperones work (i.e. by stabilizing Kir6.2 N-terminus interaction with SUR1’s ABC core).

The authors suggest that the novel compound may be a promising therapeutic for treatment of congenital hyperinsulinism due to trafficking defective KATP mutations. Because they are low affinity, reversible, inhibitors. This is a very interesting concept, and perhaps a pulsed dosing regimen would allow trafficking without constant channel inhibition (which otherwise defeats the therapeutic purpose), although it is unclear whether the new compound will offer advantages over earlier low-affinity sulfonylurea inhibitor chaperones. These include tolbutamide which has very similar affinity and effect to Aekatperone. As the authors point out this (as well as other sulfonlyureas) are currently out of favor because of potential adverse cardiovascular effects, but again, it is unclear why Aekatperone should not have the same concerns.

We thank the reviewer for the comments. This is clearly an important question to address in the future. While we have not directly tested the effects of Aekatperone on cardiac functions, we did assess its inhibitory effect on cells expressing the cardiac K_ATP channel isoform (SUR2A/Kir6.2). Our results indicate that Aekatperone exhibits higher sensitivity toward the pancreatic K_ATP channel isoform (SUR1/Kir6.2) compared to the cardiac isoform. However, we acknowledge that Aekatperone could still have cardiotoxic effects through its potential action on other channels, such as the hERG channel.

It is worth noting that tolbutamide, despite its known cardiotoxic effects, does not exert these effects through cardiac K_ATP channel inhibition. This has been demonstrated in studies showing no inhibitory effect of tolbutamide on SUR2A/Kir6.2 channels and on channels formed by Kir6.2 and SUR1 harboring the S1238Y mutation (also shown as S1237Y in some studies using a different SUR1 isoform)--the amino acid substitution found in SUR2A at the corresponding position (Ashfield R, Gribble FM, Ashcroft SJ, Ashcroft FM. Identification of the high-affinity tolbutamide site on the SUR1 subunit of the K_ATP channel. Diabetes. 1999 Jun;48(6):1341-7, PMID: 10342826). This suggests that tolbutamide’s cardiotoxic effects might involve other targets like the hERG channel. Interestingly, tolbutamide contains a hydrophobic tail and aromatic rings that align well with the structural features for hERG interaction (Garrido A, Lepailleur A, Mignani SM, Dallemagne P, Rochais C. hERG toxicity assessment: Useful guidelines for drug design. Eur J Med Chem. 2020 Jun 1;195:112290, PMID: 32283295). In contrast, highaffinity sulfonylureas such as glibenclamide and glimepiride, which have additional benzamide moieties, are associated with lower cardiovascular risks (Douros A, Yin H, Yu OHY, Filion KB, Azoulay L, Suissa S. Pharmacologic Differences of Sulfonylureas and the Risk of Adverse Cardiovascular and Hypoglycemic Events. Diabetes Care. 2017, 40:1506-1513, PMID:

28864502). Given these considerations, a comprehensive assessment of Aekatperone’s potential cardiotoxicity is crucial. Future studies involving in silico modeling, in vitro, and in vivo experiments will be essential to evaluate Aekatperone’s interaction with hERG and other offtarget effects. These efforts will help clarify its safety profile. This point has now been added to the Discussion.

Reviewer #2 (Public review):

Summary:

In their study 'AI-Based Discovery and CryoEM Structural Elucidation of a KATP Channel Pharmacochaperone', ElSheikh and colleagues undertake a computational screening approach to identify candidate drugs that may bind to an identified binding pocket in the SUR1 subunit of

KATP channels. Other KATP channel inhibitors such as glibenclamide have been previously shown to bind in this pocket, and in addition to inhibition KATP channel function, these inhibitors can very effectively rescue cell surface expression of trafficking deficient KATP mutations that cause excessive insulin secretion (Congenital Hyperinsulinism). However, a challenge for their utility for treatment of hyperinsulinism has been that they are powerful inhibitors of the channels that are rescued to the channel surface. In contrast, successful therapeutic pharmacochaperones (eg. CFTR chaperones) permit function of the channels rescued to the cell membrane. Thus, a key criteria for the authors' approach in this case was to identify relatively low affinity compounds that target the glibenclamide binding site (and be washed off) - these could potentially rescue KATP surface expression, but also permit KATP function.

Strengths:

The main findings of the manuscript include:

(1) Computational screening of a large virtual compound library, followed by functional screening of cell surface expression, which identified several potential candidate pharmacochaperones that target the glibenclamide binding site.

(2) Prioritization and functional characterization of Aekatperone as a low affinity KATP inhibitor which can be readily 'washed off' in patch clamp, and cell based efflux assays. Thus the drug clearly rescues cell surface expression, but can be manipulated experimentally to permit function of rescued channels.

(3) Determination of the binding site and dynamics of this candidate drug by cryo-EM, and functional validation of several residues involved in drug sensitivity using mutagenesis and patch clamp.

The experiments are well-conceived and executed, and the study is clearly described. The results of the experiments are very straightforward and clearly support the conclusions drawn by the authors. I found the study to provide important new information about KATP chaperone effects of certain drugs, with interesting considerations in terms of ion channel biology and human disease.

Weaknesses:

I don't have any major criticisms of the study as described, but I had some remaining questions that could be addressed in a revision.

(1) The chaperones can effectively rescue KATP trafficking mutants, but clearly not as strongly as the higher affinity inhibitor glibenclamide. Is this relationship between inhibitory potency, and efficacy of trafficking an intrinsic challenge of the approach? I suspect that it may be an intractable problem in the sense that the inhibitor bound conformation that underlies the chaperone effect cannot be uncoupled from the inhibited gating state. But this might not be true (many partial agonist drugs with low efficacy can be strongly potent, for example). In this case, the approach is really to find a 'happy medium' of a drug that is a weak enough inhibitor to be washed away, but still strong enough to exert some satisfactory chaperone effect. Could some additional clarity be added in the discussion on whether the chaperone and gating effects can be 'uncoupled'.

Thank you for the suggestion. A similar question was raised by Reviewer 1, which was addressed above (public review, point 2). We have now added more discussion to clarify this point.

(2) Based on the western blots in Figure 2B, the rescue of cell surface expression appears to require a higher concentration of AKP compared to the concentration response of channel inhibition (~9 microM in Figure 3, perhaps even more potent in patch clamp in Figure 2C). Could the authors clarify/quantify the concentration response for trafficking rescue?

Thank you for bringing up this observation. Indeed, the pharmacochaperone effects of Aekatperone as well as other previously published K_ATP pharmacochaperones require higher concentrations compared to their inhibitory effects on surface-expressed channels. This difference likely stems from the necessity for these compounds to cross the cell membrane and interact with newly synthesized channels in the endoplasmic reticulum, where the trafficking rescue occurs. We estimate that effective pharmacochaperone activity for Aekatperone can be achieved at concentrations ranging from 50 to 100 µM in cells expressing trafficking-deficient K_ATP channel mutants, higher than that required for inhibition of surface-expressed channels (~9 µM IC50). Future work could focus on medicinal chemistry modifications, for example esterification of Aekatperone (Zhou G. Exploring Ester Prodrugs: A Comprehensive Review of Approaches, Applications, and Methods. Pharmacology & Pharmacy, 2024, 15, 269-284). Once inside the cell, the esters would be cleaved by endogenous esterases to release the active compound, ensuring efficient intracellular delivery. This strategy could potentially improve membrane permeability and bioavailability of the compound, which would lower the required concentrations to achieve desired chaperoning effects.

(3) A future challenge in the application of pharmacochaperones of this type in hyperinsulinism may be the manipulation of chaperone concentration in order to permit function. In experiments it is straightforward to wash off the chaperone, but this would not be the case in an organism. I wondered if the authors had attempted to rescue channel function with diazoxide ine presence of AKP, rather than after washing off (ie. is AKP inhibition insurmountable, or can it be overcome by sufficient diazoxide).

Thank you for raising this important point. We have previously shown (Martin GM et al. Pharmacological Correction of Trafficking Defects in ATP-sensitive Potassium Channels Caused by Sulfonylurea Receptor 1 Mutations. J Biol Chem. 2016, 291: 21971-21983, PMID: 27573238) that diazoxide, which stabilizes K_ATP channels in an open conformation, also reduces physical association between Kir6.2 N-terminus and SUR1 as demonstrated by reduced crosslinking of engineered azido-phenylalanine (an unnatural amino acid) at Kir6.2 N-terminal amino acid 12 position to SUR1. Incubating cells with diazoxide did not rescue the trafficking mutants but actually further reduced the maturation efficiency of trafficking mutants. For this reason, we did not include diazoxide during Aekatperone incubation and instead added diazoxide after Aekatperone washout to potentiate the activity of mutant channels rescued to the cell surface. In vivo, we envision testing alternating Aekatperone and diazoxide dosing to maximize functional rescue of K_ATP trafficking mutants.

(4) Do the authors have any information about the turnover time of KATP after washoff of the chaperone (how stable are the rescued channels at the cell surface)? This is a difficult question to probe when glibenclamide is used as a chaperone, but maybe much simpler to address with a lower affinity chaperone like AKP.

Thank you for your thoughtful comment. While we have not yet tested the duration of rescued K_ATP channels at the cell surface following Aekatperone washout, we have conducted similar studies with carbamazepine (Chen PC et al. Carbamazepine as a novel small molecule corrector of trafficking-impaired ATP-sensitive potassium channels identified in congenital hyperinsulinism. J Biol Chem. 2013, 288: 20942-20954, PMID: 23744072), another compound exhibiting reversible inhibitory and chaperone effects (apparent affinity between glibenclamide and Aekatperone). Our previous findings with carbamazepine showed that in cultured cells its chaperone effects were detectable as early as 1 hour and peaked around 6 hours after treatment. Furthermore, when carbamazepine was removed following a 16-hour treatment, the rescue effect persisted for up to 6 hours post-drug removal. These results provide a potential duration of the surface expression rescue effects of reversible pharmacochaperones.

Reviewer #1 (Recommendations for the authors):

The paper is well-written and comprehensive with only very minor essentially copy-editing needed. That said, it would be good if the authors could answer the main points raised above:

(1) What is the relevant Tanimoto parameters and sequence identity (does this mean structural identity) for the identified compounds?

As we answered above in response to the overall assessment, to facilitate the identification of novel hits, molecules with greater than 0.5 Tanimoto similarity in ECFP4 space to any known binders of the target protein and its homologs within 70% amino acid sequence identity were excluded from the commercial library. Additionally, after scoring and ranking the molecules by the AtomNet® technology, a diversity clustering was performed on the top 30,000 molecules using the Butina algorithm with a Tanimoto similarity cutoff of 0.35 in ECFP4 space to minimize selection of structurally similar scaffolds for the final compound buy-list.

(2) Did any of the identified putative binders have inhibitory action on channels? If so, does this give clues to separating chaperoning from inhibitory effects?

Please see response to the same question in the overall assessment above.

(3) Acknowledge that the identified compounds contain sulfonylurea-like moieties, and address why Aekatperone should (or perhaps does not) offer anything advantage over low affinity sulfonrylureas such as tolbutamide?

Please see response to the same question in the overall assessment above.

Reviewer #2 (Recommendations for the authors):

Thank you for assembling the interesting study, which I felt was well designed and communicated. The diverse approaches used in the study, with consistent findings, were definitely a strength. The core findings are also well distilled in the main body of the text, and although there is quite a lot of supplementary information, I felt that it was presented appropriately and well selected in terms of what would be important for readers hoping to learn more. In addition to the questions described above, I only had a few minor editorial issues that could be fixed related to presentation.

(1) Figure 1B. The colours and resolution of the chemical structures are difficult to see clearly and could be improved.

We have revised the figure accordingly.

(2) This is a minor wording point... first sentence of the discussion describes the drugs as pancreatic-selective, when it would be more clear to describe them as selective for the pancreatic isoform of KATP (Kir6.2/SUR1), or perhaps better as 'exhibiting ~4-5 fold selective for SUR1-containing KATP channels vs. SUR2A or SUR2B'.

We have changed the wording as suggested.

(3) As a curiosity (not necessary to do more experiments), but I am curious if the authors know whether there is any meaningful enhancement of trafficking of WT channels by AKP.

All pharmacochaperones we have identified to date including Aekatperone also slightly enhance WT channel surface expression (10-20%).

Reviewing editor recommendations:

(1) Given the modest resolution of the EM reconstruction, it is perhaps not entirely clear how AKP was assigned to the density observed. Specifically, it would be helpful to include a comparison of an AKP-free map and the current AKP map (filtered to a similar resolution) showing slice views of densities in the region around the inferred binding site. This would be very helpful in ascertaining whether the cryoEM reconstruction is an independent validation of the computational and functional experiments or whether the density inference depends on the additional knowledge.

We appreciate the editor’s suggestion. We have now added a Supplemental Figure (Supplementary Figure 7 in the revised manuscript) that compares our AKP-free cryoEM density deposited previously to the EMDB (EMD-26320) and the AKP-bound cryoEM density from this study, with cryoEM density (filtered to the same resolution) superimposed on the structural model.

(2) It could help to mention in brief what is a probable mechanism of AKP inhibition - that is how after binding of AKP, channel opening is restricted. Is it similar to that of other site A ligands?

Based on the strong Kir6.2 N-terminal cryoEM density observed in our AKP map, AKP most likely inhibits K_ATP channels by trapping the Kir6.2 N-terminus in the central cavity of SUR1’s ABC core thus preventing Kir6.2-C-terminal domain from rotating to an open conformation, similar to other ligands that stabilize the Kir6.2 N-terminus-SUR1 interface by binding to site A (such as tolbutamide and AKP), site B (such as repaglinide), or both site A and site B (such as glibenclamide). We have now included this in the revised Results and Discussion sections.

(3) In the context of the MD simulations, do other site A ligands (which from my understanding bind at a similar site) also exhibit similar flexibility as AKP? If there is information available on the flexibility of ligands of varying affinities, bound to the same site, maybe some correlative inferences can be drawn? However, in MD simulation trajectories it is not entirely uncommon for a ligand to simply get trapped in a local energy well. Since the authors have performed significant analysis of their MD results it could be worth mentioning/discussing such phenomena.

Previously published MD data addressing ligand dynamics, such as glibenclamide in the SUR1 pocket (Walczewska-Szewc K, Nowak W. Photo-Switchable Sulfonylureas Binding to ATPSensitive Potassium Channel Reveal the Mechanism of Light-Controlled Insulin Release. J Phys Chem B. 2021, 125: 13111-13121, PMID: 34825567), indicate a certain degree of flexibility. Unfortunately, we cannot directly compare these results, as the simulations were performed without the KNtp domain in the SUR1 cavity, which partially contributes to ligand stabilization. This is an issue we plan to investigate in the future.

In this study, we ran five independent MD simulations, each 500 ns long, resulting in a total of 2.5 μs of simulation time. Across all replicates, the ligand stayed in the same position, with variations mainly in the dynamics of the blurred segment. Considering the length of the simulations and the consistency across the runs, we believe this binding pose is stable and represents a global (or at least highly stable) energy minimum, consistent with the cryo-EM data.

(4) In electrophysiological assays, 10 uM AKP seems to inhibit all currents (Figure 2), but in the Rb+ flux assay ~10 uM appears to be the IC50. The reason for this difference is not entirely clear and it would help to comment on this.

Thank you for noticing the difference. The initial electrophysiological experiments were conducted using the very small amount of AKP provided to us from Atomwise. We estimated the concentration of the reconstituted AKP the best we could, but the concentration was likely to not be very accurate due to difficulty in handling the very small amount of the AKP powder. Subsequent Rb<sup>+>/sup> efflux experiments were conducted using a different, larger batch of AKP we purchased from Enamine. We have now stated this in the Methods section.

eLife Assessment

This valuable manuscript uses mathematical modeling to address the synchrony of the vertebrate segmentation clock with the developmental processes. The authors use convincing arguments to support the idea that this would allow the evolution of flexible body plans and a variable number of segments. This manuscript could be of interest to developmental biologists and systems biologists.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

In this manuscript, Hammond et al. study robustness of the vertebrate segmentation clock against morphogenetic processes such as cell ingression, cell movement and cell division to ask whether the segmentation clock and morphogenesis are modular or not. The modularity of these two would be important for evolvability of the segmenting system. The authors adopt a previously proposed 3D model of the presomitic mesoderm (Uriu et al. 2021 eLife) and include new elements; different types of cell ingression, tissue compaction and cell cycles. Based on the results of numerical simulations that synchrony of the segmentation clock is robust, the authors conclude that there is a modularity in the segmentation clock and morphogenetic processes.

The presented results support the conclusion. The manuscript is clearly written.

Major comments from the original round of review:

[Optional] In both the current model and Uriu et al. 2021, coupling delay in phase oscillator model is not considered. Given that several previous studies (e.g. Lewis 2003, Herrgen et al. 2010, Yoshioka-Kobayashi et al. 2020) suggested the presence of coupling delays in Delta-Notch signaling, could the authors analyze the effect of coupling delay on robustness of the segmentation clock against morphogenetic processes?

Significance:

Synchronization of the segmentation clock has been studied by mathematical modeling, but most previous studies considered cells in a static tissue without morphogenesis. In the previous study by Uriu et al. 2021, morphogenetic processes such as cell advection due to tissue elongation, tissue shortening, and cell mobility were considered in synchronization. The current manuscript provides methodological advances in this aspect by newly including cell ingression, tissue compaction and cell cycle. In addition, the authors bring a concept of modularity and evolvability to the field of the vertebrate segmentation clock, which is new. On the other hand, the manuscript confirms that the synchronization of the segmentation clock is robust by careful simulations, but it does not propose or reveal new mechanisms for making it robust or modular. The main targets of the manuscript will be researchers working on somitogenesis and evolutionary biologists who are interested in evolution of developmental systems. The manuscript will also be interested by broader audiences, like developmental biologists, biophysicists, and physicists and computer scientists who are working on dynamical systems.

Reviewer #2 (Public review):

Summary:

The manuscript from Hammond et al., investigates the modularity of the segmentation clock and morphogenesis in early vertebrate development, focusing on how these processes might independently evolve to influence the diversity of segment numbers across vertebrates.

Methodology: The study uses a previously published computational model, parameterized for zebrafish, to simulate and analyse the interactions between the segmentation clock and the morphogenesis of the pre-somitic mesoderm (PSM). Their model integrates cell advection, motility, compaction, cell division, and the synchronization of the embryo clock. Three alternative scenarios of PSM morphogenesis were modeled to examine how these changes affect the segmentation clock.

Model System: The computational model system combines a representation of cell movements and the phase oscillator dynamics of the segmentation clock within a three-dimensional horseshoe-shaped domain mimicking the geometry of the vertebrate embryo PSM. The parameters used for the mathematical model are mostly estimated from previously published experimental findings.

Key Findings and Conclusions: (1) The segmentation clock was found to be broadly robust against variations in morphogenetic processes such as cell ingression and motility; (2) Changes in the length of the PSM and the strength of phase coupling within the clock significantly influenced the system's robustness; (3) The authors conclude that the segmentation clock and PSM morphogenesis exhibited developmental modularity (i.e. relative independence), allowing these two phenomena to evolve independently, and therefore possibly contributing to the diverse segment numbers observed in vertebrates.

Major comments from the original round of review:

(1) The key conclusion drawn by the authors (that there is robustness, and therefore modularity, between the morphogenetic cellular processes modeled and the embryo clock synchronization) stems directly from the modeling results appropriately presented and discussed in the manuscript.

The model comprises some strong assumptions, however all have been clearly explained and the parameterization choices are supported by experimental findings, providing biological meaning to the model. Estimated parameters are well explained, and seem reasonable assumptions (from the embryology perspective).

(2) This study, as is, achieves its proposed goal of evaluating the potential robustness of the embryo clock to changes in (some) morphogenetic processes. The authors do not claim that the model used is complete, and they properly identify some limitations, including the lack of cell-cell interactions. Given the recognized importance of cellular physical interactions for successful embryo development, including them in the model would be a significant addition in future studies.

(3) The authors have deposited all the code used for analysis in a public GitHub repository that is updated and available for the research community.

(4) In page 6, the authors justify their choice of clock parameters for cells ingressing the PSM: "As ingressing cells do not appear to express segmentation clock genes (Mara et al. (2007)), the position at which cells ingress into the PSM can create challenges for clock patterning, as only in the 'off' phase of the clock will ingressing cells be in-phase with their neighbors."

However, there are several lines of evidence (in chick and mouse), that some oscillatory clock genes are already being expressed as early as in the gastrulation phase (so prior to PSM ingression) (Feitas et al, 2001 [10.1242/dev.128.24.5139]; Jouve et al, 2002 [10.1242/dev.129.5.1107]; Maia-Fernandes at al, 2024 [10.1371/journal.pone.0297853]).

Question: Is this also true in zebrafish? (I.e. is there any recent experimental evidence that the clock genes are not expressed at ingression, since the paper cited to support this assumption is from 2007).

If they are expressed in zebrafish (as they are in mouse and chick), then the cell addition should have random clock gene periods when they enter the PSM and not start all with a constant initial phase of zero. Probably this will not impact the results since the cells will also be out of phase with their neighbors when they "ingress", however, it will model more closely the biological scenario (and avoid such criticism).

Significance:

GENERAL ASSESSMENT

This study uses a previously published model to simulate alternative scenarios of morphogenetic parameters to infer the potential independence (termed here modularity) between the segmentation clock and a set of morphogenetic processes, arguing that such modularity could allow the evolution of more flexible body plans, therefore partially explaining the variability in the number of segments observed in the vertebrates. This question is fundamental and relevant, yet still poorly researched. This work provides a comprehensive simulation with a model that tries to simplify the many morphogenetic processes described in the literature, reducing it to a few core fundamental processes that allow drawing the conclusions sought. It provides theoretical insight to support a conceptual advance in the field of evolutionary vertebrate embryology.

ADVANCE

This study builds on a model recently published by Uriu et al. (eLife, 2021) that incorporates quantitative experimental data within a modeling framework including cell and tissue-level parameters, allowing the study of multiscale phenomena active during zebrafish embryo segmentation. Uriu's publication reports many relevant and often non-intuitive insights uncovered by the model, most notably the description of phase vortices formed by the synchronizing genetic oscillators interfering with the traveling-wave front pattern.

However, this model can be further explored to ask additional questions beyond those described in the original paper. A good example is the present study, which uses this mathematical framework to investigate the potential independence between two of the modeled processes, thereby extracting extra knowledge from it. Accordingly, the present study represents a step forward in the direction of using relevant theoretical frameworks to quantitatively explore the landscape of complex molecular hypotheses in silico, and with it shed some light on fundamental open questions or inform the design of future experiments in the lab.

The study incorporates a wide range of existing literature on the developmental biology of vertebrates. It comprehensively cites prior work, such as the foundational studies by Cooke and Zeeman on the segmentation clock and the role of FGF signaling in PSM development as discussed by Gomez et al. The literature properly covers the breadth of knowledge in this field.

AUDIENCE

Target audience: This study is relevant for fundamental research in developmental biology, specifically targeting researchers who focus on early embryo development and morphogenesis from both experimental and theoretical perspectives. It is also relevant for evolutionary biologists investigating the genetic factors that influence vertebrate evolution, as well as to computational biologists and bioinformatics researchers studying developmental processes and embryology.

Developmental researchers studying the segmentation clock in other vertebrate model organisms (namely mouse and chick), will find this publication especially valuable since it provides insights that can help them formulate new hypotheses to elucidate the molecular mechanisms of the clock (for example finding a set of evolutionarily divergent genes that might interfere with PSM length).<br /> Additionally, this study provides a set of cellular parameters that have yet to be measured in mouse and chick, therefore guiding the design of future experiments to measure them, allowing the simulation of the same model with sets of parameters from different vertebrate model organisms, therefore testing the robustness of the findings reported for zebrafish.

Reviewer #3 (Public review):

Summary:

In this manuscript, Verd and colleagues explored how various biologically relevant factors influence the robustness of clock dynamics synchronization among neighboring cells within the context of somatogenesis, adapting a mathematical model presented by Urio et. al in 2021 in a similar context. Specifically they show that clock dynamics is robust to different biological mechanisms such as cell infusion, cellular motility, compaction-extension and cell-division. On the other hand , the length of Presomitic Mesoderm (PSM) and density of cells in it has a significant role in the robustness of clock dynamics. While the manuscript is well-written and provides clear descriptions of methods and technical details, it tends to be somewhat lengthy.

Major comments from original round of review:

(1) The authors mention that "...the model is three dimensional and so can quantitatively recapture the rates of cell mixing that we observe in the PSM". I am not convinced with this justification of using a 3D model. None of the effects the authors explore in this manuscript requires a three dimensional model or full physical description of the cellular mechanics such as excluded volume interaction etc. A one-dimensional model characterized by cell position along the arclength of PSM and somatic region and segmentation clock phase θ can incorporate all the physics authors described in this manuscript as well as significantly computationally cheap allowing the authors to explore the effect of different parameters in greater detail.

(2) I am not sure about the justification for limiting the quantification of phase synchrony in a very limited (one cell diameter wide) region at one end of the somatic part (Page 33 below Fig. 9). From my understanding of the manuscript, the segments appear in significant length anterior to this region. Wouldn't an ensemble average of multiple such one cell diameter wide regions in the somatic region be a more accurate metric for quantifying synchrony?

(3) While studying the effect of cellular ingression, the authors study three discrete modes-random, DP and DP+LV and show that in the DP+LV mode the clock synchrony becomes affected. I would like the authors to explore this in a continuous fashion from a pure DP ingression to Pure LV ingression and intermediates.

(4) While studying the effect of length and density of cells in PSM on cellular synchrony, the authors restrict to 3 values of density and 6 values of PSM length keeping the other parameter constant. I would be interested to see a phase diagram similar to Fig. 7 in the two dimensional parameter space of L and ρ0. I am curious if a scaling relation exists for the parameter values that partition the parameter space with and without synchrony.

(5) Both in the abstract and introduction, the authors discuss at a great length about the variability in the number of segments. I am curious how the number and width of the segments observed depend on different parameters related to cellular mechanics and the segmentation clock ?

(6) The authors assume that the phase dynamics of the chemical network may be described by an oscillator with constant frequency. For the completeness of the manuscript, the author should discuss in detail, for which chemical networks this is a good assumption.

(7) Figure 3 and the associated text shows no effect of the cellular motility profile in the synchrony of the segmentation clock. This may be moved to the supplementary considering the length of this manuscript.

Significance:

The manuscript answers some important questions in the synchrony of segmentation clock in the vertebrates utilizing a model published earlier. However, the presented result is incomplete in some aspects (points 2 to 5 of section A) and that could be overcome by a more detailed analysis using a simpler one dimensional (point 1 of section A). I believe this manuscript could be of interest to an intersecting audience of developmental biologists, systems biologists, and physicists/engineers interested in dynamical systems.

[Editors' note: the authors have responded comprehensively to the reviews from Review Commons.]

Author response:

Reviewer #1 (Evidence, reproducibility and clarity):

Summary:

In this manuscript, Hammond et al. study robustness of the vertebrate segmentation clock against morphogenetic processes such as cell ingression, cell movement and cell division to ask whether the segmentation clock and morphogenesis are modular or not. The modularity of these two would be important for evolvability of the segmenting system. The authors adopt a previously proposed 3D model of the presomitic mesoderm (Uriu et al. 2021 eLife) and include new elements; different types of cell ingression, tissue compaction and cell cycles. Based on the results of numerical simulations that synchrony of the segmentation clock is robust, the authors conclude that there is a modularity in the segmentation clock and morphogenetic processes. The presented results support the conclusion. The manuscript is clearly written. I have several comments that could help the authors further strengthen their arguments.

Major comment: 

[Optional] In both the current model and Uriu et al. 2021, coupling delay in phase oscillator model is not considered. Given that several previous studies (e.g. Lewis 2003, Herrgen et al. 2010, Yoshioka-Kobayashi et al. 2020) suggested the presence of coupling delays in DeltaNotch signaling, could the authors analyze the effect of coupling delay on robustness of the segmentation clock against morphogenetic processes?

We thank the reviewer for the suggestion. Owing to the computational demands of including such a delay in the model, we cannot feasibly repeat every simulation analysed here in the presence of delay, and would like to note that the increased computational demand that delays put on the simulations is also the reason why Uriu et al 2021 did not include it, as stated in their published exchange with reviewers. However, analogous to our analysis in figure 7, we can analyse how varying the position of progenitor cell ingression affects synchrony in the presence of the coupling delay measured in zebrafish by Herrgen et al. (2010). We show this analysis in a new figure 8 (8B, specifically), on page 21, and discuss its implications in the text on pages 2022. Our analysis reveals that the model cannot recover synchrony using the default parameters used by Uriu et al. (2021) and reveal a much stronger dependence on the rate of cell mixing (vs) than shown in the instantaneous coupling case (cf. figure 7). However, by systematically varying the value of the delay we find that a relatively minor increase in the delay is sufficient to recover synchrony using the parameter set of Uriu et al. (see figure 8C). Repeating this across the three scenarios of cell ingression we see that the combination of coupling strength and delay determine the robustness of synchrony to varying position of cell ingression. This suggests that the combination of these two parameters constrain the evolution of morphogenesis.

Minor comments: 

-  PSM radius and oscillation synchrony are both denoted by the same alphabet r. The authors should use different alphabets for these two to avoid confusion.

We thank the reviewer for spotting this. This has now been changed throughout to rT, as shorthand for ‘radius of tissue’.

-  page 5 Figure 1 caption: (x-x_a/L) should be (x-x_a)/L.

We thank the reviewer for spotting this. This has now been corrected.

-  Figure 3C: Description of black crosses in the panels is required in the figure legend.

Thank you for spotting this. The legend has now been corrected.

-  Figure 3C another comment: In this panel, synchrony r at the anterior PSM is shown. It is true that synchrony at anterior PSM is most relevant for normal segment formation. However, in this case, the mobility profile is changed, so it may be appropriate to show how synchrony at mid and posterior PSM would depend on changes in mobility profile. Is synchrony improved by cell mobility at the region where cell ingression happens?

We thank the reviewer for the suggestion. We have now plotted the synchrony along the AP axis for varying motility profiles, and this can be seen in figure 3 supplement 1, and is briefly discussed in the text on page 11. We show that while the synchrony varies with x-position (as already expected, see figure 2), there is no trend associated with the shape of the motility profile.

-  In page 12, the authors state that "the results for the DP and DP+LV cases are exactly equal for L = 185 um, as .... and the two ingression methods are numerically equivalent in the model". I understood that in this case two ingression methods are equivalent, but I do not understand why the results are "exactly" equal, given the presence of stochasticity in the model.

These results can be exactly equal despite the simulations being stochastic because they were both initialised using the same ‘seed’ in the source code. However, we now see that this might be confusing to the reader, and we have re-generated this figure but this time initialising the simulations for each ingression scenario using a different seed value. This is now reflected in the text on page 12 and in figure 4.

-  The authors analyze the effect of cell density on oscillation synchrony in Fig. 4 and they mention that higher density increases robustness of the clock by increasing the average number of interacting neighbours. I think it would be helpful to plot the average number of neighbouring cells in simulations as a function of density to quantitatively support the claim.

We thank the reviewer for their suggestion. Distributions of neighbour numbers for exemplar simulations with varying density can now be found in  figure 4 supplementary figure 1 and are referred to in the text on page 11.

-  The authors analyze the effect of PSM length on synchrony in Fig. 4. I think kymographs of synchrony r as shown in Fig. 2D would also be helpful to show that indeed cells get synchronized while advecting through a longer PSM.

We thank the reviewer for their suggestion and agree that visualising the data in this way is an excellent idea. We have generated the suggested kymographs and added them to figure 4 as supplements 2 and 4, and discussed these results in the text on page 12.

-  I understand that cells in M phase can interact with neighboring cells with the same coupling strength kappa in the model, although their clocks are arrested. If so, this aspect should be also mentioned in the main text in page 16, as this coupling can be another noise source for synchrony.

We agree this is an important clarification. We explicitly state this, and briefly justify our choice, in the text on page 16.

-  Figure 5-figure supplement 2: panel labels A, B, C are missing. 

Thank you for bringing this to our attention. These have now been added.

– Figure 5-figure supplement 3: panel labels A, B, C are missing.

Thank you for bringing this to our attention. These have now been added.

Reviewer #1 (Significance):

Synchronization of the segmentation clock has been studied by mathematical modeling, but most previous studies considered cells in a static tissue without morphogenesis. In the previous study by Uriu et al. 2021, morphogenetic processes such as cell advection due to tissue elongation, tissue shortening, and cell mobility were considered in synchronization. The current manuscript provides methodological advances in this aspect by newly including cell ingression, tissue compaction and cell cycle. In addition, the authors bring a concept of modularity and evolvability to the field of the vertebrate segmentation clock, which is new. On the other hand, the manuscript confirms that the synchronization of the segmentation clock is robust by careful simulations, but it does not propose or reveal new mechanisms for making it robust or modular. The main targets of the manuscript will be researchers working on somitogenesis and evolutionary biologists who are interested in evolution of developmental systems. The manuscript will also be interested by broader audiences, like developmental biologists, biophysicists, and physicists and computer scientists who are working on dynamical systems.

We thank the reviewer for their interest in our manuscript and for acknowledging us as one of the first to address the modularity and evolvability of somitogenesis. We hope that this work will encourage others to think about these concepts in this system too.  

In the original submission, we identified a high enough coupling strength as the main mechanism underlying the identified modularity in somitogenesis. Since, we have included an analysis of the coupling delay and find that it is the interplay between coupling strength and coupling delay that mediate the identified modularity, allowing PSM morphogenesis and the segmentation clock to evolve independently in regions of parameter space that are constrained and determined by the interplay between these two parameters. We have now added an extra figure (figure 8) where we explore this interplay and have discussed it at length in the last section of the results and in the discussion. We again thank the reviewer for encouraging us to include delays in our analysis.

Reviewer #2 (Evidence, reproducibility and clarity):

SUMMARY 

The manuscript from Hammond et al., investigates the modularity of the segmentation clock and morphogenesis in early vertebrate development, focusing on how these processes might independently evolve to influence the diversity of segment numbers across vertebrates.

Methodology: The study uses a previously published computational model, parameterized for zebrafish, to simulate and analyse the interactions between the segmentation clock and the morphogenesis of the pre-somitic mesoderm (PSM). Their model integrates cell advection, motility, compaction, cell division, and the synchronization of the embryo clock. Three alternative scenarios of PSM morphogenesis were modeled to examine how these changes affect the segmentation clock.

Model System: The computational model system combines a representation of cell movements and the phase oscillator dynamics of the segmentation clock within a three-dimensional horseshoe-shaped domain mimicking the geometry of the vertebrate embryo PSM. The parameters used for the mathematical model are mostly estimated from previously published experimental findings.

Key Findings and Conclusions: (1) The segmentation clock was found to be broadly robust against variations in morphogenetic processes such as cell ingression and motility; (2) Changes in the length of the PSM and the strength of phase coupling within the clock significantly influenced the system's robustness; (3) The authors conclude that the segmentation clock and PSM morphogenesis exhibited developmental modularity (i.e. relative independence), allowing these two phenomena to evolve independently, and therefore possibly contributing to the diverse segment numbers observed in vertebrates.

MAJOR COMMENTS

(1) The key conclusion drawn by the authors (that there is robustness, and therefore modularity, between the morphogenetic cellular processes modeled and the embryo clock synchronization) stems directly from the modeling results appropriately presented and discussed in the manuscript. The model comprises some strong assumptions, however all have been clearly explained and the parameterization choices are supported by experimental findings, providing biological meaning to the model. Estimated parameters are well explained and seem reasonable assumptions (from the embryology perspective).

We thank the reviewer for their positive comments about our work

(2) This study, as is, achieves its proposed goal of evaluating the potential robustness of the embryo clock to changes in (some) morphogenetic processes. The authors do not claim that the model used is complete, and they properly identify some limitations, including the lack of cellcell interactions. Given the recognized importance of cellular physical interactions for successful embryo development, including them in the model would be a significant addition in future studies.

We would like to clarify that the model does include cell-cell interactions as cells interact with their neighbours’ clock phase to synchronise and to avoid occupying the same physical space. 

(3) The authors have deposited all the code used for analysis in a public GitHub repository that is updated and available for the research community.

We support open source coding practices.

(4) In page 6, the authors justify their choice of clock parameters for cells ingressing the PSM: "As ingressing cells do not appear to express segmentation clock genes (Mara et al. (2007)), the position at which cells ingress into the PSM can create challenges for clock patterning, as only in the 'off' phase of the clock will ingressing cells be in-phase with their neighbours."  However, there are several lines of evidence (in chick and mouse), that some oscillatory clock genes are already being expressed as early as in the gastrulation phase (so prior to PSM ingression) (Feitas et al, 2001 [10.1242/dev.128.24.5139]; Jouve et al, 2002 [10.1242/dev.129.5.1107]; Maia-Fernandes at al, 2024 [10.1371/journal.pone.0297853]) Question: Is this also true in zebrafish? (I.e. is there any recent experimental evidence that the clock genes are not expressed at ingression, since the paper cited to support this assumption is from 2007). If they are expressed in zebrafish (as they are in mouse and chick), then the cell addition should have random clock gene periods when they enter the PSM and not start all with a constant initial phase of zero. Probably this will not impact the results since the cells will also be out of phase with their neighbours when they "ingress", however, it will model more closely the biological scenario (and avoid such criticism).

We thank the reviewer for their comments. While it is known that in zebrafish the clock begins oscillating during epiboly and before the onset of segmentation (Riedel-Kruse et al., 2007), to our knowledge no-one has examined whether posteriorly or laterally ingressing progenitor cells express clock genes prior to their ingression into the PSM, which occurs later in development than the first oscillations which give rise to the first somites. We have not found any published evidence of her/hes gene expression in the dorsal donor tissues or lateral tissues surrounding the PSM, however we acknowledge that this has not been actively studied before and our assumption relies on an absence of evidence, rather than evidence of absence. 

However, we agree with the reviewer that one should include such an analysis for completeness, and we have now generated additional simulations where progenitor cells ingress with a random clock phase. This data is presented in figure 2 supplement 1 and mentioned in the main text on page 9.

MINOR COMMENTS 

(1) The citations are appropriate and cover the major labs that have published work related to this study (although with some overrepresentation of the lab that published the model used).

We have cited the vast literature on somitogenesis to the best of our ability and do recognise that the work of the Oates lab appears prominently, but this is probably because their experimental data were originally used to parametrise the model in Uriu et al. 2021.

(2) The text is clear, carefully written, and both the methods and the reasoning behind them are clearly explained and supported by proper citations.

We are very glad to see that the reviewer found that the manuscript was clearly presented.

(3) The figures are comprehensive, properly annotated, with explanatory self-contained legends. I have no comments regarding the presentation of the results.

Thank you

(4) Minor suggestions: 

a. Page 26: In the Cell addition sub-section of the Methods section, correct all instances where the word domain is used, but subdomain should be used (for clarity and coherence with the description of the model, stated as having a single domain comprising 3 subdomains).

We thank the reviewer for raising this, this is a good point. We have now corrected to ‘subdomain’ where appropriate.

b. Page 32: Table 1. Parameter values used in our work, unless otherwise stated -> Suggestion: Add a column with the individual citations used for each parameter (to facilitate the confirmation of each corresponding reference).

Thank you for the suggstion, we have now done this (see table 1 page 36).

Reviewer #2 (Significance):

GENERAL ASSESSMENT 

This study uses a previously published model to simulate alternative scenarios of morphogenetic parameters to infer the potential independence (termed here modularity) between the segmentation clock and a set of morphogenetic processes, arguing that such modularity could allow the evolution of more flexible body plans, therefore partially explaining the variability in the number of segments observed in the vertebrates. This question is fundamental and relevant, yet still poorly researched. This work provides a comprehensive simulation with a model that tries to simplify the many morphogenetic processes described in the literature, reducing it to a few core fundamental processes that allow drawing the conclusions seeked. It provides theoretical insight to support a conceptual advance in the field of evolutionary vertebrate embryology.

ADVANCE

This study builds on a model recently published by Uriu et al. (eLife, 2021) that incorporates quantitative experimental data within a modeling framework including cell and tissue-level parameters, allowing the study of multiscale phenomena active during zebrafish embryo segmentation. Uriu's publication reports many relevant and often non-intuitive insights uncovered by the model, most notably the description of phase vortices formed by the synchronizing genetic oscillators interfering with the traveling-wave front pattern.  However, this model can be further explored to ask additional questions beyond those described in the original paper. A good example is the present study, which uses this mathematical framework to investigate the potential independence between two of the modeled processes, thereby extracting extra knowledge from it. Accordingly, the present study represents a step forward in the direction of using relevant theoretical frameworks to quantitatively explore the landscape of complex molecular hypotheses in silico, and with it shed some light on fundamental open questions or inform the design of future experiments in the lab.

The study incorporates a wide range of existing literature on the developmental biology of vertebrates. It comprehensively cites prior work, such as the foundational studies by Cooke and Zeeman on the segmentation clock and the role of FGF signaling in PSM development as discussed by Gomez et al. The literature properly covers the breadth of knowledge in this field.

AUDIENCE

Target audience | This study is relevant for fundamental research in developmental biology, specifically targeting researchers who focus on early embryo development and morphogenesis from both experimental and theoretical perspectives. It is also relevant for evolutionary biologists investigating the genetic factors that influence vertebrate evolution, as well as to computational biologists and bioinformatics researchers studying developmental processes and embryology.

Developmental researchers studying the segmentation clock in other vertebrate model organisms (namely mouse and chick), will find this publication especially valuable since it provides insights that can help them formulate new hypotheses to elucidate the molecular mechanisms of the clock (for example finding a set of evolutionarily divergent genes that might interfere with PSM length). Additionally, this study provides a set of cellular parameters that have yet to be measured in mouse and chick, therefore guiding the design of future experiments to measure them, allowing the simulation of the same model with sets of parameters from different vertebrate model organisms, therefore testing the robustness of the findings reported for zebrafish.

Reviewer #3 (Evidence, reproducibility and clarity): 

In this manuscript, Verd and colleagues explored how various biologically relevant factors influence the robustness of clock dynamics synchronization among neighboring cells within the context of somatogenesis, adapting a mathematical model presented by Urio et. al in 2021 in a similar context. Specifically they show that clock dynamics is robust to different biological mechanisms such as cell infusion, cellular motility, compaction-extension and cell-division. On the other hand , the length of Presomitic Mesoderm (PSM) and density of cells in it has a significant role in the robustness of clock dynamics. While the manuscript is well-written and provides clear descriptions of methods and technical details, it tends to be somewhat lengthy.

Below are the comments I would like the authors to address:

(1) The authors mention that "...the model is three dimensional and so can quantitatively recapture the rates of cell mixing that we observe in the PSM". I am not convinced with this justification of using a 3D model. None of the effects the authors explore in this manuscript requires a three dimensional model or full physical description of the cellular mechanics such as excluded volume interaction etc. A one-dimensional model characterized by cell position along the arclength of PSM and somatic region and segmentation clock phase θ can incorporate all the physics authors described in this manuscript as well as significantly computationally cheap allowing the authors to explore the effect of different parameters in greater detail.

One of the main objectives of the work we present in this manuscript is to assess how the evolution of PSM morphogenesis affects, or does not affect, segment patterning. The PSM is a three-dimensional tissue with differing cell rearrangement dynamics along its anterior-posterior axis. In addition, PSM dimension, density, the rearrangement rate, and patterns of cell ingression all vary across vertebrate species, and they are functional, especially cell mixing as it promotes synchronisation and drives elongation. In order to answer questions on the modularity of somitogenesis we therefore consider it absolutely necessary to include a three-dimensional representation of the PSM that captures single cells and their movements. In addition, this will allow us, as Reviewer #2 also pointed out, to reparametrize our model using species-specific data as it becomes available. 

While the reviewer is right in that lower dimensional representations would be computationally more efficient, and are generally more tractable, it would not be possible to represent cell mixing in one dimension, as this happens in three dimensions. One could perhaps encode the synchrony-promoting effect of cell mixing via some coupling function κ(x) that increases towards the posterior, however it is unclear what existing biological data one could use to parameterise this function or determine its form. Cell mixing can be modelled in a two-dimensional framework, however this cannot quantitatively recapture the rate of cell mixing observed in vivo, which is an advantage of this model. 

Furthermore, it is unclear how one would simulate processes such as compactionextension using a one-dimensional model. The two different scenarios of cell ingression which we consider can also not be replicated in a one-dimensional model, as having a population of cells re-acquiring synchrony on the dorsal surface of the tissue while new material is added to the ventral side, creating asynchrony, is qualitatively different than a one-dimensional scenario where cells are introduced continuously along the spatial axis.

(2) I am not sure about the justification for limiting the quantification of phase synchrony in a very limited (one cell diameter wide) region at one end of the somatic part (Page 33 below Fig. 9). From my understanding of the manuscript, the segments appear in significant length anterior to this region. Wouldn't an ensemble average of multiple such one cell diameter wide regions in the somatic region be a more accurate metric for quantifying synchrony?

Indeed, such a metric (e.g. as that used by Uriu et al. to quantify synchrony along the xaxis) would be more accurate for determining synchrony within the PSM. However, as per the clock and wavefront model of somitogenesis, only synchrony at the very anterior of the PSM (or at the wavefront, equivalently) is functional for somitogenesis and thus evolution. Therefore, we restrict our analysis to the anterior-most region of the PSM. We now further justify this in the main text on page 9.

(3) While studying the effect of cellular ingression, the authors study three discrete modes- random, DP and DP+LV and show that in the DP+LV mode the clock synchrony becomes affected. I would like the authors to explore this in a continuous fashion from a pure DP ingression to Pure LV ingression and intermediates.

We thank the reviewer for this suggestion; this is a very interesting question. We are currently working on a related computational and experimental project to address the question of how PSM morphogenesis can change over evolutionary time to evolve the different modes that we see across species. As part of this work, we are running precisely the simulations suggested by the reviewer to find regions of parameter space in which all the relevant morphogenetic processes can freely evolve.  While interesting, this work is however outside the scope of the current manuscript.

(4) While studying the effect of length and density of cells in PSM on cellular synchrony, the authors restrict to 3 values of density and 6 values of PSM length keeping the other parameter constant. I would be interested to see a phase diagram similar to Fig. 7 in the two-dimensional parameter space of L and ρ0. I am curious if a scaling relation exists for the parameter values that partition the parameter space with and without synchrony.

We thank the reviewer for their suggestion and agree that this would constitute an interesting addition to the manuscript. We have now generated these data, which are shown in figure 4 supplement 5 and mentioned on page 13. We see no clear relationship between these two variables when co-varying in the presence of random ingression. 

(5) Both in the abstract and introduction, the authors discuss at a great length about the variability in the number of segments. I am curious how the number and width of the segments observed depend on different parameters related to cellular mechanics and the segmentation clock ?

We thank the reviewer for this question. It was not clear to us if this was something the reviewer wants us to address in the study’s background and introduction, or an analysis we should include in the results. Therefore, we have responded to both comprehensively below:

The prevailing conceptual framework for understanding this is the clock and wavefront model (Cooke and Zeeman, 1976), which posits that the somite length is inversely proportional to the frequency of the clock relative to the speed of the wavefront, and that the total number of segments is the relative frequency multiplied by the total duration of somitogenesis.

Experimentally we know that the frequency is determined in part by the coupling strength (Liao, Jorg, and Oates, 2016), and from comparative embryological studies (Gomez et al., 2008; Steventon et al., 2016) we know that changes in the elongation dynamics of the PSM correlate with changes in somite number, presumably by altering the total duration of somitogenesis (Gomez et al., 2009). These changes in elongation are thought to be driven by the changes in cell and tissue mechanics we test in our manuscript. 

Within our model, we cannot in general predict how the number of segments responds to changes in either clock parameters or cell mechanical parameters, as we lack understanding of what causes somitogenesis to cease; this is thus not encoded in our model and segmentation can in principle proceed indefinitely. Therefore, we have not performed this analysis.

Similarly, we have not included an analysis of somite length. This is for two reasons: 1) as per the clock and wavefront model, the frequency at the PSM anterior (which we analyse) is equivalent to this measurement, as we assume (in general) the wavefront ($x = x_{a}$) is inertial. 2) the length of the nascent somite is not thought to be of much relevance to the adult phenotype, and by extension evolution. Somites undergo cell division and growth soon after their patterning by the segmentation clock, therefore their final size does not majorly depend on the dynamics of the segmentation clock. Rather, the main function of the clock is to control their number (and polarity).

(6) The authors assume that the phase dynamics of the chemical network may be described by an oscillator with constant frequency. For the completeness of the manuscript, the author should discuss in detail, for which chemical networks this is a good assumption.

We thank the reviewer for their suggestion and now justify this assumption in the methods on page 31. 

Such an assumption is appropriate for the segmentation clock, as the clock in the posterior of the PSM is thought to oscillate with a constant frequency, at least for the majority of somitogenesis although the frequency of somite formation slows towards the end of this process in zebrafish (Giudicelli et al., 2007, PLoS Biol.). In addition, PSM cells isolated and cultured in the presence of FGF (thus replicating the signalling environment of the posterior PSM) will continue to exhibit her1 oscillations with an apparently constant frequency (Webb et al., 2016). 

We note that such formulations are widely used within the segmentation clock literature (e.g. Riedel-Kruse et al., 2007, Morelli et al., 2009).

(7) Figure 3 and the associated text shows no effect of the cellular motility profile in the synchrony of the segmentation clock. This may be moved to the supplementary considering the length of this manuscript.

Thank you for the suggestion. However, we would argue that the lack of effect is a crucial result when discussing modularity. Reviewer #2 agrees with this assessment.

Reviewer #3 (Significance): 

The manuscript answers some important questions in the synchrony of segmentation clock in the vertebrates utilizing a model published earlier. However, the presented result is incomplete in some aspects (points 2 to 5 of section A) and that could be overcome by a more detailed analysis using a simpler one dimensional (point 1 of section A). I believe this manuscript could be of interest to an intersecting audience of developmental biologists, systems biologists, and physicists/engineers interested in dynamical systems.

eLife Assessment

This useful study presents a comparative investigation of category selectivity in dogs and humans. The study compares brain representations of animate and inanimate objects, replicating and extending previous reports in this nascent field of dog FMRI. The methods and results seem to lack sufficient detail, appropriate controls, or statistical evidence, so at this stage of the review process, the strength of evidence is deemed incomplete.

Reviewer #1 (Public review):

Summary

Farkas and colleagues conducted a comparative neuroimaging study with domestic dogs and humans to explore whether social perception in both species is underpinned by an analogous distinction between animate and inanimate entities an established functional organizing principle in the primate and human brain. Presenting domestic dogs and humans with clips of three animate classes (dogs, humans, cats) and one inanimate control (cars), the authors also set out to compare how dogs and humans perceive their own vs other species. Both research questions have been previously studied in dogs, but the authors used novel dynamic stimuli and added animate and inanimate classes, which have not been investigated before (i.e., cats and cars). Combining univariate and multivariate analysis approaches, they identified functionally analogous areas in the dog and human occipito-temporal cortex involved in the perception of animate entities, largely replicating previous observations. This further emphasizes a potentially shared functional organizing principle of social perception in the two species. The authors also describe between-species divergencies in the perception of the different animate classes, arguing for a less generalized perception of animate entities in dogs, but this conclusion is not convincingly supported by the applied analyses and reported findings.

Strengths

Domestic dogs represent a compelling model species to study the neural bases of social perception and potentially shared functional organizing principles with humans and primates. The field of comparative neuroimaging with dogs is still young, with a growing but still small number of studies, and the present study exemplifies the reproducibility of previous research. Using dynamic instead of static stimuli and adding new stimuli classes, Farkas and colleagues successfully replicated and expanded previous findings, adding to the growing body of evidence that social perception is underpinned by a shared functional organizing principle in the dog and human occipito-temporal cortex.

Weaknesses

The study design is imbalanced, with only one category of inanimate objects vs. three animate entities. Moreover, based on the example videos, it appears that the animate stimuli also differed in the complexity of the content from the car stimuli, with often multiple agents interacting or performing goal-directed actions. Moreover, while dogs are familiar with cars, they are definitely of lower relevance and interest to them than the animate stimuli. Thus, to a certain extent, the results might also reflect differences in attention towards/salience of the stimuli.

The methods section and rationale behind the chosen approaches were often difficult to follow and lacked a lot of information, which makes it difficult to judge the evidence and the drawn conclusions, and it weakens the potential for reproducibility of this work. For example, for many preprocessing and analysis steps, parameters were missing or descriptions of the tools used, no information on anatomical masks and atlas used in humans was provided, and it is often not clear if the authors are referring to the univariate or multivariate analysis.

In regard to the chosen approaches and rationale, the authors generally binarize a lot of rich information. Instead of directly testing potential differences in the neural representations of the different animate entities, they binarize dissimilarity maps for, e.g. animate entity > inanimate cars and then calculate the overlap between the maps. The comparison of the overlap of these three maps between species is also problematic, considering that the human RSA was constricted to the occipital and temporal cortex (there is now information on how they defined it) vs. whole-brain in dogs. Considering that the stimuli do differ based on low-level visual properties (just not significantly within a run), the RSA would also allow the authors to directly test if some of the (dis)similarities might be driven by low-level visual features like they, e.g. did with the early visual cortex model. I do think RSA is generally an excellent choice to investigate the neural representation of animate (and inanimate) stimuli, but the authors should apply it more appropriately and use its full potential.

The authors localized some of the "animate areas" also with the early visual cortex model (e.g. ectomarginal gyrus, mid suprasylvian); in humans, it only included the known early visual cortex - what does this mean for the animate areas in dogs?

The results section also lacks information and statistical evidence; for example, for the univariate region-of-interest (ROI) analysis (called response profiles) comparing activation strength towards each stimulus type, it is not reported if comparisons were significant or not, but the authors state they conducted t-tests. The authors describe that they created spheres on all peaks reported for the contrast animate > inanimate, but they only report results for the mid suprasylvian and occipital gyrus (e.g. caudal suprasylvian gyrus is missing). Furthermore, considering that the ROIs were chosen based on the contrast animate > inanimate stimuli, activation strength should only be compared between animate entities (i.e., dogs, humans, cats), while cars should not be reported (as this would be double dipping, after selecting voxels showing lower activation for that category). The descriptive data in Figure 3B (pending statistical evidence) suggests there were no strong differences in activation for the three species in dog and human animate areas. Thus, the ROI analysis appears to contradict findings from the binary analysis approach to investigate species preference, but the authors only discuss the results of the latter in support of their narrative for conspecific preference in dogs and do not discuss research from other labs investigating own-species preference.

The authors also unnecessarily exaggerate novelty claims. Animate vs inanimate and own vs other species perceptions have both been investigated before in dogs (and humans), so any claims in that direction seem unsubstantiated - and also not needed, as novelty itself is not a sign of quality; what is novel, and a sign of theoretical advance besides the novelty, are as said the conceptual extension and replication of previous work.

Overall, more analyses and appropriate tests are needed to support the conclusions drawn by the authors, as well as a more comprehensive discussion of all findings.

Reviewer #2 (Public review):

Summary:

The manuscript reports an fMRI study looking at whether there is animacy organization in a non-primate, mammal, the domestic dog, that is similar to that observed in humans and non-human primates (NHPs). A simple experiment was carried out with four kinds of stimulus videos (dogs, humans, cats, and cars), and univariate contrasts and RSA searchlight analysis was performed. Previous studies have looked at this question or closely associated questions (e.g. whether there is face selectivity in dogs). The import of the present study is that it looks at multiple types of animate objects, dogs, humans, and cats, and tests whether there was overlapping/similar topography (or magnitude) of responses when these stimuli were compared to the inanimate reference class of cars. The main finding was of some selectivity for animacy though this was primarily driven by the dog stimuli, which did overlap with the other animate stimulus types, but far less so than in humans.

Strengths:

I believe that this is an interesting study in so far as it builds on other recent work looking at category-selectivity in the domestic dog. Given the limited number of such studies, I think it is a natural step to consider a number of different animate stimuli and look at their overlap. While some of the results were not wholly surprising (e.g. dog brains respond more selectively for dogs than humans or cats), that does not take away from their novelty, such as it is. The findings of this study are useful as a point of comparison with other recent work on the organization of high-level visual function in the brain of the domestic dog.

Weaknesses:

(1) One challenge for all studies like this is a lack of clarity when we say there is organization for "animacy" in the human and NHP brains. The challenge is by no means unique to the present study, but I do think it brings up two more specific topics.

First, one property associated with animate things is "capable of self-movement". While cognitively we know that cars require a driver, and are otherwise inanimate, can we really assume that dogs think of cars in the same way? After all, just think of some dogs that chase cars. If dogs represent moving cars as another kind of self-moving thing, then it is not clear we can say from this study that we have a contrast between animate vs inanimate. This would not mean that there are no real differences in neural organization being found. It was unclear whether all or some of the car videos showed them moving. But if many/most do, then I think this is a concern.

Second, there is quite a lot of potential complexity in the human case that is worth considering when interpreting the results of this study. In the human case, some evidence suggests that animacy may be more of a continuum (Sha et al. 2015), which may reflect taxonomy (Connolly et al. 2012, 2016). However moving videos seem to be dominated more by signals relevant to threat or predation relative to taxonomy (Nastase et al. 2017). Some evidence suggests that this purported taxonomic organization might be driven by gradation in representing faces and bodies of animals based on their relative similarity to humans (Ritchie et al. 2021). Also, it may be that animacy organization reflects a number of (partially correlated) dimensions (Thorat et al. 2019, Jozwik et al. 2022). One may wonder whether the regions of (partial) overlap in animate responses in the dog brain might have some of these properties as well (or not).

(2) It is stated that previous studies provide evidence that the dog brain shows selectivity to "certain aspects of animacy". One of these already looked at selectivity for dog and human faces and bodies and identified similar regions of activity (Boch et al. 2023). An earlier study by Dilks et al. (2015), not cited in the present work (as far as I can tell), also used dynamic stimuli and did not suffer from the above limitations in choosing inanimate stimuli (e.g. using toy and scene objects for inanimate stimuli). But it only included human faces as the dynamic animate stimulus. So, as far as stimulus design, it seems the import of the present study is that it included a *third* animate stimulus (cats) and that the stimuli were dynamic.

(3) I am concerned that the univariate results, especially those depicted in Figure 3B, include double dipping (Kriegesorte et al. 2009). The analysis uses the response peak for the A > iA contrast to then look at the magnitude of the D, H, C vs iA contrasts. This means the same data is being used for feature selection and then to estimate the responses. So, the estimates are going to be inflated. For example, the high magnitudes for the three animate stimuli above the inanimate stimuli are going to inherently be inflated by this analysis and cannot be taken at face value. I have the same concern with the selectivity preference results in Figure 3E.

I think the authors have two options here. Either they drop these analyses entirely (so that the total set of analyses really mirrors those in Figure 4), or they modify them to address this concern. I think this could be done in one of two ways. One would be to do a within-subject standard split-half analysis and use one-half of the data for feature selection and the other for magnitude estimation. The other would be to do a between-subject design of some kind, like using one subject for magnitude estimation based on an ROI defined using the data for the other subjects.

(4) There are two concerns with how the overlap analyses were carried out. First, as typically carried out to look at overlap in humans, the proportion is of overlapping results of the contrasts of interest, e.g, for face and body selectivity overlap (Schwarlose et al. 2006), hand and tool overlap (Bracci et al. 2012), or more recently, tool and food overlap (Ritchie et al. 2024). There are a number of ways of then calculating the overlap, with their own strengths and weaknesses (see Tarr et al. 2007). Of these, I think the Jaccard index is the most intuitive, which is just the intersection of two sets as a proportion of their union. So, for example, the N of overlapping D > iA and H > iA active voxels is divided by the total number of unique active voxels for the two contrasts. Such an overlap analysis is more standard and interpretable relative to previous findings. I would strongly encourage the authors to carry out such an analysis or use a similar metric of overlap, in place of what they have currently performed (to the extent the analysis makes sense to me).

Second, the results summarized in Figure 3A suggest multiple distinct regions of animacy selectivity. Other studies have also identified similar networks of regions (e.g. Boch et al. 2023). These regions may serve different functions, but the overlap analysis does not tell us whether there is overlap in some of these portions of the cortex and not in others. The overlap is only looked at in a very general sense. There may be more overlap locally in some portions of the cortex and not in others.

(5) Two comments about the RSA analyses. First, I am not quite sure why the authors used HMAX rather than layers of a standardly trained ImageNet deep convolutional neural network. This strikes me also as a missed opportunity since many labs have looked at whether later layers of DNNs trained on object categorization show similar dissimilarity structures as category-selective regions in humans and NHPs. In so far as cross-species comparisons are the motivation here, it would be genuinely interesting to see what would happen if one did a correlation searchlight with the dog brain and layers of a DNN, a la Cichy et al. (2016).

Second, from the text is hard to tell what the models for the class- and category-boundary effects were. Are there RDMs that can be depicted here? I am very familiar with RSA searchlight and I found the description of the methods to be rather opaque. The same point about overlap earlier regarding the univariate results also applies to the RSA results. Also, this is again a reason to potentially compare DNN RDMs to both the categorical models and the brains of both species.

(6) There has been emphasis of late on the role of face and body selective regions and social cognition (Pitcher and Ungerleider, 2021, Puce, 2024), and also on whether these regions are more specialized for representing whole bodies/persons (Hu et al. 2020, Taubert, et al. 2022). It may be that the supposed animacy organization is more about how we socialize and interact with other organisms than anything about animacy as such (see again the earlier comments about animacy, taxonomy, and threat/predation). The result, of a great deal of selectivity for dogs, some for humans, and little for cats, seems to readily make sense if we assume it is driven by the social value of the three animate objects that are presented. This might be something worth reflecting on in relation to the present findings.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary

Farkas and colleagues conducted a comparative neuroimaging study with domestic dogs and humans to explore whether social perception in both species is underpinned by an analogous distinction between animate and inanimate entities an established functional organizing principle in the primate and human brain. Presenting domestic dogs and humans with clips of three animate classes (dogs, humans, cats) and one inanimate control (cars), the authors also set out to compare how dogs and humans perceive their own vs other species. Both research questions have been previously studied in dogs, but the authors used novel dynamic stimuli and added animate and inanimate classes, which have not been investigated before (i.e., cats and cars). Combining univariate and multivariate analysis approaches, they identified functionally analogous areas in the dog and human occipitotemporal cortex involved in the perception of animate entities, largely replicating previous observations. This further emphasizes a potentially shared functional organizing principle of social perception in the two species. The authors also describe between- species divergencies in the perception of the different animate classes, arguing for a less generalized perception of animate entities in dogs, but this conclusion is not convincingly supported by the applied analyses and reported findings.

Strengths

Domestic dogs represent a compelling model species to study the neural bases of social perception and potentially shared functional organizing principles with humans and primates. The field of comparative neuroimaging with dogs is still young, with a growing but still small number of studies, and the present study exemplifies the reproducibility of previous research. Using dynamic instead of static stimuli and adding new stimuli classes, Farkas and colleagues successfully replicated and expanded previous findings, adding to the growing body of evidence that social perception is underpinned by a shared functional organizing principle in the dog and human occipito-temporal cortex.

Weaknesses

The study design is imbalanced, with only one category of inanimate objects vs. three animate entities. Moreover, based on the example videos, it appears that the animate stimuli also differed in the complexity of the content from the car stimuli, with often multiple agents interacting or performing goal-directed actions. Moreover, while dogs are familiar with cars, they are definitely of lower relevance and interest to them than the animate stimuli. Thus, to a certain extent, the results might also reflect differences in attention towards/salience of the stimuli.

We agree with the Reviewer and were aware that using only one class of inanimate objects but three classes of animate entities, along with the differences in complexity and relevance between the animate and the inanimate stimuli potentially elicited more attention to the inanimate condition and may have thus introduced a confound. We are revising the related limitation in the discussion to acknowledge this and to emphasize why we believe these differences do not compromise our main findings.

The methods section and rationale behind the chosen approaches were often difficult to follow and lacked a lot of information, which makes it difficult to judge the evidence and the drawn conclusions, and it weakens the potential for reproducibility of this work. For example, for many preprocessing and analysis steps, parameters were missing or descriptions of the tools used, no information on anatomical masks and atlas used in humans was provided, and it is often not clear if the authors are referring to the univariate or multivariate analysis.

We acknowledge the concerns regarding the clarity and completeness of the methods section and are significantly revising the descriptions of the methods. Of note, in humans, the Harvard-Oxford Cortical Structural Atlas (Frazier et al., 2005; Makris et al., 2006; Desikan et al., 2006; Goldstein et al., 2007), implemented within the FSL software package, was used for anatomical masks, while the Automated Anatomical Labeling atlas (Tzourio-Mazoyer et al., 2002) was used for assigning labels.

In regard to the chosen approaches and rationale, the authors generally binarize a lot of rich information. Instead of directly testing potential differences in the neural representations of the different animate entities, they binarize dissimilarity maps for, e.g. animate entity > inanimate cars and then calculate the overlap between the maps.

We thank the Reviewer for these comments and ideas. We also appreciate the second Reviewer for their related concerns and suggestions about the overlap calculation. Since the neural processing of different animate entities in the dog brain is largely unexplored, in some of our analyses we aimed to provide a straightforward and directly comparable characterization of animacy perception in the two species. We believe that a measure of how overlapping the neural representations of different animate classes are in the dog vs. the human visual cortex is a simple but meaningful and insightful characterization of how animacy perception is structured in the two species, despite the lack of spatial detail. Our decision to use binarization was based on these considerations. In response to this Reviewer’s request for providing richer information, in our revised manuscript, we will present more details and additional non-binarized calculations. Specifically, we are going to use nonbinarized data to present the response profiles of a broad, anatomically defined set of regions that have been related in other works to visual functions, to thus show where there is significant difference and overlap between the neural responses for the three animate classes in each species.

The comparison of the overlap of these three maps between species is also problematic, considering that the human RSA was constricted to the occipital and temporal cortex (there is now information on how they defined it) vs. whole-brain in dogs.

We thank this Reviewer for raising yet another relevant point about overlap calculation. We note that the overlap calculation for univariate results used the visually responsive cortex in both dogs and humans. The decision to restrict the multivariate analysis to the occipital and temporal lobes in humans, where the visual areas are, was to reduce computational load. Since RSA in dogs yielded significant voxels almost exclusively in the occipital and temporal cortices, we believe this decision did not introduce major bias in our results. This concern will also be discussed in our revised submission.

Of note, in the category- and class-boundary test, as for the other multivariate tests, the occipital and temporal cortex of humans was delineated based on the MNI atlas.

Considering that the stimuli do differ based on low-level visual properties (just not significantly within a run), the RSA would also allow the authors to directly test if some of the (dis)similarities might be driven by low-level visual features like they, e.g. did with the early visual cortex model. I do think RSA is generally an excellent choice to investigate the neural representation of animate (and inanimate) stimuli, but the authors should apply it more appropriately and use its full potential.

We thank the Reviewer for this suggestion. While this study did not aim to investigate the correlation between low-level visual features and animacy, the data is available, and the suggested analysis can be conducted in the future. This issue will also be discussed in our revised submission.

The authors localized some of the "animate areas" also with the early visual cortex model (e.g. ectomarginal gyrus, mid suprasylvian); in humans, it only included the known early visual cortex - what does this mean for the animate areas in dogs?

We thank the Reviewer for raising this point. Although the labels are the same, both EMG and mSSG are relatively large gyri, and the clusters revealed by each of the two analyses hardly overlap, with peak coordinates more than 12 mm apart for R EMG, and in different hemispheres for mSSG (but more than 11 mm apart even if projected on the same hemisphere). We will detail the differences and the overlaps in the revised submission.

The results section also lacks information and statistical evidence; for example, for the univariate region-of-interest (ROI) analysis (called response profiles) comparing activation strength towards each stimulus type, it is not reported if comparisons were significant or not, but the authors state they conducted t-tests. The authors describe that they created spheres on all peaks reported for the contrast animate > inanimate, but they only report results for the mid suprasylvian and occipital gyrus (e.g. caudal suprasylvian gyrus is missing).

We thank this Reviewer for catching these errors. The missing statistics will be provided in the revised manuscript. Also, we mistakenly named the peak in caudal suprasylvian gyrus occipital gyrus on the figure depicting the response profiles. This will also be corrected.

Furthermore, considering that the ROIs were chosen based on the contrast animate > inanimate stimuli, activation strength should only be compared between animate entities (i.e., dogs, humans, cats), while cars should not be reported (as this would be double dipping, after selecting voxels showing lower activation for that category).

We thank both Reviewers for raising this relevant point about potential double dipping. The aim of this analysis was to describe the relationship between the neural response elicited by the three animate stimulus classes, to show that the animacy-sensitive peaks are not the results of the standalone greater response to a single animate class. We conducted t-tests only to assess significant difference between these three animate conditions and no stats were performed or reported for any animate class vs. inanimate comparisons in these ROIs. In addition to providing the missing t-tests (comparing animate classes), we will present response profiles and corresponding statistics for a broad set of additional, independent ROIs, defined either anatomically or functionally by other studies in the revised version.

The descriptive data in Figure 3B (pending statistical evidence) suggests there were no strong differences in activation for the three species in dog and human animate areas. Thus, the ROI analysis appears to contradict findings from the binary analysis approach to investigate species preference, but the authors only discuss the results of the latter in support of their narrative for conspecific preference in dogs and do not discuss research from other labs investigating own-species preference.

Studying conspecific-preference was not the primary aim of this study. We only used our data to characterize the animate-sensitive regions from this aspect. The species-preference test provides an overall characterization of the entire animate-sensitive region, revealing a higher number of voxels with a maximal response to conspecific than other stimuli in dogs (and a similar tendency in humans), confirming previous evidence on neural conspecific preference in visual areas in both species. The response profiles presented so far describe only the ROIs around the main animate-sensitive peaks and, as the Reviewer points out, in most cases reveal no significant conspecific bias. We believe there is no contradiction here: the entire animate-sensitive region may weakly but still be conspecific-preferring, whereas the main animate-sensitive peaks are not; the centers of conspecific preference may be located elsewhere in the visual cortex and may be supported by mechanisms other than animacy-sensitivity. In the revised manuscript, we will elaborate more on this. Additionally, in response to other comments, and for a better and more coherent characterization of species preference (and animacy sensitivity) across the visual cortex, we will present response profiles for other, independently defined regions and explore conspecific-sensitivity in those additional regions as well. Furthermore, we will discuss related own-species preference literature in greater detail.

The authors also unnecessarily exaggerate novelty claims. Animate vs inanimate and own vs other species perceptions have both been investigated before in dogs (and humans), so any claims in that direction seem unsubstantiated - and also not needed, as novelty itself is not a sign of quality; what is novel, and a sign of theoretical advance besides the novelty, are as said the conceptual extension and replication of previous work.

We agree with this Reviewer regarding novelty claims in general, and we confirm that we had no intention to overstate the uniqueness of our results. We also did not mean to imply that this work would be the first one on animacy perception in dogs, which it obviously is not. But we understand that we could have been more explicit presenting our work as a conceptual extension and replication of previous works, and we are revising the wording of the discussion from this aspect.

Overall, more analyses and appropriate tests are needed to support the conclusions drawn by the authors, as well as a more comprehensive discussion of all findings.

We are thankful for all comments. We will revise the methods section to provide sufficient detail and ensure replicability; conduct additional analyses as detailed above; and provide a more comprehensive discussion of all findings.

Reviewer #2 (Public review):

Summary:

The manuscript reports an fMRI study looking at whether there is animacy organization in a non-primate, mammal, the domestic dog, that is similar to that observed in humans and non-human primates (NHPs). A simple experiment was carried out with four kinds of stimulus videos (dogs, humans, cats, and cars), and univariate contrasts and RSA searchlight analysis was performed. Previous studies have looked at this question or closely associated questions (e.g. whether there is face selectivity in dogs). The import of the present study is that it looks at multiple types of animate objects, dogs, humans, and cats, and tests whether there was overlapping/similar topography (or magnitude) of responses when these stimuli were compared to the inanimate reference class of cars. The main finding was of some selectivity for animacy though this was primarily driven by the dog stimuli, which did overlap with the other animate stimulus types, but far less so than in humans.

Strengths:

I believe that this is an interesting study in so far as it builds on other recent work looking at category-selectivity in the domestic dog. Given the limited number of such studies, I think it is a natural step to consider a number of different animate stimuli and look at their overlap. While some of the results were not wholly surprising (e.g. dog brains respond more selectively for dogs than humans or cats), that does not take away from their novelty, such as it is. The findings of this study are useful as a point of comparison with other recent work on the organization of high-level visual function in the brain of the domestic dog.

Weaknesses:

(1) One challenge for all studies like this is a lack of clarity when we say there is organization for "animacy" in the human and NHP brains. The challenge is by no means unique to the present study, but I do think it brings up two more specific topics.

First, one property associated with animate things is "capable of self-movement". While cognitively we know that cars require a driver, and are otherwise inanimate, can we really assume that dogs think of cars in the same way? After all, just think of some dogs that chase cars. If dogs represent moving cars as another kind of selfmoving thing, then it is not clear we can say from this study that we have a contrast between animate vs inanimate. This would not mean that there are no real differences in neural organization being found.

It was unclear whether all or some of the car videos showed them moving. But if many/most do, then I think this is a concern.

We thank this Reviewer for raising this relevant point about the potential animacy of cars for dogs and its implication for our results. Of note, two-thirds of our car stimuli showed a car moving (slow, accelerating, or fast). We acknowledge that these stimuli contained motionbased animacy cues, and in this regard, there was no clear difference between our animate and inanimate conditions, and possibly between some of the representations they elicited. However, our animate and inanimate stimuli differed in other key factors accounting for animacy organization, such as visual features including the presence of faces, bodies, body parts, postures, and certain aspects of biological motion. So we believe that this limitation does not compromise our main conclusions. We will elaborate on this point further in the revised discussion, also considering how dogs’ differential behavioral responses to cars and animate entities may provide additional insights in this regard.

Second, there is quite a lot of potential complexity in the human case that is worth considering when interpreting the results of this study. In the human case, some evidence suggests that animacy may be more of a continuum (Sha et al. 2015), which may reflect taxonomy (Connolly et al. 2012, 2016). However moving videos seem to be dominated more by signals relevant to threat or predation relative to taxonomy (Nastase et al. 2017). Some evidence suggests that this purported taxonomic organization might be driven by gradation in representing faces and bodies of animals based on their relative similarity to humans (Ritchie et al. 2021). Also, it may be that animacy organization reflects a number of (partially correlated) dimensions (Thorat et al. 2019, Jozwik et al. 2022). One may wonder whether the regions of (partial) overlap in animate responses in the dog brain might have some of these properties as well (or not).

We agree that it would be interesting to dissect which animacy-related factor(s) contribute to the observed animacy sensitivity in different regions, and although this was not the original aim of the study, we agree that we could have made better use of the variation in our stimuli to discuss this aspect. Specifically, some animacy features are shared by all three animate stimulus classes, namely the presence of biological motions, faces, and bodies. In contrast, animate classes differed in some other aspects, for example in how dogs perceived dogs, humans, and cats as social agents and in their potential behavioral goals towards them. It can therefore be argued that regions with two- and especially three-way overlapping activations are more probably involved in processing biological motion, face and body aspects, and non-overlapping ones the social agency- and behavioural goal-related aspects. In line with this, the shared animacy features are indeed ones that have been reported to be central in human animacy representation and that may have made the overlaps in human brain responses greater. We will provide a more detailed discussion of the results from this viewpoint in the revised manuscript.

(2) It is stated that previous studies provide evidence that the dog brain shows selectivity to "certain aspects of animacy". One of these already looked at selectivity for dog and human faces and bodies and identified similar regions of activity (Boch et al. 2023). An earlier study by Dilks et al. (2015), not cited in the present work (as far as I can tell), also used dynamic stimuli and did not suffer from the above limitations in choosing inanimate stimuli (e.g. using toy and scene objects for inanimate stimuli). But it only included human faces as the dynamic animate stimulus. So, as far as stimulus design, it seems the import of the present study is that it included a *third* animate stimulus (cats) and that the stimuli were dynamic.

We agree with this Reviewer that the findings of Dilks et al. (2015) are relevant to our study and have therefore cited them. However, the citation itself was imprecise and will be corrected in the revised manuscript.

(3) I am concerned that the univariate results, especially those depicted in Figure 3B, include double dipping (Kriegesorte et al. 2009). The analysis uses the response peak for the A > iA contrast to then look at the magnitude of the D, H, C vs iA contrasts. This means the same data is being used for feature selection and then to estimate the responses. So, the estimates are going to be inflated. For example, the high magnitudes for the three animate stimuli above the inanimate stimuli are going to inherently be inflated by this analysis and cannot be taken at face value. I have the same concern with the selectivity preference results in Figure 3E.

I think the authors have two options here. Either they drop these analyses entirely (so that the total set of analyses really mirrors those in Figure 4), or they modify them to address this concern. I think this could be done in one of two ways. One would be to do a within- subject standard split-half analysis and use one-half of the data for feature selection and the other for magnitude estimation. The other would be to do a between-subject design of some kind, like using one subject for magnitude estimation based on an ROI defined using the data for the other subjects.

We thank both Reviewers again for raising this important point about potential double dipping. We also thank this Reviewer for specific suggestions for split-half analyses – we agree that, had our original analyses involved double dipping, such a modification would be necessary. But, as we explained in our response above, this was not the case. Indeed, whereas we do visualize all four conditions in Fig. 3B, we only conducted t-tests to assess differences between the three animate conditions (the corresponding stats have been missing from the original manuscript but will be added during revision). So, importantly, we did not evaluate the magnitude of the D, H, C vs iA contrasts in any of the ROIs defined by animate-sensitive peaks; therefore, we believe that these analyses do not involve double dipping. This holds for the species preference results in Fig. 3E as well. We will clarify this in the revised manuscript. Of note, in response to a request by the other reviewer and to provide richer information about the univariate results, we will also provide response profiles and corresponding stats for a broad set of additional ROIs, defined either anatomically or functionally by other studies (e.g., Boch et al., 2023).

(4) There are two concerns with how the overlap analyses were carried out. First, as typically carried out to look at overlap in humans, the proportion is of overlapping results of the contrasts of interest, e.g, for face and body selectivity overlap (Schwarlose et al. 2006), hand and tool overlap (Bracci et al. 2012), or more recently, tool and food overlap (Ritchie et al. 2024). There are a number of ways of then calculating the overlap, with their own strengths and weaknesses (see Tarr et al. 2007). Of these, I think the Jaccard index is the most intuitive, which is just the intersection of two sets as a proportion of their union. So, for example, the N of overlapping D > iA and H > iA active voxels is divided by the total number of unique active voxels for the two contrasts. Such an overlap analysis is more standard and interpretable relative to previous findings. I would strongly encourage the authors to carry out such an analysis or use a similar metric of overlap, in place of what they have currently performed (to the extent the analysis makes sense to me).

We agree with this Reviewer that the Jaccard index is an intuitive and straightforward overlap measure. Importantly, for our overlap calculations we already use this measure (and a very similar one) – but we acknowledge that this was not clear from the original description. Specifically, for the multivariate overlap test, we used the Jaccard index exactly as described by this Reviewer. For the univariate overlap test, we use a very similar measure, with the only difference that there, to reference the search space, the intersection of specific animate-inanimate contrasts was divided by the total voxel number of animate-sensitive areas (which is highly similar to the union of the specific animate-inanimate contrasts). In the revised submission we will provide a more detailed explanation of the overlap calculations, making it explicit that we used the Jaccard index (and a variant of it).

Second, the results summarized in Figure 3A suggest multiple distinct regions of animacy selectivity. Other studies have also identified similar networks of regions (e.g. Boch et al. 2023). These regions may serve different functions, but the overlap analysis does not tell us whether there is overlap in some of these portions of the cortex and not in others. The overlap is only looked at in a very general sense. There may be more overlap locally in some portions of the cortex and not in others.

We thank this Reviewer for this comment, we agree that adding spatial specificity to these results will improve the manuscript. Therefore, during revision, we will assess the anatomical distribution of the overlap results, making use of a broad set of ROIs potentially relevant for animacy perception, defined either anatomically or functionally by other studies (e.g., Boch et al., 2023 for dogs).

(5) Two comments about the RSA analyses. First, I am not quite sure why the authors used HMAX rather than layers of a standardly trained ImageNet deep convolutional neural network. This strikes me also as a missed opportunity since many labs have looked at whether later layers of DNNs trained on object categorization show similar dissimilarity structures as category-selective regions in humans and NHPs. In so far as cross-species comparisons are the motivation here, it would be genuinely interesting to see what would happen if one did a correlation searchlight with the dog brain and layers of a DNN, a la Cichy et al. (2016).

We thank the Reviewer for this comment and suggestion. At the start of the project, HMAX was the most feasible model to implement given our time and expertise constrains. Additionally, the biologically motivated HMAX was also an appropriate choice, as it simulates the selective tuning of neurons in the primary visual cortex (V1) of primates, which is considered homologous with V1 in carnivores (Boch et al., 2024).

Although we agree that using DNNs have recently been extensively and successfully used to explore object representations and could provide valuable additional insights for dogs’ visual perception as well, we believe that adding a large set of additional analyses would stretch the frames of this manuscript, disproportionately shifting its focus from our original research question. Also, our experiment, designed with a different, more specific aim in mind, did not provide a large enough stimulus variety of animate stimuli for a general comparison of the cortical hierarchy underlying object representations in dog and human brains and thus our data are not an optimal starting point for such extensive explorations. Having said that, we are thankful for this Reviewer for the idea and will consider using a DNN to uncover dog’ visual cortical hierarchy in future studies with a better suited stimulus set. Furthermore, in accordance with eLife’s data-sharing policies, we will make the current dataset publicly available so further hypothesis and models can be tested.

Second, from the text is hard to tell what the models for the class- and categoryboundary effects were. Are there RDMs that can be depicted here? I am very familiar with RSA searchlight and I found the description of the methods to be rather opaque. The same point about overlap earlier regarding the univariate results also applies to the RSA results. Also, this is again a reason to potentially compare DNN RDMs to both the categorical models and the brains of both species.

In the revised manuscript we will provide a more detailed explanation of the methods used to determine class- and category-boundary effects. In short, the analysis we performed here followed Kriegeskorte et al. (2008), and the searchlight test looked for regions in which between-class/category differences were greater than within-class/category differences. We will also include RDMs. Additionally, we will provide anatomical details for the overlap results for RSA, just as for the univariate results, using the same independently defined broad set of ROIs, defined either anatomically or functionally by other studies (e.g., Boch et al., 2023 for dogs).

(6) There has been emphasis of late on the role of face and body selective regions and social cognition (Pitcher and Ungerleider, 2021, Puce, 2024), and also on whether these regions are more specialized for representing whole bodies/persons (Hu et al. 2020, Taubert, et al. 2022). It may be that the supposed animacy organization is more about how we socialize and interact with other organisms than anything about animacy as such (see again the earlier comments about animacy, taxonomy, and threat/predation). The result, of a great deal of selectivity for dogs, some for humans, and little for cats, seems to readily make sense if we assume it is driven by the social value of the three animate objects that are presented. This might be something worth reflecting on in relation to the present findings.

We thank the Reviewer for this suggestion. The original manuscript already discussed how motion-related animacy cues involved in social cognition may explain that animacysensitive regions reported in our study extend beyond those reported previously and also the role of biological motion in the observed across-species differences. This discussion of the role of visual diagnostic features and features that involved in perceiving social agents will be extended in the revised discussion, also in response to the first comment of this Reviewer, to reflect on how social cognition-related animacy cues may have affected our results in dogs.

eLife Assessment

This valuable study provides new insights into the synchronization of ripple oscillations in the hippocampus, both within and across hemispheres. Using carefully designed statistical methods, it presents convincing evidence that synchrony is significantly higher within a hemisphere than across. However, further controlling for potential confounds related to differences in animal behavior will help clarify whether this effect is influenced by memory processing. This study will be of interest to neuroscientists studying the hippocampus and memory.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors analyze electrophysiological data recorded bilaterally from the rat hippocampus to investigate the coupling of ripple oscillations across the hemispheres. Commensurate with the majority of previous research, the authors report that ripples tend to co-occur across both hemispheres. Specifically, the amplitude of ripples across hemispheres is correlated but their phase is not. These data corroborate existing models of ripple generation suggesting that CA3 inputs (coordinated across hemispheres via the commisural fibers) drive the sharp-wave component while the individual ripple waves are the result of local interactions between pyramidal cells and interneurons in CA1.

Strengths:

The manuscript is well-written, the analyses well-executed and the claims are supported by the data.

Weaknesses:

One question left unanswered by this study is whether information encoded by the right and left hippocampi is correlated.

Reviewer #2 (Public review):

Summary:

The authors completed a statistically rigorous analysis of the synchronization of sharp-wave ripples in the hippocampal CA1 across and within hemispheres. They used a publicly available dataset (collected in the Buzsaki lab) from 4 rats (8 sessions) recorded with silicon probes in both hemispheres. Each session contained approximately 8 hours of activity recorded during rest. The authors found that the characteristics of ripples did not differ between hemispheres, and that most ripples occurred almost simultaneously on all probe shanks within a hemisphere as well as across hemispheres. The differences in amplitude and exact timing of ripples between recording sites increased slightly with the distance between recording sites. However, the phase coupling of ripples (in the 100-250 Hz range), changed dramatically with the distance between recording sites. Ripples in opposite hemispheres were about 90% less coupled than ripples on nearby tetrodes in the same hemisphere. Phase coupling also decreased with distance within the hemisphere. Finally, pyramidal cell and interneuron spikes were coupled to the local ripple phase and less so to ripples at distant sites or the opposite hemisphere.

Strengths:

The analysis was well-designed and rigorous. The authors used statistical tests well suited to the hypotheses being tested, and clearly explained these tests. The paper is very clearly written, making it easy to understand and reproduce the analysis. The authors included an excellent review of the literature to explain the motivation for their study.

Weaknesses:

The authors state that their findings (highly coincident ripples between hemispheres), contradict other findings in the literature (in particular the study by Villalobos, Maldonado, and Valdes, 2017), but fail to explain why this large difference exists. They seem to imply that the previous study was flawed, without examining the differences between the studies.

The paper fails to mention the context in which the data was collected (the behavior the animals performed before and after the analyzed data), which may in fact have a large impact on the results and explain the differences between the current study and that by Villalobos et al. The Buzsaki lab data includes mice running laps in a novel environment in the middle of two rest sessions. Given that ripple occurrence is influenced by behavior, and that the neurons spiking during ripples are highly related to the prior behavioral task, it is likely that exposure to novelty changed the statistics of ripples. Thus, the authors should analyze the pre-behavior rest and post-behavior rest sessions separately. The Villalobos et al. data, in contrast, was collected without any intervening behavioral task or novelty (to my knowledge). Therefore, I predict that the opposing results are a result of the difference in recent experiences of the studied rats, and can actually give us insight into the memory function of ripples.

In one figure (5), the authors show data separated by session, rather than pooled. They should do this for other figures as well. There is a wide spread between sessions, which further suggests that the results are not as widely applicable as the authors seem to think. Do the sessions with small differences between phase coupling and amplitude coupling have low inter-hemispheric amplitude coupling, or high phase coupling? What is the difference between the sessions with low and high differences in phase vs. amplitude coupling? I noticed that the Buzsaki dataset contains data from rats running either on linear tracks (back and forth), or on circular tracks (unidirectionally). This could create a difference in inter-hemisphere coupling, because rats running on linear tracks would have the same sensory inputs to both hemispheres (when running in opposite directions), while rats running on a circular track would have different sensory inputs coming from the right and left (one side would include stimuli in the middle of the track, and the other would include closer views of the walls of the room). The synchronization between hemispheres might be impacted by how much overlap there was in sensory stimuli processed during the behavior epoch.

The paper would be a lot stronger if the authors analyzed some of the differences between datasets, sessions, and epochs based on the task design, and wrote more about these issues. There may be more publicly available bi-hemispheric datasets to validate their results.

eLife Assessment

In this important study, the authors employed state-of-the-art biochemistry, cryo-EM, and HDX mass spec approaches to study the formation of the binary Uba7-UBE2L6 and ternary UBA7-UBE2L6-ISG15 complexes. The results established mechanisms by which UBA7 and UBE2L6 form disulfide bonds, disrupting the ISG15 transfer cascade. While the biochemical and structural experiments are largely convincing, the mechanism under in vivo conditions remains unclear, due to the limited use of a single E2 enzyme. The authors need to repeat their experiments with a representative panel of human E2 enzymes.

Reviewer #1 (Public review):

Summary:

Chen and colleagues describe mechanisms by which UBA7 and UBE2L6 form disulfide bonds, disrupting the ISG15 transfer cascade. As other similar structures are currently available, the authors further note that the spontaneous formation of this disulfide suggests that it is a potential regulatory mechanism. Demonstrating that this mechanism occurs and is modulated in cells would greatly improve the impact of their work.

Strengths:

The various biochemical and structural experiments are largely convincing.

Weaknesses:

(1) The main point of the paper is that this covalent complex could occur and is potentially regulated in cells is limited. The authors even show an experiment in cells where this complex is formed by expressing UBE2L6-V5 and GFP-UBA7, awkwardly referenced in the discussion.

The authors should consider attempting an experiment with endogenous proteins and either modulate the formation of this complex in different cellular conditions or downplay this part of their story. For example, this sentence, "This redox-sensitive complex implies a link between oxidative stress and regulation of the immune response, highlighting a potential therapeutic target for modulating immune reactions arising from infections and inflammatory conditions." is in the abstract and should be excluded or rephrased considering the lack of cellular data.

Also, their one-cell-based experiment is shown in the discussion. This should be in the results as is standard practice but also repeated. It appears that the reduced lanes don't seem to have GFP or the GFP-UBA7. Without those controls, this experiment seems incomplete.

(2) Their intro sets up the paper to explain the disulfide formation they see in Figure 1, but a more fitting experiment would be to look at the disulfide formation between UBA7 and UBE2L6 at different pHs. It would nicely supplement the biochemical pKa data as this reaction is their focal point.

(3) While the biochemical data is extensive, it is not concise or easily accessible to a broad readership. The authors should try to clarify and simplify the text overall. Furthermore, many figure callouts are missing, interfering with the clarity of the text.

Minor

(1) Because the experiments are pKa dependent, knowing what buffers the proteins were finished in (final SEC purification step) is important. Similarly - for all assays, the buffers were not reported (SEC-MALS, biochemical assays).

(2) While the CBB and fluorescent gel assays look convincing, more controls are needed for their SEC experiments (Figure 1d), particularly because the authors definitively say the binding is because of S-S bonds. Using a reducing buffer like TCEP or DTT or their catalytic mutants to show reduced co-migration would be helpful. This is even more important given the reported high affinities between UBA7/UBE2L6 in Figure 6.

(3) Based on the data presented, it is unclear that the kinetic values are taken within initial velocity regimes. Some data in the supplement showing that the single time points represent initial velocities would be appreciated.

(4) As stated, "Previous experiments reveal an intriguing anomaly during the UBA7-UBE2L6-ISG15 thioester transfer reaction. Despite adding more ISG15 and UBE2L6, the level of UBE2L6~ISG15 remained the same." This experiment should be shown or the statement removed.

(5) Similarly, "Forty human E2 enzymes are classified in the InterProdatabase (https://www.ebi.ac.uk/interpro/), with the majority interacting with UBA1, whereas UBE2L6 and UBE2Z exclusively interact with UBA7 and UBA6, respectively." Is missing a reference.

Reviewer #2 (Public review):

Summary:

Chen et al. describe by different techniques that UBA7 and UBE2L6 readily form a complex that is covalently linked by a disulfide bond involving the active site cysteines of UBA6 and UBE2L6. Furthermore, they determined cryo-EM structures of the disulfide-linked UBY7-UBE2L6 complex in the absence and presence of ISG15. They propose that this disulfide-linked complex blocks ISGylation by temporarily rendering UBA7 inactive.

Strengths:

The authors employ a wide variety of techniques to study the formation of the binary Uba7-UBE2L6 and ternary UBA7-UBE2L6-ISG15 complexes including the structural characterization of the two complexes by cryo-EM. Despite the shortcomings (see below), the authors provide numerous valuable data that characterize the first steps of the ISGylation pathway, namely the activation of ISG15 and its transfer to UBE2L6.

Weaknesses:

(1) The authors correctly state that "Immune responses often entail the generation or reactive oxygen species, antioxidant defense mechanisms, and redox signaling" (1st sentence of 3rd paragraph in the Introduction). Based on the data presented in this study these cellular responses should lead to the formation of the covalent UBA7-UBE2L6. Since this complex renders UBA7 inactive, thus preventing it from initiating the ISGylation cascade in response to viral infections, the underlying cellular logic of complex formation remains a mystery.

The bulk of their work describes in vitro experiments, which will certainly not reflect the in vivo situation and hence one cannot rule out that this complex will not form inside cells. The authors have also observed this complex in HEK293T cells, however, this involved overexpression of both proteins and one can thus not rule out that the disulfide-linked complex will not form at physiological protein levels. Furthermore, this cellular model appears not to be a suitable system.

(2) The authors carried out a comparative analysis of E1-E2 disulfide bond formation with UBA1, the major activating enzyme for ubiquitin, and UBE2L3, a ubiquitin-specific E2. The choice of UBE2L3 was motivated by its close relationship to UBE2L6. From these studies, the authors conclude that UBA1 does not form the corresponding complex. Given that there are over 30 ubiquitin-specific E2s this conclusion does not rest on a very solid basis, since, as demonstrated for example in this study (PMID: 22949505), at least yeast Uba1 forms a disulfide-linked complex with Cdc34. Another study documenting the formation of a disulfide-linked complex between Uba1 and an E2 enzyme, in this case, Rad6, (PMID: 35613580) is even cited by the authors. If the authors want to make the argument that Uba1 does not form corresponding E1-E2 complexes, they need to repeat their experiments with a representative panel of human E2 enzymes and the two enzymes employed in the aforementioned studies (Cdc34 and Rad6) or, more precisely, their human counterparts represent obvious starting points. Depending on the outcome of these studies the experiments with the CCL mutants need to be revisited.

Reviewer #3 (Public review):

Summary:

In this manuscript, "Elucidating the mechanism underlying UBA7-UBE2L6 disulfide complex formation", Chen et al. describe the mechanism of spontaneous disulfide bond formation between the active site cysteines of UBA7 and UBE2L6. Employing state-of-the-art biochemistry, cryo-EM, and HDX mass spec approaches, the authors provide insights into how this mechanism occurs in UBA7/UBE2L6 but not in related ubiquitin enzymes. A central conclusion of the study is that the length of the catalytic cysteine loop (CCL) in UBA7 is insufficient to block access to the E1's catalytic cysteine, thereby facilitating UBE2L6 disulfide formation. In contrast, the CCL of UBA1 is sufficiently long and shields its catalytic cysteine, preventing access to the Ub E2 enzymes. In addition to the CCL, the authors also show that UBA7's specificity and strong binding affinity for UBE2L6 help promote this disulfide-linked E1-E2 complex.

Strengths:

The data within in manuscript is interesting and significantly contributes to our understanding of the mechanisms of the ISG15 conjugation pathway. Moreover, the biochemical and structural experiments were performed at an exceptionally high level and the data throughout the manuscript is convincing.

Weaknesses:

It is not clear whether this regulatory mechanism occurs in a biological context (e.g., during IFN signaling or oxidative stress). However, this weakness is somewhat offset by the last experiment of the manuscript which demonstrates the existence of UBA7-UBE2L6 disulfide complex formation in cells under overexpression conditions. If the authors could expand upon this finding, as outlined below it would further improve their study.

eLife Assessment

In this important quantitative study of HIV-1 evolution in humans and rhesus macaques, selection coefficients are inferred at scale over the HIV genome. Selection coefficients are similar in humans and macaques, providing convincing evidence that these coefficients are representative of the fitness landscapes of these viruses within hosts. This work should be of interest to the community working on quantitative evolution and fitness landscape inference, and the finding that rapid fitness gains in the HIV population predict bNAb emergence has implications for HIV vaccine design.

Reviewer #1 (Public review):

Summary:

The present work studies the coevolution of HIV-1 and the immune response in clinical patient data. Using the Marginal Path Likelihood (MPL) framework, they infer selection coefficients for HIV mutations from time-series data of virus sequences as they evolve in a given patient.

Strengths:

The authors analyze data from two human patients, consisting of HIV population sequence samples at various points in time during the infection. They infer selection coefficients from the observed changes in sequence abundance using MPL. Most beneficial mutations appear in viral envelop proteins. The authors also analyze SHIV samples in rhesus macaques, and find selection coefficients that are compatible with those found in the corresponding human samples.

The manuscript is well-written and organized.

Weaknesses:

The MPL method used by the authors considers only additive effects of mutations, thus ignoring epistasis.

Although the evolution of broadly neutralizing antibodies (bnAbs) is a motivating question in the introduction and discussion sections (and the title), the relevance of the analysis and results to better understanding how bnAbs arise is not clear. The only result presented in direct connection to bnAbs is Figure 6.

Questions or suggestions for further discussion:

I list here a number of points for which I believe the paper would benefit if additional discussion/results were included.

The MPL method used by the authors considers only additive effects of mutations, thus ignoring epistasis. In Sohail et al (2022) MBE 39(10), p. msac199 (https://doi.org/10.1093/molbev/msac199) an extension of MPL is developed allowing one to infer epistasis. Can the authors comment on why this was not attempted here?

I presume one possible reason is that epistasis inference requires considerably more computational effort (and more data). However, since the authors find most beneficial mutations occurring in Env, perhaps restricting the analysis to Env genes only (e.g. the trimer shown in Figure 2) can lead to tractable inference of epistasis within this segment (instead of the full genome).

Do the authors find correlations in the inferred selection coefficients of the two samples CH505 and CH848? I could not find any discussion of this in the manuscript. Only correlations between Humans and RM are discussed.

Reviewer #2 (Public review):

Summary

This paper combines a biological topic of interest with the demonstration of important theoretical/methodological advances. Fitness inference is the foundation of the quantitative analysis of adapting systems. It is a hard and important problem and this paper highlights a compelling approach (MPL) first presented in (1) and refined in (2), roughly summarized in equation 12.

(1) Sohail, M. S., Louie, R. H., McKay, M. R. & Barton, J. P. Mpl resolves genetic linkage in fitness inference from complex evolutionary histories. Nature biotechnology 39, 472-479 (2021).<br /> (2) Shimagaki, K. & Barton, J. P. Bézier interpolation improves the inference of dynamical models from data. Physical Review E 107, 024116 (2023).

The authors find that positive selection shapes the variable regions of env in shared patterns across two patient donors. The patterns of positive selection are interesting in and of themselves, they confirm the intuition that hyper-variation in env is the result of immune evasion rather than a broadly neutral landscape (flatness). They show that the immune evasion patterns due to CD8 T and naive B-cell selection are shared across patients. Furthermore, they suggest that a particular evolutionary history (larger flux to high fitness states) is associated with bNAb emergence. Mimicking this evolutionary pattern in vaccine design may help us elicit bNAbs in patients in the future.

There is a lot of information to be found in the full fitness landscape of env. The enormous strength of reversion-to-consensus in the patterns is a known pattern of HIV post-infection populations but they are nicely quantified here. Agreement between SHIV and HIV evolution is shown. They find selection is larger for autologous antibodies than the bNAbs themselves (perhaps bNAbs are just too small a component of the host response to drive the bulk of selection?), and that big fitness increases precede antibody breadth in rhesus macaques, suggesting that this fitness increase is the immune challenge required to draw forth a bNAb. This is all of high interest to HIV researchers.

Strength of evidence

One limitation is, of course, that the fitness model is constant in time when the immune challenge is variable and changing. This simplification may complicate some interpretations.

Equation 12 in the methods is really a beautiful tool because it is so simple, but accounts for linkage and can be solved precisely even in the presence of detailed mutational and selection models. However, the reliance on incomplete observations of the frequency leads to complications that must be carefully (re)addressed here.

For instance, the consistent finding of strong selection in hypervariable regions is biologically intuitive but so striking, that I worry that it might be the result of a bias for selection in high entropy regions. Mutational and covariance terms in equation 12 might be underestimated, due to finite sampling effect in highly diverse populations. Sampling effects lead to zeros in x(t) when actual frequency zeros might be rare at the population sizes of HIV viral loads and mutation rates. Both mutational flux and C underestimation will bias selection upward in eq. 12. The prior papers (1) and (2) seem to show robustness to finite sampling effects, but, again, more care needs to be shown that this robustness transfers to the amino acid inference under these conditions. That synonymous sites are rarely selected for in the nucleotide level is a good sign, and it may be a matter of simply fully explaining the amino-acid level model.

Uncertainty propagates to the later parts of the paper, eg. HIV and SIV shared patterns might be the result of shared biases in the method application. However, this worry does not extend to the apples-to-apples comparison of fitness trajectories across individuals (Figures 5 and 6) which I think are robust (for these sample sizes). The timing evidence is slightly weakened by the fact that bNAb detection is different from bNAb presence and the possibility that fitness increases occurred after the bNAbs appeared remains. Still, their conclusion is plausible and fits in with the other observations which form a coherent and compelling picture.

Overall this is a convincing paper, part of a larger admirable project of accurately inferring complete fitness landscapes.

Reviewer #3 (Public review):

Summary:

Shimagaki et al. investigate the virus-antibody coevolutionary processes that drive the development of broadly neutralizing antibodies (bnAbs). The study's primary goal is to characterize the evolutionary dynamics of HIV-1 within hosts that accompany the emergence of bnAbs, with a particular focus on inferring the landscape of selective pressures shaping viral evolution. To assess the generality of these evolutionary patterns, the study extends its analysis to rhesus macaques (RMs) infected with simian-human immunodeficiency viruses (SHIV) incorporating HIV-1 Env proteins derived from two human individuals.

Strengths:

A key strength of the study is its rigorous assessment of the similarity in evolutionary trajectories between humans and macaques. This cross-species comparison is particularly compelling, as it quantitatively establishes a shared pattern of viral evolution using a sophisticated inference method. The finding that similar selective pressures operate in both species adds robustness to the study's conclusions and suggests broader biological relevance.

Weaknesses:

However, the study has some limitations. The most significant weakness is that the authors do not sufficiently discuss the implications of the observed similarities. While the identification of shared evolutionary patterns (e.g., Figure 5) is intriguing, the study would benefit from a more explicit discussion of what these findings mean for instance, in the context of HIV vaccine design, immunotherapy, or fundamental viral-host interactions. Even speculative interpretations could provide valuable insights into the broader significance of these results.

A secondary, albeit less critical, limitation is the placement of methodological details in the Supplementary Information. While it is understandable that the authors focus on results in the main text - especially since the methodology is not novel and has been previously described in earlier publications - some readers might benefit from a more thorough presentation of the method within the main paper.

Conclusions:

Overall, the study presents a compelling analysis of HIV-1 evolution and its parallels in SHIV-infected macaques. While the quantitative comparison between species is a notable contribution, a deeper discussion of its broader implications would strengthen the paper's impact.

eLife Assessment

The authors attempt to identify which patients with benign lesions will progress to cancer using a liquid biomarker. Although the study is valuable, the evidence provided for the liquid biopsy EV miRNA signature developed based on radiomics features is incomplete. This is because the data are derived from discrepant sample sets and the description of the clinical characteristics of the samples enrolled in the study needs to be improved.

Reviewer #1 (Public review):

Summary:

The manuscript by Shi et al, has utilized multiple imaging datasets and one set of samples for analyzing serum EV-miRNAs & EV-RNAs to develop an EV miRNA signature associated with disease-relevant radiomics features for early diagnosis of pancreatic cancer. CT imaging features (in two datasets (UMMD & JHC and WUH) were derived from pancreatic benign disease patients vs pancreatic cancer cases), while circulating EV miRNAs were profiled from samples obtained from a different center (DUH). The EV RNA signature from external public datasets (GSE106817, GSE109319, GSE113486, GSE112264) were analyzed for differences in healthy controls vs pancreatic cancer cases. The miRNAs were also analyzed in the TCGA tissue miRNA data from normal adjacent tissue vs pancreatic cancer.

Strengths:

The concept of developing EV miRNA signatures associated with disease relevant radiomics features is a strength.

Weaknesses:

While the overall concept of developing EV miRNA signature associated with radiomics features is interesting, the findings reported are not convincing for the reasons outlined below:

(1) Discrepant datasets for analyzing radiomic features with EV-miRNAs: It is not justified how CT images (UMMD & JHC and WUH) and EV-miRNAs (DUH) on different subjects and centers/cohorts shown in Figures 1 &2 were analyzed for association. It is stated that the samples were matched according to age but there is no information provided for the stages of pancreatic cancer and the kind of benign lesions analyzed in each instance.

(2) The study is focused on low-abundance miRNAs with no adequate explanation of the selection criteria for the miRNAs analyzed.

(3) While EV-miRNAs were profiled or sequenced (not well described in the Methods section) with two different EV isolation methods, the authors used four public datasets of serum circulating miRNAs to validate the findings. It would be better to show the expression of the three miRNAs in the additional dataset(s) of EV-miRNAs and compare the expressions of the three EV-miRNAs in pancreatic cancer with healthy and benign disease controls.

(4) It is not clear how the 12 EV-miRNAs in Figure 4C were identified.

(5) Box plots in Figures 4D-F and G-I of three miRNAs in serum and tissue should show all quantitative data points.

(6) What is the GBM model in Figure 5?

(7) What are the AUCs of individual EV-miRNAs integrated as a panel of three EV-miRNAs?

(8) The authors could have compared the performance of CA19-9 with that of the three EV-miRNAs.

(9) How was the diagnostic performance of the three EV-miRNAs in the two molecular subtypes identified in Figure 6&7? Do the C1 & C2 clusters correlate with the classical/basal subtypes, staging, and imaging features?

Reviewer #2 (Public review):

Summary:

This study investigates a low abundance microRNA signature in extracellular vesicles to subtype pancreatic cancer and for early diagnosis. There are several major questions that need to be addressed. Numerous minor issues are also present.

Strengths:

The authors did a comprehensive job with numerous analyses of moderately sized cohorts to describe the clinical and translational significance of their miRNA signature.

Weaknesses:

There are multiple weaknesses of this study that should be addressed:

(1) The description of the datasets in the Materials and Methods lacks details. What were the benign lesions from the various hospital datasets? What were the healthy controls from the public datasets? No pancreatic lesions? No pancreatic cancer? Any cancer history or other comorbid conditions? Please define these better.

(2) It is unclear how many of the controls and cases had both imaging for radiomics and blood for biomarkers.

(3) The authors should define the imaging methods and protocols used in more detail. For the CT scans, what slice thickness? Was a pancreatic protocol used? What phase of contrast is used (arterial, portal venous, non-contrast)? Any normalization or pre-processing?

(4) Who performed the segmentation of the lesions? An experienced pancreatic radiologist? A student? How did the investigators ensure that the definition of the lesions was performed correctly? Raidomics features are often sensitive to the segmentation definitions.

(5) Figure 1 is full of vague images that do not convey the study design well. Numbers from each of the datasets, a summary of what data was used for training and for validation, definitions of all of the abbreviations, references to the Roman numerals embedded within the figure, and better labeling of the various embedded graphs are needed. It is not clear whether the graphs are real results or just artwork to convey a concept. I suspect that they are just artwork, but this remains unclear.

(6) The DF selection process lacks important details. Please reference your methods with the Boruta and Lasso models. Please explain what machine learning algorithms were used. There is a reference in the "Feature selection.." section of "the model formula listed below" but I do not see a model formula below this paragraph.

(7) In Figure 2, more quantitative details are needed. How are patients dichotomized into non-obese and obese? What does alcohol/smoking mean? Is it simply no to both versus one or the other as yes? These two risk factors should be separated and pack years of smoking should be reported. The details of alcohol use should also be provided. Is it an alcohol abuse history? Any alcohol use, including social drinking? Similarly, "diabetes" needs to be better explained. Type I, type II, type 3c? P values should be shown to demonstrate any statistically significant differences in the proportions of the patients from one dataset to another.

(8) In the section "Different expression radiomic features between pancreatic benign lesions and aggressive tumors", there is a reference to "MUJH" for the first time. What is this? There is also the first reference to "aggressive tumors" in the section. Do the authors just mean the cases? Otherwise there is no clear definition of "aggressive" (vs. indolent) pancreatic cancer. This terminology of tumor "aggressiveness" either needs to be removed or better defined.

(9) Figure 3 needs to have the specific radiomic features defined and how these features were calculated. Labeling them as just f1, f2, etc is not sufficient for another group to replicate the results independently.

(10) It is not clear what Figure 4A illustrates as regards model performance. What do the different colors represent, and what are the models used here? This is very confusing.

(11) Figure 5 shows results for many more model runs than the described 10, please explain what you are trying to convey with each row. What are "Test A" and "Test B"? There is no description in the manuscript of what these represent. In the figure caption, there is a reference to "our center data" which is not clear. Be more specific about what that data is.

(12) Figure 6 describes the subtypes identified in this study, but the authors do not show a multi-variable cox proportional hazards model to show that this subtype classification independently predicts DFS and OS when incorporating confounding variables. This is essential to show the subtypes are clinically relevant. In particular, the authors need to account for the stage of the patients, and receipt of chemotherapy, surgery, and radiation. If surgery was done, we need to know whether they had R1 or R0 resection. The details about the years in which patients were included is also important.

(13) How do these subtypes compare to other published subtypes?

Reviewer #3 (Public review):

Summary:

The authors appear to be attempting to identify which patients with benign lesions will progress to cancer using a liquid biomarker. They used radiomics and EV miRNAs in order to assess this.

Strengths:

It is a strength that there are multiple test datasets. Data is batch-corrected. A relatively large number of patients is included. Only 3 miRNAs are needed to obtain their sensitivity and specificity scores.

Weaknesses:

This manuscript is not clearly written, making interpretation of the quality and rigor of the data very difficult. There is no indication from the methods that the patients in their cohorts who are pancreatic cancer patients (from the CT images) had prior benign lesions, limiting the power of their analysis. The data regarding the cluster subtypes is very confusing. There is no discussion or comparison if these two clusters are just representing classical and basal subtypes (which have been well described).

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Dad et al. explored the roles of cytosolic carboxypeptidase 5（CCP5）in the development of ependymal multicilia in the brain. CCP family are erasers of polyglutamylation of ciliary-axoneme microtubules. The authors generated a new mutant mouse of Agbl5 gene, which encodes CCP5, with deletion of its N-terminus and partial carboxypeptidase (CP) domain (named AGBL5M1/M1).

Strengths:

The mutant mice revealed lethal hydrocephalus due to degeneration of ependymal multicilia. Interestingly, this is in contrast with the phenotype of Agbl5 mutants with disruption solely in the CP domain of CCP5 (named AGBL5M2/M2) that did not develop hydrocephalus despite increased glutamylation levels in ependymal cilia as observed for AGBL5M1/M1 mutants. The study has been well-performed and the findings suggest a unique function of the N-domain of CCP5 in ependymal multicilia stability.

Weaknesses:

The content of this article is relatively descriptive and lacks molecular insights.

We thank the Reviewer’s positive comments. To address the molecular insights of the dysregulated planar cell polarity (PCP) in Agbl5^M1/M1 ependyma, we are planning to further assess the microtubule polarization and the expression/localization of PCP core proteins in ependymal cells. We also plan to quantify the intensity of actin networks around BB patches to better understand to which extent it is affected in the ependyma of the mutants and contributes to the impaired stability of BBs (Please see below).

We will also assess whether Agbl5 commonly functions in multiciliated cells of other organs.

Reviewer #2 (Public review):

Summary:

This study analyzed the consequences of Agbl5 mutation on ependymal cell development and function. The authors first characterize their mutant mouse line reporting a reduced lifespand and severe hydrocephalus. Next, they report a defect in ependymal cell cilia number and motility. They provide evidence for impaired basal body organisation and cilia glutamylation.

Strengths:

Description of a mutant mouse which implicates Cytosolic Carboxypeptidase 5 (the product of Agbl5 gene) for proper ependymal cells.

Weaknesses:

Description of phenotype is incomplete:

We thank the Reviewer’s constructive comments. We agree that more quantitative analysis of the phenotypes in Agbl5^M1/M1 will strengthen this study.

- Figure 3G - the sequence from the movie is not really informative. Providing beating frequencies as quantification of the data would be more informative.

We agree that quantification of the cilia beating frequencies and directions in these experiments will be more informative.

- Figure 3 - the quantification of actin network would strengthen the message.

We agree with the Reviewers. We will quantify the total intensity of actin around BB patch and the total intensity of actin per BB to determine to which extent the actin networks are affected in Agbl5^M1/M1 ependymal cells.

- Lines 219 -220 - the authors conclude “Taken together, in Agbl5^M1/M1 ependymal cells, the expression of genes promoting multiciliogenesis were not impaired but certain proteins associated with differentiated ependymal cells are not properly expressed”. However, they do not assess gene but protein expression (IF). In addition, their quantification shows differences in the number of FoxJ1 positive cells which indeed is an impaired expression.

We will clarify this statement.

- Microtubules are involved in the local organization of ciliary basal bodies (see Werner et al., Vladar et al.,2011; Boutin et al., 2014). It would be interesting for the authors to check whether the subapical network of microtubules is glutamylated or not during ependymal cell differentiation and how this network is affected in their mutants.

We thank the Reviewer’s suggestion. We agree this is an interesting point to look at. We will assess the glutamylation status of the subapical microtubule networks in differentiating ependymal cells and whether they are affected in the mutants.

- Showing the data mentioned in the discussion on Cep110 would be a nice addition to the paper.

These results will be provided.

- Line 354: "The latter serves as a component of tissue polarity that is required for asymmetric PCP protein localization in each cell (Boutin et al., 2014; Vladar et al., 2012)." The cited reference did not demonstrate that this microtubule network is required for asymmetric PCP localization.

We thank the Reviewer for critical reading. We will correct the citation.

Reviewer #3 (Public review):

Summary:

The authors developed a new Agbl5 KO allele, extending the deletion to the N-terminus of CCP5 to explore its function in mouse ependymal cells.

Strengths:

They show that the KO mice exhibit severe hydrocephalus due to disorganized and mislocated basal bodies. Additionally, they present evidence of both impaired beating coordination and a reduction in ciliary beating.

Weaknesses:

The manuscript is well-written but lacks specific interpretations of the results presented. Further experiments are needed to be fully convincing.

We thank the Reviewer’s comments. We plan to conduct the following experiments to strengthen this study.

(1) Quantify the intensity of actin staining around BB patches and its intensity relative to the number of BBs to assess to which extent the actin networks in Agbl5^M1/M1 ependymal cells are affected (please refer to the above response to the comments of Reviewer 2#).

(2) Co-stain tdTomato with cell specific markers to strengthen the spatial expression of tdTomato.

(3) Seek proper antibodies to determine the correlation between signals of GT335 and Ac-Tub in ependymal multicilia of Agbl5^M1/M1 mice.

(4) Quantitatively compare the size of ependymal cells in the wild-type and Agbl5^M1/M1 mice to address whether there is a consequence of possible dysfunction of primary cilia in the precursors of ependymal cells in the mutants. If so, we will further analyze how the primary cilia in the precursors of ependymal cells are affected in the mutants.

(5) Address whether the rotational polarity is affected in the Agbl5^M1/M1 mutant mice.

eLife Assessment

This is a valuable study that explores the function of CCP5 in mouse ependymal cells. The methods, data, and analyses broadly support the claims. However, the study is incomplete as it stands. Minor weaknesses remain and the authors may wish to address them.

Reviewer #1 (Public review):

Summary:

Dad et al. explored the roles of cytosolic carboxypeptidase 5（CCP5）in the development of ependymal multicilia in the brain. CCP family are erasers of polyglutamylation of ciliary-axoneme microtubules. The authors generated a new mutant mouse of Agbl5 gene, which encodes CCP5, with deletion of its N-terminus and partial carboxypeptidase (CP) domain (named AGBL5M1/M1).

Strengths:

The mutant mice revealed lethal hydrocephalus due to degeneration of ependymal multicilia. Interestingly, this is in contrast with the phenotype of Agbl5 mutants with disruption solely in the CP domain of CCP5 (named AGBL5M2/M2) that did not develop hydrocephalus despite increased glutamylation levels in ependymal cilia as observed for AGBL5M1/M1 mutants. The study has been well-performed and the findings suggest a unique function of the N-domain of CCP5 in ependymal multicilia stability.

Weaknesses:

The content of this article is relatively descriptive and lacks molecular insights.

Reviewer #2 (Public review):

Summary:

This study analyzed the consequences of Agbl5 mutation on ependymal cell development and function. The authors first characterize their mutant mouse line reporting a reduced lifespand and severe hydrocephalus. Next, they report a defect in ependymal cell cilia number and motility. They provide evidence for impaired basal body organisation and cilia glutamylation.

Strengths:

Description of a mutant mouse which implicates Cytosolic Carboxypeptidase 5 (the product of Agbl5 gene) for proper ependymal cells.

Weaknesses:

Description of phenotype is incomplete:

- Figure 3G - the sequence from the movie is not really informative. Providing beating frequencies as quantification of the data would be more informative.

- Figure 3 - the quantification of actin network would strengthen the message.

- Lines 219 -220 - the authors conclude «Taken together, in Agbl5M1/M1 ependymal cells, the expression of genes promoting multiciliogenesis were not impaired but certain proteins associated with differentiated ependymal cells are not properly expressed». However, they do not assess gene but protein expression (IF). In addition, their quantification shows differences in the number of FoxJ1 positive cells which indeed is an impaired expression.

- Microtubules are involved in the local organization of ciliary basal bodies (see Werner et al., Vladar et al.,2011; Boutin et al., 2014). It would be interesting for the authors to check whether the subapical network of microtubules is glutamylated or not during ependymal cell differentiation and how this network is affected in their mutants.

- Showing the data mentioned in the discussion on Cep110 would be a nice addition to the paper.

- Line 354: "The latter serves as a component of tissue polarity that is required for asymmetric PCP protein localization in each cell (Boutin et al., 2014; Vladar et al., 2012)." The cited reference did not demonstrate that this microtubule network is required for asymmetric PCP localization.

Reviewer #3 (Public review):

Summary:

The authors developed a new Agbl5 KO allele, extending the deletion to the N-terminus of CCP5 to explore its function in mouse ependymal cells.

Strengths:

They show that the KO mice exhibit severe hydrocephalus due to disorganized and mislocated basal bodies. Additionally, they present evidence of both impaired beating coordination and a reduction in ciliary beating.

Weaknesses:

The manuscript is well-written but lacks specific interpretations of the results presented. Further experiments are needed to be fully convincing.

eLife Assessment

This study provides an important first look at the influence of vertical transmission in the establishment of the amphibian microbiome, with a specific focus on the potential role of parental care. Through a combination of cross-fostering experimental work, comparative analysis across species that show variable levels of care, and developmental time series, the authors provide convincing evidence that vertical transmission through care is possible, but incomplete evidence that it plays a significant role in shaping frog skin microbiomes in nature or across time. This work will be of interest to researchers studying the evolution of parental care and microbiomes in vertebrates.

Reviewer #1 (Public review):

Summary:

This manuscript describes a series of lab and field experiments to understand the role of tadpole transport in shaping the microbiome of poison frogs in early life. The authors conducted a cross-foster experiment in which R. variabilis tadpoles were carried by adults of their own species, carried by adults of another frog species, or not carried at all. After being carried for 6 hours, tadpole microbiomes resembled those of their caregiving species. Next, the authors reported higher microbiome diversity in tadpoles of two species that engage in transport-based parental care compared to one species that does not. Finally, they collected tadpoles either from the backs of an adult (i.e., they had recently been transported) or from eggs (i.e., not transported) but did not find significant overlap in microbiome composition between transported tadpoles and their parents.

Strengths:

The cross-foster experiment and the field experiment that reared transported and non-transported tadpoles are creative ways to address an important question in animal microbiome research. Together, they imply a small role for parental care in the development of the tadpole microbiome. The manuscript is generally well-written and easy to understand.

Weaknesses:

(1) Developmental time series:

It was not entirely clear how this experiment relates to the rest of the manuscript, as it does not compare any effects of transport within or across species.

(2) Cross-foster experiment:

The "heterospecific transport" tadpoles were manually brushed onto the back of the surrogate frog, while the "biological transport" tadpoles were picked up naturally by the parent. It is a little challenging to interpret the effect of caregiver species since it is conflated with the method of attachment to the parent. I noticed that the uptake of Os-associated microbes by Os-transported tadpoles seemed to be higher than the uptake of Rv-associated microbes by Rv-associated tadpoles (comparing the second box from the left to the rightmost boxplot in panel S2C). Perhaps this could be a technical artifact if manual attachment to Os frogs was more efficient than natural attachment to Rv frogs.

I was also surprised to see so much of the tadpole microbiome attributed to Os in tadpoles that were not transported by Os frogs (25-50% in many cases). It suggests that SourceTracker may not be effectively classifying the taxa.

(3) Cross-species analysis:

Like the developmental time series, this analysis doesn't really address the central question of the manuscript. I don't think it is fair for the authors to attribute the difference in diversity to parental care behavior, since the comparison only includes n=2 transporting species and n=1 non-transporting species that differ in many other ways. I would also add that increased diversity is not necessarily an expectation of vertical transmission. The similarity between adults and tadpoles is likely a more relevant outcome for vertical transmission, but the authors did not find any evidence that tadpole-adult similarity was any higher in species with tadpole transport. In fact, tadpoles and adults were more similar in the non-transporting species than in one of the transporting species (lines 296-298), which seems to directly contradict the authors' hypothesis. I don't see this result explained or addressed in the Discussion.

(4) Field experiment:

The rationale and interpretation of the genus-level network are not clear, and the figure is not legible. What does it mean to "visualize the microbial interconnectedness" or to be a "central part of the community"? The previous sentences in this paragraph (lines 337-343) seem to imply that transfer is parent-specific, but the genus-level network is based on the current adult frogs, not the previous generation of parents that transported them. So it is not clear that the distribution or co-distribution of these taxa provides any insight into vertical transmission dynamics.

Reviewer #2 (Public review):

Summary:

Here, Fischer et al. attempt to understand the role of parental care, specifically the transport of offspring, in the development of the amphibian microbiome. The amphibian microbiome is an important study system due to its association with host health and disease outcomes. This study provides vertical transfer of bacteria through parental transport of tadpoles as a mechanism influencing tadpole microbiome composition. This paper gives insight into the relative roles of the environment, species, and parental care in determining microbiome composition in amphibians.

The authors determine the time of bacterial colonization during tadpole development using PCR, observing that tadpoles were not colonized by bacteria prior to hatching from the vitelline membrane. By doing this, the impact of transport can be more accurately assessed in their laboratory experiments. The authors found that caregiver species influenced community composition, with transported tadpoles sharing a greater proportion of their skin communities with the transporting species.

In a comparison of three sympatric amphibian species that vary in their reproductive strategies, the authors found that tadpole community diversity was not reflective of habitat diversity, but may be associated with the different reproductive strategies of each species. Parental care explained some of the variance of tadpole microbiomes between species, however, transportation by conspecific adults did not lead to more similar microbiomes between tadpoles and adults compared to species that do not exhibit parental transport.

I did not find any major weaknesses in my review of this paper. The work here could potentially benefit from absolute abundance levels for shared ASVs between adults and tadpoles to more thoroughly understand the influences of vertical transmission that might be masked by relative abundance counts. This would only be a minor improvement as I think the conclusions from this work would likely remain the same, however.

Author response:

To address Reviewer 1’s concerns, we will implement the following changes:

Comment 1: We will clarify that, even without direct comparisons within or across species, whether vertically transmitted microbes act as pioneering colonizers or integrate into an existing community is an important factor influencing their effect on community composition.

Comment 2: We will provide additional details on the biology of the surrogate frog Oophaga sylvatica, explain how tadpole manipulation might influence adhesion to the caregiver, and acknowledge that the lack of knowledge on the physiological mechanisms underlying tadpole attachment currently limits our discussion to speculation.

We will further clarify in the “Methods” section that SourceTracker’s ability to accurately estimate source proportions was assessed by evaluating how well it assigned training samples to their correct source environments. We will provide the predictions for the training set and describe how they informed our data preprocessing and analysis approach.

Comment 3: While we predicted that community distances between tadpoles and adults would be smaller in species with parental transport, we explicitly state that our results did not confirm this expectation. We thus see no contradiction in our discussion but will ensure that this point is more clearly communicated. In response to the reviewer’s suggestion, we will incorporate additional literature on how tadpoles’ skin microbial communities change over time and adapt to their environment. We will also expand on how the life history of L. longirostris—specifically, the frequent presence of adults in tadpole habitats—may facilitate horizontal microbiota transmission, potentially contributing to shorter community distances.

Comment 4: We will remove the network visualization to prevent any misinterpretation.

Additionally, following Reviewer 2’s suggestion, we will include data on the absolute abundance of ASVs shared between parent and offspring after one month of development to further support the manuscript.

eLife Assessment

The valuable findings in this study reveal an intricate pattern of memory expression following retrieval extinction at different intervals from retrieval-extinction to test. They document that immediately after extinction there is a nonselective impairment in memory, which leads to no impairment at a 6-hour interval. At a 24-hour interval, there is a selective impairment. The evidence supporting the claims is incomplete and there are inconsistencies in the analyses reported that obscure the interpretation.

Reviewer #1 (Public review):

Summary:

The novel advance by Wang et al is in the demonstration that, relative to a standard extinction procedure, the retrieval-extinction procedure more effectively suppresses responses to a conditioned threat stimulus when testing occurs just minutes after extinction. The authors provide some solid evidence to show that this "short-term" suppression of responding involves engagement of the dorsolateral prefrontal cortex.

Strengths:

Overall, the study is well-designed and the results are potentially interesting. There are, however, a few issues in the way that it is introduced and discussed. Some of the issues concern clarity of expression/communication. However, others relate to a theory that could be used to help the reader understand why the results should have come out the way that they did. More specific comments and questions are presented below.

Weaknesses:

INTRODUCTION & THEORY

(1) It is difficult to appreciate why the first trial of extinction in a standard protocol does NOT produce the retrieval-extinction effect. This applies to the present study as well as others that have purported to show a retrieval-extinction effect. The importance of this point comes through at several places in the paper. E.g., the two groups in Study 1 experienced a different interval between the first and second CS extinction trials; and the results varied with this interval: a longer interval (10 min) ultimately resulted in less reinstatement of fear than a shorter interval. Even if the different pattern of results in these two groups was shown/known to imply two different processes, there is nothing in the present study that addresses what those processes might be. That is, while the authors talk about mechanisms of memory updating, there is little in the present study that permits any clear statement about mechanisms of memory. The references to a "short-term memory update" process do not help the reader to understand what is happening in the protocol.

In reply to this point, the authors cite evidence to suggest that "an isolated presentation of the CS+ seems to be important in preventing the return of fear expression." They then note the following: "It has also been suggested that only when the old memory and new experience (through extinction) can be inferred to have been generated from the same underlying latent cause, the old memory can be successfully modified(Gershman et al., 2017). On the other hand, if the new experiences are believed to be generated by a different latent cause, then the old memory is less likely to be subject to modification. Therefore, the way the 1stand 2ndCS are temporally organized (retrieval-extinction or standard extinction) might affect how the latent cause is inferred and lead to different levels of fear expression from a theoretical perspective." This merely begs the question: why might an isolated presentation of the CS+ result in the subsequent extinction experiences being allocated to the same memory state as the initial conditioning experiences? This is not yet addressed in any way.

(2) The discussion of memory suppression is potentially interesting but, in its present form, raises more questions than it answers. That is, memory suppression is invoked to explain a particular pattern of results but I, as the reader, have no sense of why a fear memory would be better suppressed shortly after the retrieval-extinction protocol compared to the standard extinction protocol; and why this suppression is NOT specific to the cue that had been subjected to the retrieval-extinction protocol.

(3) Relatedly, how does the retrieval-induced forgetting (which is referred to at various points throughout the paper) relate to the retrieval-extinction effect? The appeal to retrieval-induced forgetting as an apparent justification for aspects of the present study reinforces points 2 and 3 above. It is not uninteresting but lacks clarification/elaboration and, therefore, its relevance appears superficial at best.

(4) I am glad that the authors have acknowledged the papers by Chalkia, van Oudenhove & Beckers (2020) and Chalkia et al (2020), which failed to replicate the effects of retrieval-extinction reported by Schiller et al in Reference 6. The authors have inserted the following text in the revised manuscript: "It should be noted that while our long-term amnesia results were consistent with the fear memory reconsolidation literature, there were also studies that failed to observe fear prevention (Chalkia, Schroyens, et al., 2020; Chalkia, Van Oudenhove, et al., 2020; Schroyens et al., 2023). Although the memory reconsolidation framework provides a viable explanation for the long-term amnesia, more evidence is required to validate the presence of reconsolidation, especially at the neurobiological level (Elsey et al., 2018). While it is beyond the scope of the current study to discuss the discrepancies between these studies, one possibility to reconcile these results concerns the procedure for the retrieval-extinction training. It has been shown that the eligibility for old memory to be updated is contingent on whether the old memory and new observations can be inferred to have been generated by the same latent cause (Gershman et al., 2017; Gershman and Niv, 2012). For example, prevention of the return of fear memory can be achieved through gradual extinction paradigm, which is thought to reduce the size of prediction errors to inhibit the formation of new latent causes (Gershman, Jones, et al., 2013). Therefore, the effectiveness of the retrieval-extinction paradigm might depend on the reliability of such paradigm in inferring the same underlying latent cause." Firstly, if it is beyond the scope of the present study to discuss the discrepancies between the present and past results, it is surely beyond the scope of the study to make any sort of reference to clinical implications!!! Secondly, it is perfectly fine to state that "the effectiveness of the retrieval-extinction paradigm might depend on the reliability of such paradigm in inferring the same underlying latent cause..." This is not uninteresting, but it also isn't saying much. Minimally, I would expect some statement about factors that are likely to determine whether one is or isn't likely to see a retrieval-extinction effect, grounded in terms of this theory.

CLARIFICATIONS, ELABORATIONS, EDITS

(5) Some parts of the paper are not easy to follow. Here are a few examples (though there are others):

(a) In the abstract, the authors ask "whether memory retrieval facilitates update mechanisms other than memory reconsolidation"... but it is never made clear how memory retrieval could or should "facilitate" a memory update mechanism.

(b) The authors state the following: "Furthermore, memory reactivation also triggers fear memory reconsolidation and produces cue specific amnesia at a longer and separable timescale (Study 2, N = 79 adults)." Importantly, in study 2, the retrieval-extinction protocol produced a cue-specific disruption in responding when testing occurred 24 hours after the end of extinction. This result is interesting but cannot be easily inferred from the statement that begins "Furthermore..." That is, the results should be described in terms of the combined effects of retrieval and extinction, not in terms of memory reactivation alone; and the statement about memory reconsolidation is unnecessary. One can simply state that the retrieval-extinction protocol produced a cue-specific disruption in responding when testing occurred 24 hours after the end of extinction.

(c) The authors also state that: "The temporal scale and cue-specificity results of the short-term fear amnesia are clearly dissociable from the amnesia related to memory reconsolidation, and suggest that memory retrieval and extinction training trigger distinct underlying memory update mechanisms." ***The pattern of results when testing occurred just minutes after the retrieval-extinction protocol was different to that obtained when testing occurred 24 hours after the protocol. Describing this in terms of temporal scale is unnecessary; and suggesting that memory retrieval and extinction trigger different memory update mechanisms is not obviously warranted. The results of interest are due to the combined effects of retrieval+extinction and there is no sense in which different memory update mechanisms should be identified with the different pattern of results obtained when testing occurred either 30 min or 24 hours after the retrieval-extinction protocol (at least, not the specific pattern of results obtained here).

(d) The authors state that: "We hypothesize that the labile state triggered by the memory retrieval may facilitate different memory update mechanisms following extinction training, and these mechanisms can be further disentangled through the lens of temporal dynamics and cue-specificities." *** The first part of the sentence is confusing around usage of the term "facilitate"; and the second part of the sentence that references a "lens of temporal dynamics and cue-specificities" is mysterious. Indeed, as all rats received the same retrieval-extinction exposures in Study 2, it is not clear how or why any differences between the groups are attributed to "different memory update mechanisms following extinction".

DATA

(6A) The eight participants who were discontinued after Day 1 in Study 1 were all from the no reminder group. The authors should clarify how participants were allocated to the two groups in this experiment so that the reader can better understand why the distribution of non-responders was non-random (as it appears to be).

(6B) Similarly, in study 2, of the 37 participants that were discontinued after Day 2, 19 were from Group 30 min and 5 were from Group 6 hours. The authors should comment on how likely these numbers are to have been by chance alone. I presume that they reflect something about the way that participants were allocated to groups: e.g., the different groups of participants in studies 1 and 2 could have been run at quite different times (as opposed to concurrently). If this was done, why was it done? I can't see why the study should have been conducted in this fashion - this is for myriad reasons, including the authors' concerns re SCRs and their seasonal variations.

(6C) In study 2, why is responding to the CS- so high on the first test trial in Group 30 min? Is the change in responding to the CS- from the last extinction trial to the first test trial different across the three groups in this study? Inspection of the figure suggests that it is higher in Group 30 min relative to Groups 6 hours and 24 hours. If this is confirmed by the analysis, it has implications for the fear recovery index which is partly based on responses to the CS-. If not for differences in the CS- responses, Groups 30 min and 6 hours are otherwise identical. That is, the claim of differential recovery to the CS1 and CS2 across time may simply an artefact of the way that the recovery index was calculated. This is unfortunate but also an important feature of the data given the way in which the fear recovery index was calculated.

(6D) The 6 hour group was clearly tested at a different time of day compared to the 30 min and 24 hour groups. This could have influenced the SCRs in this group and, thereby, contributed to the pattern of results obtained.

(6E) The authors find different patterns of responses to CS1 and CS2 when they were tested 30 min after extinction versus 24 h after extinction. On this basis, they infer distinct memory update mechanisms. However, I still can't quite see why the different patterns of responses at these two time points after extinction need to be taken to infer different memory update mechanisms. That is, the different patterns of responses at the two time points could be indicative of the same "memory update mechanism" in the sense that the retrieval-extinction procedure induces a short-term memory suppression that serves as the basis for the longer-term memory suppression (i.e., the reconsolidation effect). My pushback on this point is based on the notion of what constitutes a memory update mechanism; and is motivated by what I take to be a rather loose use of language/terminology in the reconsolidation literature and this paper specifically (for examples, see the title of the paper and line 2 of the abstract).

Reviewer #2 (Public review):

Summary

The study investigated whether memory retrieval followed soon by extinction training results in a short-term memory deficit when tested - with a reinstatement test that results in recovery from extinction - soon after extinction training. Experiment 1 documents this phenomenon using a between-subjects design. Experiment 2 used a within-subject control and saw that the effect is also observed in a control condition. In addition, it also revealed that if testing is conducted 6 hours after extinction, there is not effect of retrieval prior to extinction as there is recovery from extinction independently of retrieval prior to extinction. A third Group also revealed that retrieval followed by extinction attenuates reinstatement when the test is conducted 24 hours later, consistent with previous literature. Finally, Experiment 3 used continuous theta-burst stimulation of the dorsolateral prefrontal cortex and assessed whether inhibition of that region (vs a control region) reversed the short-term effect revealed in Experiments 1 and 2. The results of control groups in Experiment 3 replicated the previous findings (short-term effect), and the experimental group revealed that these can be reversed by inhibition of the dorsolateral prefrontal cortex.

Strengths

The work is performed using standard procedures (fear conditioning and continuous theta-burst stimulation) and there is some justification of the sample sizes. The results replicate previous findings - some of which have been difficult to replicate and this needs to be acknowledged - and suggest that the effect can also be observed in a short-term reinstatement test.

The study establishes links between the memory reconsolidation and retrieval-induced forgetting (or memory suppression) literatures. The explanations that have been developed for these are distinct and the current results integrate these, by revealing that the DLPFC activity involved in retrieval-extinction short-term effect. There is thus some novelty in the present results, but numerous questions remain unaddressed.

Weakness

The fear acquisition data is converted to a differential fear SCR and this is what is analysed (early vs late). However, the figure shows the raw SCR values for CS+ and CS- and therefore it is unclear whether acquisition was successful (despite there being an "early" vs "late" effect - no descriptives are provided).

In Experiment 1 (Test results) it is unclear whether the main conclusion stems from a comparison of the test data relative to the last extinction trial ("we defined the fear recovery index as the SCR difference between the first test trial and the last extinction trial for a specific CS") or the difference relative to the CS- ("differential fear recovery index between CS+ and CS-"). It would help the reader assess the data if Fig 1e presents all the indexes (both CS+ and CS-). In addition, there is one sentence which I could not understand "there is no statistical difference between the differential fear recovery indexes between CS+ in the reminder and no reminder groups (P=0.048)". The p value suggests that there is a difference, yet it is not clear what is being compared here. Critically, any index taken as a difference relative to the CS- can indicate recovery of fear to the CS+ or absence of discrimination relative to the CS-, so ideally the authors would want to directly compare responses to the CS+ in the reminder and no-reminder groups. In the absence of such comparison, little can be concluded, in particular if SCR CS- data is different between groups. The latter issue is particularly relevant in Experiment 2, in which the CS- seems to vary between groups during the test and this can obscure the interpretation of the result.

In experiment 1, the findings suggest that there is a benefit of retrieval followed by extinction in a short-term reinstatement test. In Experiment 2, the same effect is observed to a cue which did not undergo retrieval before extinction (CS2+), a result that is interpreted as resulting from cue-independence, rather than a failure to replicate in a within-subjects design the observations of Experiment 1 (between-subjects). Although retrieval-induced forgetting is cue-independent (the effect on items that are suppressed [Rp-] can be observed with an independent probe), it is not clear that the current findings are similar, and thus that the strong parallels made are not warranted. Here, both cues have been extinguished and therefore been equally exposed during the critical stage.

The findings in Experiment 2 suggest that the amnesia reported in Experiment 1 is transient, in that no effect is observed when the test is delayed by 6 hours. The phenomena whereby reactivated memories transition to extinguished memories as a function of the amount of exposure (or number of trials) is completely different from the phenomena observed here. In the former, the manipulation has to do with the number of trials (or total amount of time) that the cues are exposed. In the current Experiment 2, the authors did not manipulate the number of trials but instead the retention interval between extinction and test. The finding reported here is closer to a "Kamin effect", that is the forgetting of learned information which is observed with intervals of intermediate length (Baum, 1968). Because the Kamin effect has been inferred to result from retrieval failure, it is unclear how this can be explained here. There needs to be much more clarity on the explanations to substantiate the conclusions.<br /> There are many results (Ryan et al., 2015) that challenge the framework that the authors base their predictions on (consolidation and reconsolidation theory), therefore these need to be acknowledged. These studies showed that memory can be expressed in the absence of the biological machinery thought to be needed for memory performance. The authors should be careful about statements such as "eliminate fear memores" for which there is little evidence.

The parallels between the current findings and the memory suppression literature are speculated in the general discussion, and there is the conclusion that "the retrieval-extinction procedure might facilitate a spontaneous memory suppression process". Because one of the basic tenets of the memory suppression literature is that it reflects an "active suppression" process, there is no reason to believe that in the current paradigm the same phenomenon is in place, but instead it is "automatic". In other words, the conclusions make strong parallels with the memory suppression (and cognitive control) literature, yet the phenomena that they observed is thought to be passive (or spontaneous/automatic). Ultimately, it is unclear why 10 mins between the reminder and extinction learning will "automatically" suppress fear memories. Further down in the discussion it is argued that "For example, in the well-known retrieval-induced forgetting (RIF) phenomenon, the recall of a stored memory can impair the retention of related long-term memory and this forgetting effect emerges as early as 20 minutes after the retrieval procedure, suggesting memory suppression or inhibition can occur in a more spontaneous and automatic manner". I did not follow with the time delay between manipulation and test (20 mins) would speak about whether the process is controlled or automatic. In addition, the links with the "latent cause" theoretical framework are weak if any. There is little reason to believe that one extinction trial, separated by 10 mins from the rest of extinction trials, may lead participants to learn that extinction and acquisition have been generated by the same latent cause.

Among the many conclusions, one is that the current study uncovers the "mechanism" underlying the short-term effects of retrieval-extinction. There is little in the current report that uncovers the mechanism, even in the most psychological sense of the mechanism, so this needs to be clarified. The same applies to the use of "adaptive".

Whilst I could access the data in the OFS site, I could not make sense of the Matlab files as there is no signposting indicating what data is being shown in the files. Thus, as it stands, there is no way of independently replicating the analyses reported.

The supplemental material shows figures with all participants, but only some statistical analyses are provided, and sometimes these are different from those reported in the main manuscript. For example, the test data in Experiment 1 is analysed with a two-way ANOVA with main effects of group (reminder vs no-reminder) and time (last trial of extinction vs first trial of test) in the main report. The analyses with all participants in the sup mat used a mixed two-way ANOVA with group (reminder vs no reminder) and CS (CS+ vs CS-). This makes it difficult to assess the robustness of the results when including all participants. In addition, in the supplementary materials there are no figures and analyses for Experiment 3.

One of the overarching conclusions is that the "mechanisms" underlying reconsolidation (long term) and memory suppression (short term) phenomena are distinct, but memory suppression phenomena can also be observed after a 7-day retention interval (Storm et al., 2012), which then questions the conclusions achieved by the current study.

References:

Baum, M. (1968). Reversal learning of an avoidance response and the Kamin effect. Journal of Comparative and Physiological Psychology, 66(2), 495.<br /> Chalkia, A., Schroyens, N., Leng, L., Vanhasbroeck, N., Zenses, A. K., Van Oudenhove, L., & Beckers, T. (2020). No persistent attenuation of fear memories in humans: A registered replication of the reactivation-extinction effect. Cortex, 129, 496-509.<br /> Ryan, T. J., Roy, D. S., Pignatelli, M., Arons, A., & Tonegawa, S. (2015). Engram cells retain memory under retrograde amnesia. Science, 348(6238), 1007-1013.<br /> Storm, B. C., Bjork, E. L., & Bjork, R. A. (2012). On the durability of retrieval-induced forgetting. Journal of Cognitive Psychology, 24(5), 617-629.

Comments on revisions:

The authors have revised the manuscript but most of my concerns have remained unaddressed.

(1) There are still no descriptive statistics to substantiate learning in Experiment 1.

(2) In the revised analyses, the authors now show that CS- changes in different groups (for example, Experiment 2) so this means that there is little to conclude from the differential scores because these depend on CS-. It is unclear whether the effects arise from CS+ performance or the differential which is subject to CS- variations.

(3) The notion that suppression is automatic is speculative at best

(4) It still struggle with the parallels between these findings and the "limbo" literature. Here you manipulated the retention interval, whereas in the cited studies the number of extinction (exposure) was varied. These are two completely different phenomena.

(5) My point about the data problematic for the reconsolidation (and consolidation) frameworks is that they observed memory in the absence of the brain substrates that are needed for memory to be observed. The answer did not address this. I do not understand how the latent cause model can explain this, if the only difference is the first ITI. Wouldn't participants fail to integrate extinction with acquisition with a longer ITI?

(6) The materials in the OSF site are the same as before, they haven't ben updated.

(7) Concerning supplementary materials, the robustness tests are intended to prove that you 1) can get the same results by varying the statistical models or 2) you can get the same results when you include all participants. Here authors have done both so this does not help. Also, in the rebuttal letter, they stated "Please note we did not include non-learners in these analyses " which contradicts what is stated in the figure captions "(learners + non learners)"

(8) Finally, the literature suggesting that reconsolidation interference "eliminates" a memory is not substantiated by data nor in line with current theorising, so I invite a revision of these strong claims.

Overall, I conclude that the revised manuscript did not address my main concerns.

Author response:

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

Reviewer #1 (Public Review):

Weaknesses:

INTRODUCTION & THEORY

(1) Can the authors please clarify why the first trial of extinction in a standard protocol does NOT produce the retrieval-extinction effect? Particularly as the results section states: "Importantly, such a short-term effect is also retrieval dependent, suggesting the labile state of memory is necessary for the short-term memory update to take effect (Fig. 1e)." The importance of this point comes through at several places in the paper:

1A. "In the current study, fear recovery was tested 30 minutes after extinction training, whereas the effect of memory reconsolidation was generally evident only several hours later and possibly with the help of sleep, leaving open the possibility of a different cognitive mechanism for the short-term fear dementia related to the retrieval-extinction procedure." ***What does this mean? The two groups in study 1 experienced a different interval between the first and second CS extinction trials; and the results varied with this interval: a longer interval (10 min) ultimately resulted in less reinstatement of fear than a shorter interval. Even if the different pattern of results in these two groups was shown/known to imply two different processes, there is absolutely no reason to reference any sort of cognitive mechanism or dementia - that is quite far removed from the details of the present study.

Indeed, the only difference between the standard extinction paradigm and the retrieval-extinction paradigm is the difference between the first and second CS extinction trials. It has been shown before that a second CS+ presented 1 hour after the initial retrieval CS+ resulted in the dephosphorylation of GluR1 in rats, which was indicative of memory destabilization. The second CS+ presented only 3 minutes after the initial retrieval CS+, as in the standard extinction training, did not cause the GluR1 dephosphorylation effect (Monfils et al., 2009). Therefore, an isolated presentation of the CS+ seems to be important in preventing the return of fear expression. Behaviorally, when the CSs were presented in a more temporally spaced (vs. mass presentation) or a more gradual manner in the extinction training, the fear amnesia effects were more salient (Cain et al., 2003, Gershman et al., 2013). It has also been suggested that only when the old memory and new experience (through extinction) can be inferred to have been generated from the same underlying latent cause, the old memory can be successfully modified (Gershman et al., 2017). On the other hand, if the new experiences are believed to be generated by a different latent cause, then the old memory is less likely to be subject to modification. Therefore, the way the first and 2nd CS are temporally organized (retrieval-extinction or standard extinction) might affect how the latent cause is inferred and lead to different levels of fear expression from a theoretical perspective. These findings, together with studies in both fear and drug memories using the retrieval-extinction paradigm (Liu et al., 2014, Luo et al., 2015, Schiller et al., 2010, Xue et al., 2012), seem to suggest that the retrieval-extinction and the standard extinction procedures engage different cognitive and molecular mechanisms that lead to significant different behavioral outcomes. 

In our study, we focus on the short-term and long-term amnesia effects of the retrieval-extinction procedure but also point out the critical role of retrieval in eliciting the short-term effect.

1B. "Importantly, such a short-term effect is also retrieval dependent, suggesting the labile state of memory is necessary for the short-term memory update to take effect (Fig. 1e)." ***As above, what is "the short-term memory update"? At this point in the text, it would be appropriate for the authors to discuss why the retrieval-extinction procedure produces less recovery than a standard extinction procedure as the two protocols only differ in the interval between the first and second extinction trials. References to a "short-term memory update" process do not help the reader to understand what is happening in the protocol.

Sorry for the lack of clarity here. By short-term memory update we meant the short-term amnesia in fear expression.

(2) "Indeed, through a series of experiments, we identified a short-term fear amnesia effect following memory retrieval, in addition to the fear reconsolidation effect that appeared much later."

***The only reason for supposing two effects is because of the differences in responding to the CS2, which was subjected to STANDARD extinction, in the short- and long-term tests. More needs to be said about how and why the performance of CS2 is affected in the short-term test and recovers in the long-term test. That is, if the loss of performance to CS1 and CS2 is going to be attributed to some type of memory updating process across the retrieval-extinction procedure, one needs to explain the selective recovery of performance to CS2 when the extinction-to-testing interval extends to 24 hours. Instead of explaining this recovery, the authors note that performance to CS1 remains low when the extinction-to-testing interval is 24 hours and invoke something to do with memory reconsolidation as an explanation for their results: that is, they imply (I think) that reconsolidation of the CS1-US memory is disrupted across the 24-hour interval between extinction and testing even though CS1 evokes negligible responding just minutes after extinction.

In our results, we did not only focus on the fear expression related to CS2. In fact, we also demonstrated that the CS1 related fear expression diminished in the short-term memory test but re-appeared in the long-term memory after the CS1 retrieval-extinction training.

The “…recovery of performance to CS2 when the extinction-to-testing interval extends to 24 hours…” is a result that has been demonstrated in various previous studies (Kindt and Soeter, 2018, Kindt et al., 2009, Nader et al., 2000, Schiller et al., 2013, Schiller et al., 2010, Xue et al., 2012). That is, the reconsolidation framework stipulates that the pharmacological or behavioral intervention during the labile states of the reconsolidation window only modifies the fear memory linked to the reminded retrieval cue, but not for the non-reminded CS-US memory expression (but also see (Liu et al., 2014, Luo et al., 2015) for using the unconditioned stimulus as the reminder cue and the retrieval-extinction paradigm to prevent the return of fear memory associated with different CS).  In fact, we hypothesized the temporal dynamics of CS1 and CS2 related fear expressions were due to the interplay between the short-term and long-term (reconsolidation) effects of the retrieval-extinction paradigm in the last figure (Fig. 6). 

(3) The discussion of memory suppression is potentially interesting but, in its present form, raises more questions than it answers. That is, memory suppression is invoked to explain a particular pattern of results but I, as the reader, have no sense of why a fear memory would be better suppressed shortly after the retrieval-extinction protocol compared to the standard extinction protocol; and why this suppression is NOT specific to the cue that had been subjected to the retrieval-extinction protocol.

We discussed memory suppression as one of the potential mechanisms to account for the three characteristics of the short-term amnesia effects: cue-independence, temporal dynamics (short-term) and thought-control-ability relevance. According to the memory suppression theory, the memory suppression effect is NOT specific to the cue and this effect was demonstrated via the independent cue test in a variety of studies (Anderson and Floresco, 2022, Anderson and Green, 2001, Gagnepain et al., 2014, Zhu et al., 2022). Therefore, we suggest in the discussion that it might be possible the CS1 retrieval cue prompted an automatic suppression mechanism and yielded the short-term fear amnesia consistent with various predictions from the memory suppression theory:

“In our experiments, subjects were not explicitly instructed to suppress their fear expression, yet the retrieval-extinction training significantly decreased short-term fear expression. These results are consistent with the short-term amnesia induced with the more explicit suppression intervention (Anderson et al., 1994; Kindt and Soeter, 2018; Speer et al., 2021; Wang et al., 2021; Wells and Davies, 1994). It is worth noting that although consciously repelling unwanted memory is a standard approach in memory suppression paradigm, it is possible that the engagement of the suppression mechanism can be unconscious. For example, in the retrieval-induced forgetting (RIF) paradigm, recall of a stored memory impairs the retention of related target memory and this forgetting effect emerges as early as 20 minutes after the retrieval procedure, suggesting memory suppression or inhibition can occur in a more spontaneous and automatic manner (Imai et al., 2014). Moreover, subjects with trauma histories exhibited more suppression-induced forgetting for both negative and neutral memories than those with little or no trauma (Hulbert and Anderson, 2018). Similarly, people with higher self-reported thought-control capabilities showed more severe cue-independent memory recall deficit, suggesting that suppression mechanism is associated with individual differences in spontaneous control abilities over intrusive thoughts (Küpper et al., 2014). It has also been suggested that similar automatic mechanisms might be involved in organic retrograde amnesia of traumatic childhood memories (Schacter et al., 2012; Schacter et al., 1996).”

3A. Relatedly, how does the retrieval-induced forgetting (which is referred to at various points throughout the paper) relate to the retrieval-extinction effect? The appeal to retrieval-induced forgetting as an apparent justification for aspects of the present study reinforces points 2 and 3 above. It is not uninteresting but needs some clarification/elaboration.

We introduced the retrieval-induced forgetting (RIF) to make the point that RIF was believed to be related to the memory suppression mechanism and the RIF effect can appear relatively early, consistent with what we observed in the short-term amnesia effect. We have re-written the manuscript to make this point clearer:

“It is worth noting that although consciously repelling unwanted memory is a standard approach in memory suppression paradigm, it is possible that the engagement of the suppression mechanism can be unconscious. For example, in the retrieval-induced forgetting (RIF) paradigm, recall of a stored memory impairs the retention of related target memory and this forgetting effect emerges as early as 20 minutes after the retrieval procedure, suggesting memory suppression or inhibition can occur in a more spontaneous and automatic manner (Imai et al., 2014). Moreover, subjects with trauma histories exhibited more suppression-induced forgetting for both negative and neutral memories than those with little or no trauma (Hulbert and Anderson, 2018). Similarly, people with higher self-reported thought-control capabilities showed more severe cue-independent memory recall deficit, suggesting that suppression mechanism is associated with individual differences in spontaneous control abilities over intrusive thoughts (Küpper et al., 2014).”

(4) Given the reports by Chalkia, van Oudenhove & Beckers (2020) and Chalkia et al (2020), some qualification needs to be inserted in relation to reference 6. That is, reference 6 is used to support the statement that "during the reconsolidation window, old fear memory can be updated via extinction training following fear memory retrieval". This needs a qualifying statement like "[but see Chalkia et al (2020a and 2020b) for failures to reproduce the results of 6]."

https://pubmed.ncbi.nlm.nih.gov/32580869/

https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7115860/

We have incorporated the reviewer’s suggestion into the revised manuscript in both the introduction:

“Pharmacological blockade of protein synthesis and behavioral interventions can both eliminate the original fear memory expression in the long-term (24 hours later) memory test ( Lee, 2008; Lee et al., 2017; Schiller et al., 2013; Schiller et al., 2010), resulting in the cue-specific fear memory deficit (Debiec et al., 2002; Lee, 2008; Nader, Schafe, & LeDoux, 2000). For example, during the reconsolidation window, retrieving a fear memory allows it to be updated through extinction training (i.e., the retrieval-extinction paradigm (Lee, 2008; Lee et al., 2017; Schiller et al., 2013; Schiller et al., 2010), but also see (Chalkia, Schroyens, et al., 2020; Chalkia, Van Oudenhove, et al., 2020; D. Schiller, LeDoux, & Phelps, 2020)”

And in the discussion:

“It should be noted that while our long-term amnesia results were consistent with the fear memory reconsolidation literatures, there were also studies that failed to observe fear prevention (Chalkia, Schroyens, et al., 2020; Chalkia, Van Oudenhove, et al., 2020; Schroyens et al., 2023). Although the memory reconsolidation framework provides a viable explanation for the long-term amnesia, more evidence is required to validate the presence of reconsolidation, especially at the neurobiological level (Elsey et al., 2018). While it is beyond the scope of the current study to discuss the discrepancies between these studies, one possibility to reconcile these results concerns the procedure for the retrieval-extinction training. It has been shown that the eligibility for old memory to be updated is contingent on whether the old memory and new observations can be inferred to have been generated by the same latent cause (Gershman et al., 2017; Gershman and Niv, 2012). For example, prevention of the return of fear memory can be achieved through gradual extinction paradigm, which is thought to reduce the size of prediction errors to inhibit the formation of new latent causes (Gershman, Jones, et al., 2013). Therefore, the effectiveness of the retrieval-extinction paradigm might depend on the reliability of such paradigm in inferring the same underlying latent cause. Furthermore, other studies highlighted the importance of memory storage per se and suggested that memory retention was encoded in the memory engram cell ensemble connectivity whereas the engram cell synaptic plasticity is crucial for memory retrieval (Ryan et al., 2015; Tonegawa, Liu, et al., 2015; Tonegawa, Pignatelli, et al., 2015). It remains to be tested how the cue-independent short-term and cue-dependent long-term amnesia effects we observed could correspond to the engram cell synaptic plasticity and functional connectivity among engram cell ensembles (Figure 6). This is particularly important, since the cue-independent characteristic of the short-term amnesia suggest that either different memory cues fail to evoke engram cell activities, or the retrieval-extinction training transiently inhibits connectivity among engram cell ensembles. Finally, SCR is only one aspect of the fear expression, how the retrieval-extinction paradigm might affect subjects’ other emotional (such as the startle response) and cognitive fear expressions such as reported fear expectancy needs to be tested in future studies since they do not always align with each other (Kindt et al., 2009; Sevenster et al., 2012, 2013).”

5A. What does it mean to ask: "whether memory retrieval facilitates update mechanisms other than memory reconsolidation"? That is, in what sense could or would memory retrieval be thought to facilitate a memory update mechanism?

It is widely documented in the literatures that memory retrieval renders the old memory into a labile state susceptible for the memory reconsolidation process. However, as we mentioned in the manuscript, studies have shown that memory reconsolidation requires the de novo protein synthesis and usually takes hours to complete. What remains unknown is whether old memories are subject to modifications other than the reconsolidation process. Our task specifically tested the short-term effect of the retrieval-extinction paradigm and found that fear expression diminished 30mins after the retrieval-extinction training. Such an effect cannot be accounted for by the memory reconsolidation effect.

5B. "First, we demonstrate that memory reactivation prevents the return of fear shortly after extinction training in contrast to the memory reconsolidation effect which takes several hours to emerge and such a short-term amnesia effect is cue independent (Study 1, N = 57 adults)."

***The phrasing here could be improved for clarity: "First, we demonstrate that the retrieval-extinction protocol prevents the return of fear shortly after extinction training (i.e., when testing occurs just min after the end of extinction)." Also, cue-dependence of the retrieval-extinction effect was assessed in study 2.

We thank the reviewer and have modified the phrasing of the sentence:

“First, we demonstrate that memory retrieval-extinction protocol prevents the return of fear expression shortly after extinction training and this short-term effect is memory reactivation dependent (Study 1, N = 57 adults).”

5C. "Furthermore, memory reactivation also triggers fear memory reconsolidation and produces cue-specific amnesia at a longer and separable timescale (Study 2, N = 79 adults)." ***In study 2, the retrieval-extinction protocol produced a cue-specific disruption in responding when testing occurred 24 hours after the end of extinction. This result is interesting but cannot be easily inferred from the statement that begins "Furthermore..." That is, the results should be described in terms of the combined effects of retrieval and extinction, not in terms of memory reactivation alone; and the statement about memory reconsolidation is unnecessary. One can simply state that the retrieval-extinction protocol produced a cue-specific disruption in responding when testing occurred 24 hours after the end of extinction.

We have revised the text according to the reviewer’s comment.

“Furthermore, across different timescales, the memory retrieval-extinction paradigm triggers distinct types of fear amnesia in terms of cue-specificity and cognitive control dependence, suggesting that the short-term fear amnesia might be caused by different mechanisms from the cue-specific amnesia at a longer and separable timescale (Study 2, N = 79 adults).”

5D. "...we directly manipulated brain activities in the dorsolateral prefrontal cortex and found that both memory retrieval and intact prefrontal cortex functions were necessary for the short-term fear amnesia."

***This could be edited to better describe what was shown: E.g., "...we directly manipulated brain activities in the dorsolateral prefrontal cortex and found that intact prefrontal cortex functions were necessary for the short-term fear amnesia after the retrieval-extinction protocol."

Edited:

“Finally, using continuous theta-burst stimulation (Study 3, N = 75 adults), we directly manipulated brain activity in the dorsolateral prefrontal cortex, and found that both memory reactivation and intact prefrontal cortex function were necessary for the short-term fear amnesia after the retrieval-extinction protocol.”

5E. "The temporal scale and cue-specificity results of the short-term fear amnesia are clearly dissociable from the amnesia related to memory reconsolidation, and suggest that memory retrieval and extinction training trigger distinct underlying memory update mechanisms."

***The pattern of results when testing occurred just minutes after the retrieval-extinction protocol was different from that obtained when testing occurred 24 hours after the protocol. Describing this in terms of temporal scale is unnecessary, and suggesting that memory retrieval and extinction trigger different memory update mechanisms is not obviously warranted. The results of interest are due to the combined effects of retrieval+extinction and there is no sense in which different memory update mechanisms should be identified with retrieval (mechanism 1) and extinction (mechanism 2).

We did not argue for different memory update mechanisms for the “retrieval (mechanism 1) and extinction (mechanism 2)” in our manuscript. Instead, we proposed that the retrieval-extinction procedure, which was mainly documented in the previous literatures for its association with the reconsolidation-related fear memory retention (the long-term effect), also had a much faster effect (the short-term effect). These two effects differed in many aspects, suggesting that different memory update mechanisms might be involved.

5F. "These findings raise the possibility of concerted memory modulation processes related to memory retrieval..."

***What does this mean?

As we mentioned in our response to the previous comment, we believe that the retrieval-extinction procedure triggers different types of memory update mechanisms working on different temporal scales.

(6) "...suggesting that the fear memory might be amenable to a more immediate effect, in addition to what the memory reconsolidation theory prescribes..."

***What does it mean to say that the fear memory might be amenable to a more immediate effect?

We intended to state that the retrieval-extinction procedure can produce a short-term amnesia effect and have thus revised the text.

(7) "Parallel to the behavioral manifestation of long- and short-term memory deficits, concurrent neural evidence supporting memory reconsolidation theory emphasizes the long-term effect of memory retrieval by hypothesizing that synapse degradation and de novo protein synthesis are required for reconsolidation."

***This sentence needs to be edited for clarity.

We have rewritten this sentence:

“Corresponding to the long-term behavioral manifestation, concurrent neural evidence supporting memory reconsolidation hypothesis emphasizes that synapse degradation and de novo protein synthesis are required for reconsolidation.”

(8) "previous behavioral manipulations engendering the short-term declarative memory effect..."

***What is the declarative memory effect? It should be defined.

We meant the amnesia on declarative memory research, such as the memory deficit caused by the think/no-think paradigms. Texts have been modified for clarity:

“On the contrary, previous behavioral manipulations engendering the short-term amnesia on declarative memory, such as the think/no-think paradigm, hinges on the intact activities in brain areas such as dorsolateral prefrontal cortex (cognitive control) and its functional coupling with specific brain regions such as hippocampus (memory retrieval) (Anderson and Green, 2001; Wimber et al., 2015).”

(9) "The declarative amnesia effect emerges much earlier due to the online functional activity modulation..."

***Even if the declarative memory amnesia effect had been defined, the reference to online functional activity modulation is not clear.

We have rephrased the sentence:

“The declarative amnesia effect arises much earlier due to the more instant modulation of functional connectivity, rather than the slower processes of new protein synthesis in these brain regions.”

(10) "However, it remains unclear whether memory retrieval might also precipitate a short-term amnesia effect for the fear memory, in addition to the long-term prevention orchestrated by memory consolidation."

***I found this sentence difficult to understand on my first pass through the paper. I think it is because of the phrasing of memory retrieval. That is, memory retrieval does NOT precipitate any type of short-term amnesia for the fear memory: it is the retrieval-extinction protocol that produces something like short-term amnesia. Perhaps this sentence should also be edited for clarity.

We have changed “memory retrieval” to “retrieval-extinction” where applicable.

I will also note that the usage of "short-term" at this point in the paper is quite confusing: Does the retrieval-extinction protocol produce a short-term amnesia effect, which would be evidenced by some recovery of responding to the CS when tested after a sufficiently long delay? I don't believe that this is the intended meaning of "short-term" as used throughout the majority of the paper, right?

By “short-term”, we meant the lack of fear expression in the test phase (measured by skin conductance responses) shortly after the retrieval-extinction procedure (30 mins in studies 1 & 2 and 1 hour in study 3). It does not indicate that the effect is by itself “short-lived”.

(11) "To fully comprehend the temporal dynamics of the memory retrieval effect..."<br /> ***What memory retrieval effect? This needs some elaboration.

We’ve changed the phrase “memory retrieval effect” to “retrieval-extinction effect” to refer to the effect of retrieval-extinction on fear amnesia.

(12) "We hypothesize that the labile state triggered by the memory retrieval may facilitate different memory update mechanisms following extinction training, and these mechanisms can be further disentangled through the lens of temporal dynamics and cue-specificities."

***What does this mean? The first part of the sentence is confusing around the usage of the term "facilitate"; and the second part of the sentence that references a "lens of temporal dynamics and cue-specificities" is mysterious. Indeed, as all rats received the same retrieval-extinction exposures in Study 2, it is not clear how or why any differences between the groups are attributed to "different memory update mechanisms following extinction".

As the reviewer mentioned, if only one time point data were collected, we cannot differentiate whether different memory update mechanisms are involved. In study 2, however, the 3 groups only differed on the time onsets the reinstatement test was conducted. Accordingly, our results showed that the fear amnesia effects for CS1 and CS2 cannot be simply explained by forgetting: different memory update mechanisms must be at work to explain the characteristics of the SCR related to both CS1 and CS2 at three different time scales (30min, 6h and 24h). It was based on these results, together with the results from the TMS study (study 3), that we proposed the involvement of a short-term memory update mechanism in addition to the reconsolidation related fear amnesia (which should become evident much later) induced by the retrieval-extinction protocol.

(13) "In the first study, we aimed to test whether there is a short-term amnesia effect of fear memory retrieval following the fear retrieval-extinction paradigm."

***Again, the language is confusing. The phrase, "a short-term amnesia effect" implies that the amnesia itself is temporary; but I don't think that this implication is intended. The problem is specifically in the use of the phrase "a short-term amnesia effect of fear memory retrieval." To the extent that short-term amnesia is evident in the data, it is not due to retrieval per se but, rather, the retrieval-extinction protocol.

We have changed the wordings and replaced “memory retrieval” with “retrieval-extinction” where applicable.

(14) The authors repeatedly describe the case where there was a 24-hour interval between extinction and testing as consistent with previous research on fear memory reconsolidation. Which research exactly? That is, in studies where a CS re-exposure was combined with a drug injection, responding to the CS was disrupted in a final test of retrieval from long-term memory which typically occurred 24 hours after the treatment. Is that what the authors are referring to as consistent? If so, which aspect of the results are consistent with those previous findings? Perhaps the authors mean to say that, in the case where there was a 24-hour interval between extinction and testing, the results obtained here are consistent with previous research that has used the retrieval-extinction protocol. This would clarify the intended meaning greatly.

Our 24 hour test results after the retrieval-extinction protocol was consistent with both pharmacological and behavioral intervention studies in fear memory reconsolidation studies (Kindt and Soeter, 2018, Kindt et al., 2009, Liu et al., 2014, Luo et al., 2015, Monfils et al., 2009, Nader et al., 2000, Schiller et al., 2013, Schiller et al., 2010, Xue et al., 2012) since the final test phase typically occurred 24 hours after the treatment. At the 24-hour interval, the memory reconsolidation effect would become evident either via drug administration or behavioral intervention (extinction training).

DATA

(15) Points about data:

5A. The eight participants who were discontinued after Day 1 in study 1 were all from the no-reminder group. Can the authors please comment on how participants were allocated to the two groups in this experiment so that the reader can better understand why the distribution of non-responders was non-random (as it appears to be)?

15B. Similarly, in study 2, of the 37 participants that were discontinued after Day 2, 19 were from Group 30 min, and 5 were from Group 6 hours. Can the authors comment on how likely these numbers are to have been by chance alone? I presume that they reflect something about the way that participants were allocated to groups, but I could be wrong.

We went back and checked out data. As we mentioned in the supplementary materials, we categorized subjects as non-responders if their SCR response to any CS was less than 0.02  in Day 1 (fear acquisition). Most of the discontinued participants (non-responders) in the no-reminder group (study 1) and the 30min & 24 h groups (study 2) were when the heating seasons just ended or were yet to start, respectively. It has been documented that human body thermal conditions were related to the quality of the skin conductance response (SCR) measurements (Bauer et al., 2022, Vila, 2004). We suspect that the non-responders might be related to the body thermal conditions caused by the lack of central heating.

15C. "Post hoc t-tests showed that fear memories were resilient after regular extinction training, as demonstrated by the significant difference between fear recovery indexes of the CS+ and CS- for the no-reminder group (t26 = 7.441, P < 0.001; Fig. 1e), while subjects in the reminder group showed no difference of fear recovery between CS+ and CS- (t29 = 0.797, P = 0.432, Fig. 1e)."

***Is the fear recovery index shown in Figure 1E based on the results of the first test trial only? How can there have been a "significant difference between fear recovery indexes of the CS+ and CS- for the no-reminder group" when the difference in responding to the CS+ and CS- is used to calculate the fear recovery index shown in 1E? What are the t-tests comparing exactly, and what correction is used to account for the fact that they are applied post-hoc?

As we mentioned in the results section of the manuscript, the fear recovery index was defined as “the SCR difference between the first test trial and the last extinction trial of a specific CS”. We then calculated the “differential fear recovery index” (figure legends of Fig. 1e) between CS+ and CS- for both the reminder and no-reminder groups. The post-hoc t-tests were used to examine whether there were significant fear recoveries (compare to 0) in both the reminder (t₂₉ = 0.797, P = 0.432, Fig. 1e) and no-reminder (t₂₆ = 7.441, P  < 0.001; Fig. 1e) groups. We realize that the description of Bonferroni correction was not specified in the original manuscript and hence added in the revision where applicable.

15D. "Finally, there is no statistical difference between the differential fear recovery indexes between CS+ in the reminder and no reminder groups (t55 = -2.022, P = 0.048; Fig. 1c, also see Supplemental Material for direct test for the test phase)."

***Is this statement correct - i.e., that there is no statistically significant difference in fear recovery to the CS+ in the reminder and no reminder groups? I'm sure that the authors would like to claim that there IS such a difference; but if such a difference is claimed, one would be concerned by the fact that it is coming through in an uncorrected t-test, which is the third one of its kind in this paragraph. What correction (for the Type 1 error rate) is used to account for the fact that the t-tests are applied post-hoc? And if no correction, why not?

We are sorry about the typo.  The reviewer was correct that we meant to claim here that “… there is a significant difference between the differential fear recovery indexes between CS+ in the reminder and no-reminder groups (t₅₅ =- 2.022, P = 0.048; Fig. 1e)”.  Note that the t-test performed here was a confirmatory test following our two-way ANOVA with main effects of group (reminder vs. no-reminder) and time (last extinction trial vs. first test trial) on the differential CS SCR response (CS+ minus CS-) and we found a significant group x time interaction effect (F_1.55 = 4.087, P = 0.048, η² = 0.069). The significant difference between the differential fear recovery indexes was simply a re-plot of the interaction effect mentioned above and therefore no multiple correction is needed. We have reorganized the sequence of the sentences such that this t-test now directly follows the results of the ANOVA:

“The interaction effect was confirmed by the significant difference between the differential fear recovery indexes between CS1+ and CS2+ in the reminder and no-reminder groups (t₅₅ \= -2.022, P \= 0.048; Figure 1E, also see Supplemental Material for the direct test of the test phase).”

15E. In study 2, why is responding to the CS- so high on the first test trial in Group 30 min? Is the change in responding to the CS- from the last extinction trial to the first test trial different across the three groups in this study? Inspection of the figure suggests that it is higher in Group 30 min relative to Groups 6 hours and 24 hours. If this is confirmed by the analysis, it has implications for the fear recovery index which is partly based on responses to the CS-. If not for differences in the CS- responses, Groups 30 minutes and 6 hours are otherwise identical.

Following the reviewer’s comments, we went back and calculated the mean SCR difference of CS- between the first test trial and the last extinction trial for all three studies (see Author response image 1 below). In study 1, there was no difference in the mean CS- SCR (between the first test trial and last extinction trial) between the reminder and no-reminder groups (Kruskal-Wallis test , panel a), though both groups showed significant fear recovery even in the CS- condition (Wilcoxon signed rank test, reminder: P = 0.0043, no-reminder: P = 0.0037). Next, we examined the mean SCR for CS- for the 30min, 6h and 24h groups in study 2 and found that there was indeed a group difference (one-way ANOVA,F_2.76 = 5.3462, P = 0.0067, panel b), suggesting that the CS- related SCR was influenced by the test time (30min, 6h or 24h). We also tested the CS- related SCR for the 4 groups in study 3 (where test was conducted 1 hour after the retrieval-extinction training) and found that across TMS stimulation types (PFC vs. VER) and reminder types (reminder vs. no-reminder) the ANOVA analysis did not yield main effect of TMS stimulation type (F_1.71 = 0.322, P = 0.572) nor main effect of reminder type (F_1.71 = 0.0499, P = 0.824, panel c). We added the R-VER group results in study 3 (see panel c) to panel b and plotted the CS- SCR difference across 4 different test time points and found that CS- SCR decreased as the test-extinction delay increased (Jonckheere-Terpstra test, P = 0.00028). These results suggest a natural “forgetting” tendency for CS- related SCR and highlight the importance of having the CS- as a control condition to which the CS+ related SCR was compared with.

Author response image 1.

15F. Was the 6-hour group tested at a different time of day compared to the 30-minute and 24-hour groups; and could this have influenced the SCRs in this group?

For the 30min and 24h groups, the test phase can be arranged in the morning, in the afternoon or at night. However, for the 6h group, the test phase was inevitably in the afternoon or at night since we wanted to exclude the potential influence of night sleep on the expression of fear memory (see Author response table 1 below). If we restricted the test time in the afternoon or at night for all three groups, then the timing of their extinction training was not matched.

Author response table 1.

Nevertheless, we also went back and examined the data for the subjects only tested in the afternoon or at nights in the 30min and 24h groups to match with the 6h group where all the subjects were tested either in the afternoon or at night. According to Author response table 1 above, we have 17 subjects for the 30min group (9+8),18 subjects for the 24h group (9 + 9) and 26 subjects for the 6h group (12 + 14). As Author response image 2 shows, the SCR patterns in the fear acquisition, extinction and test phases were similar to the results presented in the original figure.

Author response image 2.

15G. Why is the range of scores in "thought control ability" different in the 30-minute group compared to the 6-hour and 24-hour groups? I am not just asking about the scale on the x-axis: I am asking why the actual distribution of the scores in thought control ability is wider for the 30-minute group?

We went back and tested whether the TCAQ score variance was the same across three groups. We found that there was significant difference in the variance of the TCAQ score distribution across three groups (F_2.155 = 4.324, P = 0.015, Levene test). However, post-hoc analyses found that the variance of TCAQ is not significantly different between the 30min and 6h groups (F_26.25 = 0.4788, P = 0.0697), nor between the 30min and 24h groups (i>F_26.25 = 0.4692, P = 0.0625). To further validate our correlational results between the TCAQ score and the fear recovery index, we removed the TCAQ scores that were outside the TCAQ score range of the 6h & 24h groups from the 30min group (resulting in 4 “outliner” TCAQ scores in the 30min group, panel a in Author response image 3 below) and the Levene test confirmed that the variance of the TCAQ scores showed no difference across groups after removing the 4 “outliner” data points in the 30min group (i>F_2.147 = 0.74028, P = 0.4788). Even with the 4 “outliers” removed from the 30min group, the correlational analysis of the TCAQ scores and the fear recovery index still yielded significant result in the 30min group (beta = -0.0148, t = -3.731, P = 0.0006, see panel b below), indicating our results were not likely due to the inclusion of subjects with extreme TCAQ scores.

Author response image 3.

(16) During testing in each experiment, how were the various stimuli presented? That is, was the presentation order for the CS+ and CS- pseudorandom according to some constraint, as it had been in extinction? This information should be added to the method section.

We mentioned the order of the stimuli in the testing phase in the methods section “… For studies 2 & 3, …a pseudo-random stimulus order was generated for fear acquisition and extinction phases of three groups with the rule that no same trial- type (CS1+, CS2+ and CS-) repeated more than twice. In the test phase, to exclude the possibility that the difference between CS1+ and CS2+ was simply caused by the presentation sequence of CS1+ and CS2+, half of the participants completed the test phase using a pseudo-random stimuli sequence and the identities of CS1+ and CS2+ reversed in the other half of the participants.”

(17) "These results are consistent with previous research which suggested that people with better capability to resist intrusive thoughts also performed better in motivated dementia in both declarative and associative memories."

***Which parts of the present results are consistent with such prior results? It is not clear from the descriptions provided here why thought control ability should be related to the present findings or, indeed, past ones in other domains. This should be elaborated to make the connections clear.

In the 30min group, we found that subjects’ TCAQ scores were negatively correlated with their fear recovery indices. That is, people with better capacity to resist intrusive thoughts were also less likely to experience the return of fear memory, which are consistent with previous results. Together with our brain stimulation results, the short-term amnesia is related to subject’s cognitive control ability and intact dlPFC functions. It is because of these similarities that we propose that the short-term amnesia might be related to the automatic memory suppression mechanism originated from the declarative memory research. Since we have not provided all the evidence at this point of the results section, we briefly listed the connections with previous declarative and associative memory research.

Reviewer #2 (Public Review):

The fear acquisition data is converted to a differential fear SCR and this is what is analysed (early vs late). However, the figure shows the raw SCR values for CS+ and CS- and therefore it is unclear whether the acquisition was successful (despite there being an "early" vs "late" effect - no descriptives are provided).

As the reviewer mentioned, the fear acquisition data was converted to a differential fear SCR and we conducted a two-way mixed ANOVA (reminder vs. no-reminder) x time (early vs. late part of fear acquisition) on the differential SCRs. We found a significant main effect of time (early vs. late; F_1.55 = 6.545, P = 0.013, η² = 0.106), suggesting successful fear acquisition in both groups. Fig. 1c also showed the mean differential SCR for the latter half of the acquisition phase in both the reminder and no-reminder groups and there was no significant difference in acquired SCRs between groups (early acquisition: t₅₅ = -0.063, P = 0.950; late acquisition: t₅₅ = -0.318, P = 0.751; Fig. 1c).

In Experiment 1 (Test results) it is unclear whether the main conclusion stems from a comparison of the test data relative to the last extinction trial ("we defined the fear recovery index as the SCR difference between the first test trial and the last extinction trial for a specific CS") or the difference relative to the CS- ("differential fear recovery index between CS+ and CS-"). It would help the reader assess the data if Figure 1e presents all the indexes (both CS+ and CS-). In addition, there is one sentence that I could not understand "there is no statistical difference between the differential fear recovery indexes between CS+ in the reminder and no reminder groups (P=0.048)". The p-value suggests that there is a difference, yet it is not clear what is being compared here. Critically, any index taken as a difference relative to the CS- can indicate recovery of fear to the CS+ or absence of discrimination relative to the CS-, so ideally the authors would want to directly compare responses to the CS+ in the reminder and no-reminder groups. The latter issue is particularly relevant in Experiment 2, in which the CS- seems to vary between groups during the test and this can obscure the interpretation of the result.

In all the experiments, the fear recovery index (FRI) was defined as the SCR difference between the first test trial and the last extinction trial for any CS. Subsequently, the differential fear recovery index (FRI) was defined between the FRI of a specific CS+ and the FRI of the CS-. The differential FRI would effectively remove the non-specific time related effect (using the CS- FRI as the baseline). We have revised the text accordingly.

As we responded to reviewer #1, the CS- fear recovery indices (FIR) for the reminder and no-reminder groups were not statistically different (Kruskal-Wallis test , panel a, Author response image 1), though both groups showed significant fear recovery even in the CS- condition (Wilcoxon signed rank test, reminder: P = 0.0043, no-reminder: P = 0.0037, panel a). Next, we examined the mean SCR for CS- for the 30min, 6h and 24h groups in study 2 and found that there was indeed a group difference (one-way ANOVA,  one-way ANOVA,F_2.76 = 5.3462, P = 0.0067, panel b), suggesting that the CS- SCR was influenced by the test time delay. We also tested the CS- SCR for the 4 groups in study 3 and found that across TMS stimulation types (PFC vs. VER) and reminder types (reminder vs. no-reminder) the ANOVA analysis did not yield main effect of TMS stimulation type (F_1.71 = 0.322, P = 0.572) nor main effect of reminder type (F_1.71 = 0.0499, P = 0.824, panel c). We added the R-VER group results in study 3 (see panel c) to panel b and plotted the CS- SCR difference across 4 different test time points and found that CS- SCR decreased as the test-extinction delay increased (Jonckheere-Terpstra test, P = 0.00028). These results suggest a natural “forgetting” tendency for the CS- fear recovery index and highlight the importance of having the CS- as a control condition to compare the CS+ recovery index with (resulting in the Differential recovery index). Parametric and non-parametric analyses were adopted based on whether the data met the assumptions for the parametric analyses.

In Experiment 1, the findings suggest that there is a benefit of retrieval followed by extinction in a short-term reinstatement test. In Experiment 2, the same effect is observed on a cue that did not undergo retrieval before extinction (CS2+), a result that is interpreted as resulting from cue-independence, rather than a failure to replicate in a within-subjects design the observations of Experiment 1 (between-subjects). Although retrieval-induced forgetting is cue-independent (the effect on items that are suppressed [Rp-] can be observed with an independent probe), it is not clear that the current findings are similar. Here, both cues have been extinguished and therefore been equally exposed during the critical stage.

We appreciate the reviewer’s insight on this issue. Although in the discussion we raised the possibility of memory suppression to account for the short-term amnesia effect, we did not intend to compare our paradigm side-by-side with retrieval-induced forgetting. In our previous work (Wang et al., 2021), we reported that active suppression effect of CS+ related fear memory during the standard extinction training generalized to other CS+, yielding a cue-independent effect. In the current experiments, we did not implement active suppression; instead, we used the CS+ retrieval-extinction paradigm. It is thus possible that the CS+ retrieval cue may function to facilitate automatic suppression. Indeed, in the no-reminder group (standard extinction) of study 1, we did observe the return of fear expression, suggesting the critical role of CS+ reminder before the extinction training. Based on the results mentioned above, we believe our short-term amnesia results were consistent with the hypothesis that the retrieval CS+ (reminder) might prompt subjects to adopt an automatic suppress mechanism in the following extinction training, yielding cue-independent amnesia effects.

The findings in Experiment 2 suggest that the amnesia reported in Experiment 1 is transient, in that no effect is observed when the test is delayed by 6 hours. The phenomena whereby reactivated memories transition to extinguished memories as a function of the amount of exposure (or number of trials) is completely different from the phenomena observed here. In the former, the manipulation has to do with the number of trials (or the total amount of time) that the cues are exposed to. In the current study, the authors did not manipulate the number of trials but instead the retention interval between extinction and test. The finding reported here is closer to a "Kamin effect", that is the forgetting of learned information which is observed with intervals of intermediate length (Baum, 1968). Because the Kamin effect has been inferred to result from retrieval failure, it is unclear how this can be explained here. There needs to be much more clarity on the explanations to substantiate the conclusions.

Indeed, in our studies, we did not manipulate the amount of exposure (or number of trials) but only the retention interval between extinction and test. Our results demonstrated that the retrieval-extinction protocol yielded the short-term amnesia on fear memory, qualitatively different from the reconsolidation related amnesia proposed in the previous literatures. After examining the temporal dynamics, cue-specificity and TCAQ association with the short-term amnesia, we speculated that the short-term effect might be related to an automatic suppression mechanism. Of course, further studies will be required to test such a hypothesis.

Our results might not be easily compared with the “Kamin effect”, a term coined to describe the “retention of a partially learned avoidance response over varying time intervals” using a learning-re-learning paradigm (Baum, 1968, Kamin, 1957). However, the retrieval-extinction procedure used in our studies was different from the learning-re-learning paradigm in the original paper (Kamin, 1957) and the reversal-learning paradigm the reviewer mentioned (Baum, 1968).

There are many results (Ryan et al., 2015) that challenge the framework that the authors base their predictions on (consolidation and reconsolidation theory), therefore these need to be acknowledged. Similarly, there are reports that failed to observe the retrieval-extinction phenomenon (Chalkia et al., 2020), and the work presented here is written as if the phenomenon under consideration is robust and replicable. This needs to be acknowledged.

We thank the reviewer pointing out the related literature and have added a separate paragraph about other results in the discussion (as well as citing relevant references in the introduction) to provide a full picture of the reconsolidation theory to the audience:

“It should be noted that while our long-term amnesia results were consistent with the fear memory reconsolidation literatures, there were also studies that failed to observe fear prevention (Chalkia, Schroyens, et al., 2020; Chalkia, Van Oudenhove, et al., 2020; Schroyens et al., 2023). Although the memory reconsolidation framework provides a viable explanation for the long-term amnesia, more evidence is required to validate the presence of reconsolidation, especially at the neurobiological level (Elsey et al., 2018). While it is beyond the scope of the current study to discuss the discrepancies between these studies, one possibility to reconcile these results concerns the procedure for the retrieval-extinction training. It has been shown that the eligibility for old memory to be updated is contingent on whether the old memory and new observations can be inferred to have been generated by the same latent cause (Gershman et al., 2017; Gershman and Niv, 2012). For example, prevention of the return of fear memory can be achieved through gradual extinction paradigm, which is thought to reduce the size of prediction errors to inhibit the formation of new latent causes (Gershman, Jones, et al., 2013). Therefore, the effectiveness of the retrieval-extinction paradigm might depend on the reliability of such paradigm in inferring the same underlying latent cause. Furthermore, other studies highlighted the importance of memory storage per se and suggested that memory retention was encoded in the memory engram cell ensemble connectivity whereas the engram cell synaptic plasticity is crucial for memory retrieval (Ryan et al., 2015; Tonegawa, Liu, et al., 2015; Tonegawa, Pignatelli, et al., 2015). It remains to be tested how the cue-independent short-term and cue-dependent long-term amnesia effects we observed could correspond to the engram cell synaptic plasticity and functional connectivity among engram cell ensembles (Figure 6). This is particularly important, since the cue-independent characteristic of the short-term amnesia suggest that either different memory cues fail to evoke engram cell activities, or the retrieval-extinction training transiently inhibits connectivity among engram cell ensembles. Finally, SCR is only one aspect of the fear expression, how the retrieval-extinction paradigm might affect subjects’ other emotional (such as the startle response) and cognitive fear expressions such as reported fear expectancy needs to be tested in future studies since they do not always align with each other (Kindt et al., 2009; Sevenster et al., 2012, 2013).”

The parallels between the current findings and the memory suppression literature are speculated in the general discussion, and there is the conclusion that "the retrieval-extinction procedure might facilitate a spontaneous memory suppression process". Because one of the basic tenets of the memory suppression literature is that it reflects an "active suppression" process, there is no reason to believe that in the current paradigm, the same phenomenon is in place, but instead, it is "automatic". In other words, the conclusions make strong parallels with the memory suppression (and cognitive control) literature, yet the phenomena that they observed are thought to be passive (or spontaneous/automatic).

Ultimately, it is unclear why 10 mins between the reminder and extinction learning will "automatically" suppress fear memories. Further down in the discussion, it is argued that "For example, in the well-known retrieval-induced forgetting (RIF) phenomenon, the recall of a stored memory can impair the retention of related long-term memory and this forgetting effect emerges as early as 20 minutes after the retrieval procedure, suggesting memory suppression or inhibition can occur in a more spontaneous and automatic manner". I did not follow with the time delay between manipulation and test (20 mins) would speak about whether the process is controlled or automatic.

In our previous research, we showed that the memory suppression instruction together with the extinction procedure successfully prevented the return of fear expression in the reinstatement test trials 30mins after the extinction training (Wang et al., 2021). In the current experiments, we replaced the suppression instruction with the retrieval cue before the extinction training (retrieval-extinction protocol) and observed similar short-term amnesia effects. These results prompted us to hypothesize in the discussion that the retrieval cue might facilitate an automatic suppression process. We made the analogy to RIF phenomenon in the discussion to suggest that the suppression of (competing) memories could be unintentional and fast (20 mins), both of which were consistent with our results. We agree with the reviewer that this hypothesis is more of a speculation (hence in the discussion), and more studies are required to further test such a hypothesis. However, what we want to emphasize in this paper is the report of the short-term amnesia effects which were clearly not related to the memory reconsolidation effect in a variety of aspects.

Among the many conclusions, one is that the current study uncovers the "mechanism" underlying the short-term effects of retrieval extinction. There is little in the current report that uncovers the mechanism, even in the most psychological sense of the mechanism, so this needs to be clarified. The same applies to the use of "adaptive".

Whilst I could access the data on the OFS site, I could not make sense of the Matlab files as there is no signposting indicating what data is being shown in the files. Thus, as it stands, there is no way of independently replicating the analyses reported.

We have re-organized data on the OFS site, and they should be accessible now.

The supplemental material shows figures with all participants, but only some statistical analyses are provided, and sometimes these are different from those reported in the main manuscript. For example, the test data in Experiment 1 is analysed with a two-way ANOVA with the main effects of group (reminder vs no-reminder) and time (last trial of extinction vs first trial of the test) in the main report. The analyses with all participants in the sup mat used a mixed two-way ANOVA with a group (reminder vs no reminder) and CS (CS+ vs CS-). This makes it difficult to assess the robustness of the results when including all participants. In addition, in the supplementary materials, there are no figures and analyses for Experiment 3.

We are sorry for the lack of clarity in the supplementary materials. We have supplementary figures Fig. S1 & S2 for the data re-analysis with all the responders (learners + non-learners). The statistical analyses performed on the responders in both figures yielded similar results as those in the main text. For other analyses reported in the supplementary materials, we specifically provided different analysis results to demonstrate the robustness of our results. For example, to rule out the effects we observed in two-way ANOVA in the main text may be driven by the different SCR responses on the last extinction trial, we only tested the two-way ANOVA for the first trial SCR of test phase and these analyses provided similar results. Please note we did not include non-learners in these analyses (the texts of the supplementary materials).

Since we did not exclude any non-learners in study 3, all the results were already reported in the main text.

One of the overarching conclusions is that the "mechanisms" underlying reconsolidation (long term) and memory suppression (short term) phenomena are distinct, but memory suppression phenomena can also be observed after a 7-day retention interval (Storm et al., 2012), which then questions the conclusions achieved by the current study.

As we stated before, the focus of the manuscript was to demonstrate a novel short-term fear amnesia effect following the retrieval-extinction procedure. We discussed memory suppression as one of the potential mechanisms for such a short-term effect. In fact, the durability of the memory suppression effect is still under debate. Although Storm et al. (2012) suggested that the retrieval-induced forgetting can persist for as long as a week, other studies, however, failed to observe long-term forgetting (after 24 hrs; (Carroll et al., 2007, Chan, 2009). It is also worth noting that Storm et al. (2012) tested RIF one week later using half of the items the other half of which were tested 5 minutes after the retrieval practice. Therefore, it can be argued that there is a possibility that the long-term RIF effect is contaminated by the test/re-test process on the same set of (albeit different) items at different time onsets (5mins & 1 week).

Reviewer #3 (Public Review):

(1) The entire study hinges on the idea that there is memory 'suppression' if (1) the CS+ was reminded before extinction and (2) the reinstatement and memory test takes place 30 minutes later (in Studies 1 & 2). However, the evidence supporting this suppression idea is not very strong. In brief, in Study 1, the effect seems to only just reach significance, with a medium effect size at best, and, moreover, it is unclear if this is the correct analysis (which is a bit doubtful, when looking at Figure 1D and E). In Study 2, there was no optimal control condition without reminder and with the same 30-min interval (which is problematic, because we can assume generalization between CS1+ and CS2+, as pointed out by the authors, and because generalization effects are known to be time-dependent). Study 3 is more convincing, but entails additional changes in comparison with Studies 1 and 2, i.e., applications of cTBS and an interval of 1 hour instead of 30 minutes (the reason for this change was not explained). So, although the findings of the 3 studies do not contradict each other and are coherent, they do not all provide strong evidence for the effect of interest on their own.

Related to the comment above, I encourage the authors to double-check if this statement is correct: "Also, our results remain robust even with the "non-learners" included in the analysis (Fig. S1 in the Supplemental Material)". The critical analysis for Study 1 is a between-group comparison of the CS+ and CS- during the last extinction trial versus the first test trial. This result only just reached significance with the selected sample (p = .048), and Figures 1D and E even seem to suggest otherwise. I doubt that the analysis would reach significance when including the "non-learners" - assuming that this is what is shown in Supplemental Figure 1 (which shows the data from "all responded participants").

Our subjects were categorized based on the criteria specified in supplementary table S1. More specifically, we excluded the non-responders (Mean CS SCR < 0.02 uS  in the fear acquisition phase), and non-learners and focused our analyses on the learners. Non-responders were dismissed after day 1 (the day of fear acquisition), but both learners and non-learners finished the experiments. This fact gave us the opportunity to examine data for both the learners and the responders (learners + non-learners). What we showed in fig. 1D and E were differential SCRs (CS+ minus CS-) of the last extinction trials and the differential fear recovery indices (CS+ minus CS-), respectively. We have double checked the figures and both the learners (Fig. 1) and the responders (i.e. learners and non-learners, supplementary Fig. 1) results showed significant differences between the reminder and no-reminder groups on the differential fear recovery index.

Also related to the comment above, I think that the statement "suggesting a cue-independent short-term amnesia effect" in Study 2 is not correct and should read: "suggesting extinction of fear to the CS1+ and CS2+", given that the response to the CS+'s is similar to the response to the CS-, as was the case at the end of extinction. Also the next statement "This result indicates that the short-term amnesia effect observed in Study 2 is not reminder-cue specific and can generalize to the non-reminded cues" is not fully supported by the data, given the lack of an appropriate control group in this study (a group without reinstatement). The comparison with the effect found in Study 1 is difficult because the effect found there was relatively small (and may have to be double-checked, see remarks above), and it was obtained with a different procedure using a single CS+. The comparison with the 6-h and 24-h groups of Study 2 is not helpful as a control condition for this specific question (i.e., is there reinstatement of fear for any of the CS+'s) because of the large procedural difference with regard to the intervals between extinction and reinstatement (test).

In Fig. 2e, we showed the differential fear recovery indices (FRI) for the CS+ in all three groups. Since the fear recovery index (FRI) was calculated as the SCR difference between the first test trial and the last extinction trial for any CS, the differential fear recovery indices (difference between CS+ FRI and CS- FRI) not significantly different from 0 should be interpreted as the lack of fear expression in the test phase. Since spontaneous recovery, reinstatement and renewal are considered canonical phenomena in demonstrating that extinction training does not really “erase” conditioned fear response, adding the no-reinstatement group as a control condition would effectively work as the spontaneous recovery group and the comparison between the reinstatement and no-instatement groups turns into testing the difference in fear recovery using different methods (reinstatement vs. spontaneous recovery).

(2) It is unclear which analysis is presented in Figure 3. According to the main text, it either shows the "differential fear recovery index between CS+ and CS-" or "the fear recovery index of both CS1+ and CS2+". The authors should clarify what they are analyzing and showing, and clarify to which analyses the ** and NS refer in the graphs. I would also prefer the X-axes and particularly the Y-axes of Fig. 3a-b-c to be the same. The image is a bit misleading now. The same remarks apply to Figure 5.

We are sorry about the lack of clarity here. Figures 3 & 5 showed the correlational analyses between TCAQ and the differential fear recovery index (FRI) between CS+ and CS-. That is, the differential FRI of CS1+ (CS1+ FRI minus CS- FRI) and the differential FRI of CS2+ (CS2+ FRI minus CS- FRI).

We have rescaled both X and Y axes for figures 3 & 5 (please see the revised figures). 

(3) In general, I think the paper would benefit from being more careful and nuanced in how the literature and findings are represented. First of all, the authors may be more careful when using the term 'reconsolidation'. In the current version, it is put forward as an established and clearly delineated concept, but that is not the case. It would be useful if the authors could change the text in order to make it clear that the reconsolidation framework is a theory, rather than something that is set in stone (see e.g., Elsey et al., 2018 (https://doi.org/10.1037/bul0000152), Schroyens et al., 2022 (https://doi.org/10.3758/s13423-022-02173-2)).

In addition, the authors may want to reconsider if they want to cite Schiller et al., 2010 (https://doi.org/10.1038/nature08637), given that the main findings of this paper, nor the analyses could be replicated (see, Chalkia et al., 2020 (https://doi.org/10.1016/j.cortex.2020.04.017; https://doi.org/10.1016/j.cortex.2020.03.031).

We thank the reviewer’s comments and have incorporated the mentioned papers into our revised manuscript by pointing out the extant debate surrounding the reconsolidation theory in the introduction:

“Pharmacological blockade of protein synthesis and behavioral interventions can both eliminate the original fear memory expression in the long-term (24 hours later) memory test ( Lee, 2008; Lee et al., 2017; Schiller et al., 2013; Schiller et al., 2010), resulting in the cue-specific fear memory deficit (Debiec et al., 2002; Lee, 2008; Nader, Schafe, & LeDoux, 2000). For example, during the reconsolidation window, retrieving a fear memory allows it to be updated through extinction training (i.e., the retrieval-extinction paradigm (Lee, 2008; Lee et al., 2017; Schiller et al., 2013; Schiller et al., 2010), but also see (Chalkia, Schroyens, et al., 2020; Chalkia, Van Oudenhove, et al., 2020; D. Schiller, LeDoux, & Phelps, 2020). ”

As well as in the discussion:

“It should be noted that while our long-term amnesia results were consistent with the fear memory reconsolidation literatures, there were also studies that failed to observe fear prevention (Chalkia, Schroyens, et al., 2020; Chalkia, Van Oudenhove, et al., 2020; Schroyens et al., 2023). Although the memory reconsolidation framework provides a viable explanation for the long-term amnesia, more evidence is required to validate the presence of reconsolidation, especially at the neurobiological level (Elsey et al., 2018). While it is beyond the scope of the current study to discuss the discrepancies between these studies, one possibility to reconcile these results concerns the procedure for the retrieval-extinction training. It has been shown that the eligibility for old memory to be updated is contingent on whether the old memory and new observations can be inferred to have been generated by the same latent cause (Gershman et al., 2017; Gershman and Niv, 2012). For example, prevention of the return of fear memory can be achieved through gradual extinction paradigm, which is thought to reduce the size of prediction errors to inhibit the formation of new latent causes (Gershman, Jones, et al., 2013). Therefore, the effectiveness of the retrieval-extinction paradigm might depend on the reliability of such paradigm in inferring the same underlying latent cause. Furthermore, other studies highlighted the importance of memory storage per se and suggested that memory retention was encoded in the memory engram cell ensemble connectivity whereas the engram cell synaptic plasticity is crucial for memory retrieval (Ryan et al., 2015; Tonegawa, Liu, et al., 2015; Tonegawa, Pignatelli, et al., 2015). It remains to be tested how the cue-independent short-term and cue-dependent long-term amnesia effects we observed could correspond to the engram cell synaptic plasticity and functional connectivity among engram cell ensembles (Figure 6). This is particularly important, since the cue-independent characteristic of the short-term amnesia suggest that either different memory cues fail to evoke engram cell activities, or the retrieval-extinction training transiently inhibits connectivity among engram cell ensembles. Finally, SCR is only one aspect of the fear expression, how the retrieval-extinction paradigm might affect subjects’ other emotional (such as the startle response) and cognitive fear expressions such as reported fear expectancy needs to be tested in future studies since they do not always align with each other (Kindt et al., 2009; Sevenster et al., 2012, 2013).”

Relatedly, it should be clarified that Figure 6 is largely speculative, rather than a proven model as it is currently presented. This is true for all panels, but particularly for panel c, given that the current study does not provide any evidence regarding the proposed reconsolidation mechanism.

We agree with the reviewer that Figure 6 is largely speculative. We realize that there are still debates regarding the retrieval-extinction procedure and the fear reconsolidation hypothesis. We have provided a more elaborated discussion and pointed out that figure 6 is only a working hypothesis and more work should be done to test such a hypothesis:

“Although mixed results have been reported regarding the durability of suppression effects in the declarative memory studies (Meier et al., 2011; Storm et al., 2012), future research will be needed to investigate whether the short-term effect we observed is specifically related to associative memory or the spontaneous nature of suppression (Figure 6C).”

Lastly, throughout the paper, the authors equate skin conductance responses (SCR) with fear memory. It should at least be acknowledged that SCR is just one aspect of a fear response, and that it is unclear whether any of this would translate to verbal or behavioral effects. Such effects would be particularly important for any clinical application, which the authors put forward as the ultimate goal of the research.

Again, we agree with the reviewer on this issue, and we have acknowledged that SCR is only one aspect of the fear response and caution should be exerted in clinical application:

“Finally, SCR is only one aspect of the fear expression, how the retrieval-extinction paradigm might affect subjects’ other emotional (such as the startle response) and cognitive fear expressions such as reported fear expectancy needs to be tested in future studies since they do not always align with each other (Kindt et al., 2009; Sevenster et al., 2012, 2013).”

(4) The Discussion quite narrowly focuses on a specific 'mechanism' that the authors have in mind. Although it is good that the Discussion is to the point, it may be worthwhile to entertain other options or (partial) explanations for the findings. For example, have the authors considered that there may be an important role for attention? When testing very soon after the extinction procedure (and thus after the reminder), attentional processes may play an important role (more so than with longer intervals). The retrieval procedure could perhaps induce heightened attention to the reminded CS+ (which could be further enhanced by dlPFC stimulation)?

We thank the reviewer for this suggestion and have added more discussion on the potential mechanisms involved. Unfortunately, since the literature on attention and fear recovery is rather scarce, it is even more of a speculation given our study design and results are mainly about subjects’ skin conductance responses (SCR).

(5) There is room for improvement in terms of language, clarity of the writing, and (presentation of the) statistical analyses, for all of which I have provided detailed feedback in the 'Recommendations for the authors' section. Idem for the data availability; they are currently not publicly available, in contrast with what is stated in the paper. In addition, it would be helpful if the authors would provide additional explanation or justification for some of the methodological choices (e.g., the 18-s interval and why stimulate 8 minutes after the reminder cue, the choice of stimulation parameters), and comment on reasons for (and implications of) the large amount of excluded participants (>25%).

We have addressed the data accessibility issue and added the justifications for the methodological choices as well as the excluded participants. As we mentioned in the manuscript and the supplementary materials, adding the non-learners into data analysis did not change the results. Since the non-responders discontinued after Day 1 due to their non-measurable spontaneous SCR signals towards different CS, it’s hard to speculate whether or how the results might have changed. However, participants’ exclusion rate in the SCR studies were relatively high (Hu et al., 2018, Liu et al., 2014, Raio et al., 2017, Schiller et al., 2010, Schiller et al., 2012, Wang et al., 2021). The non-responders were mostly associated with participants being tested in the winter in our tasks. Cold weather and dry skins in the winter are likely to have caused the SCR hard to measure (Bauer et al., 2022, Vila, 2004). Different intervals between the reinstating US (electric shock) and the test trials were used in the previous literature such as 10min (Schiller et al., 2010, Schiller et al., 2013) and 18 or 19s (Kindt and Soeter, 2018, Kindt et al., 2009, Wang et al., 2021). We stuck with the 18s reinstatement interval in the current experiment. For the cTBS stimulation, since the stimulation itself lasted less than 2mins, we started the cTBS 8min after the onset of reminder cue to ensure that any effect caused by the cTBS stimulation occurred during the hypothesized time window, where the old fear memory becomes labile after memory retrieval. All the stimulation parameters were determined based on previous literature, which showed that with the transcranial magnetic stimulation (TMS) on the human dorsolateral prefrontal cortex could disrupt fear memory reconsolidation (Borgomaneri et al., 2020, Su et al., 2022).

Finally, I think several statements made in the paper are overly strong in light of the existing literature (or the evidence obtained here) or imply causal relationships that were not directly tested.

We have revised the texts accordingly.

Reviewer #2 (Recommendations For The Authors):

On numerous occasions there are typos and the autocorrect has changed "amnesia" for "dementia".

We are sorry about this mistake and have revised the text accordingly.

Reviewer #3 (Recommendations For The Authors):

*"Neither of the studies reported in this article was preregistered. The data for both studies are publicly accessible at https://osf.io/9agvk". This excerpt from the text suggests that there are 2 studies, but there are 3 in the paper. Also, the data are only accessible upon request, not publicly available. I haven't requested them, as this could de-anonymize me as a reviewer.

We are sorry for the accessibility of the link. The data should be available to the public now.

*Please refrain from causal interpretations when they are not supported by the data:

- Figure 3 "thought-control ability only affected fear recovery"; a correlation does not provide causal evidence.

- "establishing a causal link between the dlPFC activity and short-term fear amnesia." I feel this statement is too strong; to what extent do we know for sure what the applied stimulation of (or more correct: near) the dlPFC does exactly?

We thank the reviewer for the suggestion and have changed the wording related to figure 3. On the other hand, we’d like to argue that the causal relationship between the dlPFC activity and short-term fear amnesia is supported by the results from study 3. Although the exact functional role of the TMS on dlPFC can be debated, the fact that the TMS stimulation on the dlPFC (compared to the vertex group) brought back the otherwise diminished fear memory expression can be viewed as the causal evidence between the dlPFC activity and short-term fear amnesia.

*The text would benefit from language editing, as it contains spelling and grammar mistakes, as well as wording that is vague or inappropriate. I suggest the authors check the whole text, but below are already some excerpts that caught my eye:

"preludes memory reconsolidation"; "old fear memory can be updated"; "would cause short-term memory deficit"; "the its functional coupling"; "Subjects (...) yielded more severe amnesia in the memory suppression tasks"; "memory retrieval might also precipitate a short-term amnesia effect"; "more SEVERE amnesia in the memory suppression tasks"; "the effect size of reinstatement effect"; "the previous literatures"; "towards different CS"; "failed to show SCR response to the any stimuli"; "significant effect of age of TMS"; "each subject' left hand"; "latter half trials"; "Differntial fear recovery"; "fear dementia"; "the fear reinstatement effects at different time scale is related to"; "fear reocery index"; "thought-control abiliites"; "performed better in motivated dementia"; "we tested that in addition to the memory retrieval cue (reminder), whether the"; "during reconsolidation window"; "consisitent with the short-term dementia"; "low level of shock (5v)"

We thank the reviewer for thorough reading and sorry about typos in the manuscript. We have corrected typos and grammar mistakes as much as we can find.

*In line with the remark above, there are several places where the text could still be improved.

- The last sentence of the Abstract is rather vague and doesn't really add anything.

- Please reword or clarify: "the exact functional role played by the memory retrieval remains unclear".

- Please reword or clarify: "the unbinding of the old memory trace".

- "suggesting that the fear memory might be amenable to a more immediate effect, in addition to what the memory reconsolidation theory prescribes" shouldn't this rather read "in contrast with"?

We have modified the manuscript.

- In the Introduction, the authors state: "Specifically, memory reconsolidation effect will only be evident in the long-term (24h) memory test due to its requirement of new protein synthesis and is cue-dependent". They then continue about the more immediate memory update mechanisms that they want to study, but it is unclear from how the rationale is presented whether (and why (not)) they also expect this mechanism to be cue-dependent.

Most of the previous studies on the fear memory reconsolidation using CS as the memory retrieval cues have demonstrated that the reconsolidation effect is cue-dependent (Kindt and Soeter, 2018, Kindt et al., 2009, Monfils et al., 2009, Nader et al., 2000, Schiller et al., 2013, Schiller et al., 2010, Xue et al., 2012). However, other studies using unconditioned stimulus retrieval-extinction paradigm showed that such protocol was able to prevent the return of fear memory expression associated with different CSs (Liu et al., 2014, Luo et al., 2015). In our task, we used CS+ as the memory retrieval cues and our results were consistent with results from previous studies using similar paradigms.

- "The effects of cTBS over the right dlPFC after the memory reactivation were assessed using the similar mixed-effect four-way ANOVA". Please clarify what was analyzed here.<br /> - "designing novel treatment of psychiatric disorders". Please make this more concrete or remove the statement.

This sentence was right after a similar analysis performed in the previous paragraph. While the previous graph focused on how the SCRs in the acquisition phase were modulated by factors such as CS+ (CS1+ and CS2+), reminder (reminder vs. no-reminder), cTBS site (right dlPFC vs. vertex) and trial numbers, this analysis focused instead on the SCR responses in the extinction training phase. We have made the modifications as the reviewer suggested.

*I have several concerns related to the (presentation) of the statistical analyses/results:<br /> - Some statistical analyses, as well as calculation of certain arbitrary indices (e.g., differential fear recovery index) are not mentioned nor explained in the Methods section, but only mentioned in the Results section.

We have added the explanation of the differential fear recovery index into the methods section:

“To measure the extent to which fear returns after the presentation of unconditioned stimuli (US, electric shock) in the test phase, we defined the fear recovery index as the SCR difference between the first test trial and the last extinction trial for a specific CS for each subject. Similarly, in studies 2 and 3, differential fear recovery index was defined as the difference between fear recovery indices of CS+ and CS- for both CS1+ and CS2+.”

- Figure 1C-E: It is unclear what the triple *** mean. Do they have the same meaning in Figure 1C and Figure 1E? I am not sure that that makes sense. The meaning is not explained in the figure caption (I think it is different from the single asterisk*) and is not crystal clear from the main text either.

We explained the triple *** in the figure legend (Fig. 1): ***P < 0.001. The asterisk placed within each bar in Figure 1C-E indicates the statistical results of the post-hoc test of whether each bar was significant. For example, the *** placed inside bars in Figure 1E indicates that the differential fear recovery index is statistically significant in the no-reminder group (P < 0.001).

- Supplemental Figure 1: "with all responded participants" Please clarify how you define 'responded participants' and include the n's.

We presented the criteria for both the responder/non-responder and the learner/non-learner in the table of the supplementary materials and reported the number of subjects in each category (please see supplement Table 1).

- "the differential SCRs (difference between CS+ and CS-) for the CS+". Please clarify what this means and/or how it is calculated exactly.

Sorry, it means the difference between the SCRs invoked by CS+ and CS- for both CS1+ (CS1+ minus CS-) and CS2+ (CS2+ minus CS-).

*I suggest that the authors provide a bit more explanation about the thought-control ability questionnaire. For example, the type of items, etc, as this is not a very commonly used questionnaire in the fear conditioning field.

We provided a brief introduction to the thought-control ability questionnaire in the methods section:

“The control ability over intrusive thought was measured by the 25-item Thought-Control Ability Questionnaire (TCAQ) scle(30). Participants were asked to rate on a five-point Likert-type scale the extent to which they agreed with the statement from 1 (completely disagree) to 5 (completely agree). At the end of the experiments, all participants completed the TCAQ scale to assess their perceived control abilities over intrusive thoughts in daily life(17).”

We have added further description of the item types to the TCAQ scale.

*The authors excluded more than 25% of the participants. It would be interesting to hear reasons for this relatively large number and some reflection on whether they think this selection affects their results (e.g., could being a (non)responder in skin conductance influence the susceptibility to reactivation-extinction in some way?).

Participants exclusion rate in the SCR studies were relatively high (Hu et al., 2018, Liu et al., 2014, Raio et al., 2017, Schiller et al., 2010, Schiller et al., 2012, Wang et al., 2021). The non-responders were mostly associated with participants being tested in the winter in our tasks. Cold weather and dry skins in the winter are likely to have caused the SCR hard to measure (Bauer et al., 2022, Vila, 2004).

*Minor comments that the authors may want to consider:

- Please explain abbreviations upon first use, e.g., TMS.

- In Figure 6, it is a bit counterintuitive that the right Y-axis goes from high to low.

We added the explanation of TMS:

“Continuous theta burst stimulation (cTBS), a specific form of repetitive transcranial magnetic stimulation (rTMS)…”

We are sorry and agree that the right Y-axis was rather counterintuitive. However, since the direction of the fear recovery index (which was what we measured in the experiment) and the short/long-term amnesia effect are of the opposite directions, plotting one index from low to high would inevitably cause the other index to go from high to low.

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eLife Assessment

This study provides a valuable structural analysis of the Sedoheptulose-1,7-Bisphosphatase (SBPase) from Chlamydomonas reinhardtii. The data presented are solid and based on X-ray structures of the CrSBPase in an oxidized and reduced state, the authors identify a disulfide bond in close proximity to the dimer interface. They show that the redox-state of the CrSBPase impacts its oligomeric state and might also influence the activity of the protein.

Joint Public Review:

The central theme of the manuscript is the structure of SBPase - an enzyme central to the photosynthetic Calvin-Benson-Bassham cycle. The authors claim that the structure is first of its kind from a chlorophyte Chlamydomonas reinhardtii, a model unicellular green microalga. The authors use a number of methods like protein expression, purification, enzymatic assays, SAXS, molecular dynamics simulations and xray crystallography to resolve a 3.09 A crystal structure of the oxidized and partially reduced state. The results are supported by the claims made in the manuscript. While the structure is the first from a chlorophyte, it is not unique. Several structures of SBPase are available and a comparison has been made between the structure reported here and others that have been previously published.

Author response:

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

Recommendations for the authors:

Reviewer #1:

The authors have thoroughly changed the manuscript and addressed most of my concerns. I appreciate adding the activity assays of the C115/120S mutants, however, I suggest that the authors embed and also discuss these data more clearly. It also escaped my attention earlier that the positioning of the disulfide bond is 117-122 in the deposited PDBs instead of 115-120. The authors should carefully check which positioning is correct here.

We thank reviewer #1 for his or her careful assessment of our revised manuscript. As suggested, we detailed the results section “CrSBPase enzymatic activity” with additional numerical values, and discussed more clearly the comparisons of results for activity assays of mutants C115S and C120S in the section “Oligomeric states of CrSBPase”. Residues numbering was carefully proof-checked throughout the manuscript for correctness and homogeneity. C115 and C120 are numbered according to best databases consensus, ie. GenBank and Uniprot, and may differ from one database to another (including PDB) due to varying numbering rules. We clarified the chosen nomenclature in methods section “Cloning and mutagenesis of CrSBPase expression plasmids”.

Line 246-250: I think it is evident that the two SBPase structures superpose well given the sequence identity of more than 70%. However, it would be great to include a superposition of the two structures in Figure 1, especially with regard to the region harboring C115 and C120.

We added a panel showing superimposition of CrSBPase 7b2o and PpSBPase 5iz3 and made a close-up view around the region C115-C120 in supplementary figure 5. Given the density in information of figure 1 we prefer not to add additional images on it. Supplementary figure 5 was initially intended to illustrate sequence conservation/variation among homologs, thus fitting with the objective to compare past and present XRC results.

Line 255-266: I am again missing a panel in Figure 1 here, e.g. a side-by-side view of Xray vs AF2/3 structure.

We added another panel in supplementary figure 5 to visually compare side-by-side SBPase crystallographic structure 7b2o and our AF3 model. Again, for the sake of clarity we prefer not to overload figure 1 with additional panels. This will also enable thorough comparison of past XRC of PpSBPase, present XRC of CrSBPase, and various AF models (see below, oligomer comparisons).

Line 261-266: Did the authors predict dimers and tetramers using AF3? What are the confidence metrics in this case? Do the authors see differences to the monomer prediction in case a multimer is confidently predicted?

We modeled dimers and tetramers using AF3 and added them on supplementary figure 5 side by side with protomer of XRC model 7b2o and with monomer predicted by AF3. Color code for supplementary figure 5 panels F-H is according to AF standard representation of plDDT. Confidence metrics per residue correspond to very high reliability (navy blue) or, locally, confident prediction (cyan) and overall prediction scores range from pTM=0.85-0.91, a high-quality prediction. Interface prediction score is high for both dimer (ipTM=0.9) and tetramer (ipTM=0.82). We reported these data in supplementary figure 5 and corresponding updated legend. XRC and AF models all align with RMSD<0.5 Å, indicating a globally unchanged structure of the protomer in the various methods and oligomeric states.

Line 441: How does the oligomeric equilibrium change in C115/120S mutants? This information should be added for the mutants. Besides, the mAU units in Fig. 6 could be normalized to allow an easier comparison between the chromatograms of wt and mutants.

Change in oligomeric equilibrium is assessed by size-exclusion chromatography of WT and mutants C115S, C120S as reported in figure 6A. We made quantitative estimation of WT, and C115S and C120S mutants equilibrium by comparing maximal peak intensity and added this information in the text. Briefly, the oligomer ratio on a scale of 100 is 9:48:43 for WT, 42:25:33 for mutant C115S, and 29:17:54 for mutant C120S (ratio expressed as tetramer:dimer:monomer). We prefer not to normalize values of absorbance, but rather keep the actual measurement of absorbance at 280 nm on the chromatogram of figure 6, for the sake of consistency with the added text and for a more transparent report of the experiment.

Line 447: WT activity is 12.15+-2.15 and both mutants have a higher activity. The authors should check if their values (96% and 107%) are correct. Besides, did the authors check if the increase in C120S is statistically significant? My impression is that both mutants have a higher activity than the wildtype, in both correlating with increased fractions of the tetramer. This would also make sense, as the corresponding region is part of the tetramer interface in the crystal packing.

The reported activity values were checked for correctness. Wild-type SBPase specific activity at 12.5 ±2.15 µmol(NADPH) min^-1 mg(SBPase)^-1 was obtained by pre-incubating the enzyme with 1 µM CrTRXf2 supplemented with 1 mM DTT and 10 mM Mg²⁺, while the results of supplementary figure 14 reporting the comparison of activation of WT and mutants, with a variation of 107 or 96 %, were obtained with a slightly different protocol for pre-incubation of the enzyme with 10 mM DTT and 10 mM Mg²⁺. Please note that whether WT enzyme was assayed in 10 mM DTT 10 mM Mg or in 1 µM TRX 1 mM DTT 10 mM Mg, its specific activity appears equal within experimental error. Both mutants have nearly the same activity than the WT in the assay reported in supplementary figure 14: we fully agree that 107% (and 96%) variation is indeed not significant considering the uncertainty of the measurement (see error bars representing standard deviations of the mean in supplementary figure 14). We added this important information in the text. Even though both mutations stabilize the most active tetramer in untreated recombinant protein, we think that after reducting treatment both WT and mutants all reach the same maximal activity because they all form an equivalent proportion of the active tetramer versus alternative oligomeric states. We furhter interprete this piece of data as a decoupling of reduction and catalysis: in physiological conditions we assume that SBPase would initiate activation upon the reduction of disulfide bridges, including but not limited to C115-C120 that restricts the entry into fully active tetramer, at which point SBPase in reduced form reaches maximal activity until another post-translational signal eventually changes its conformation and oligomerisation.

We thank again reviewer 1 for his or her assessment and valuable suggestions.

eLife Assessment

The study presents important findings on inositol-requiring enzyme (IRE1α) inhibition on diet-induced obesity (overnutrition) and insulin resistance where IRE1α inhibition enhances thermogenesis and reduces the metabolically active and M1-like macrophages in adipose tissue. The evidence supporting the conclusions is convincing. The work will be of interest to cell biologists and biochemists working in metabolism, insulin resistance and inflammation with a broad eLife readership.

Reviewer #1 (Public review):

First, the authors confirm the up-regulation of the main genes involved in the three branches of the Unfolded Protein Response (UPR) system in diet-induced obese mice in AT, observations that have been extensively reported before. Not surprisingly, IRE1a inhibition with STF led to an amelioration of the obesity and insulin resistance of the animals. Moreover, non-alcoholic fatty liver disease was also improved by the treatment. More novel are their results in terms of thermogenesis and energy expenditure, where IRE1a seems to act via activation of brown AT. Finally, mice treated with STF exhibited significantly fewer metabolically active and M1-like macrophages in the AT compared to those under vehicle conditions. Overall, the authors conclude that targeting IRE1a has therapeutical potential for treating obesity and insulin resistance.

The study has some strengths, such as the detailed characterization of the effect of STF in different fat depots and a thorough analysis of macrophage populations. However, the lack of novelty in the findings somewhat limits the study´s impact on the field.

Reviewer #3 (Public review):

Summary:

The manuscript by Wu D. et al. explores an innovative approach in immunometabolism and obesity by investigating the potential of targeting macrophage Inositol-requiring enzyme 1α (IRE1α) in cases of overnutrition. Their findings suggest that pharmacological inhibition of IRE1α could influence key aspects such as adipose tissue inflammation, insulin resistance, and thermogenesis. Notable discoveries include the identification of High-Fat Diet (HFD)-induced CD9+ Trem2+ macrophages and the reversal of metabolically active macrophages' activity with IRE1α inhibition using STF. These insights could significantly impact future obesity treatments.

Strengths:

The study's key strengths lie in its identification of specific macrophage subsets and the demonstration that inhibiting IRE1α can reverse the activity of these macrophages. This provides a potential new avenue for developing obesity treatments and contributes valuable knowledge to the field.

Weaknesses:

The research lacks an in-depth exploration of the broader metabolic mechanisms involved in controlling diet-induced obesity (DIO). Addressing this gap would strengthen the understanding of how targeting IRE1α might fit into the larger metabolic landscape.

Impact and Utility:

The findings have the potential to advance the field of obesity treatment by offering a novel target for intervention. However, further research is needed to fully elucidate the metabolic pathways involved and to confirm the long-term efficacy and safety of this approach. The methods and data presented are useful, but additional context and exploration are required for broader application and understanding.

Comments on revisions:

The authors have satisfactorily addressed all of my previous concerns.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

First, the authors confirm the up-regulation of the main genes involved in the three branches of the Unfolded Protein Response (UPR) system in diet-induced obese mice in AT, observations that have been extensively reported before. Not surprisingly, IRE1a inhibition with STF led to an amelioration of the obesity and insulin resistance of the animals. Moreover, non-alcoholic fatty liver disease was also improved by the treatment. More novel are their results in terms of thermogenesis and energy expenditure, where IRE1a seems to act via activation of brown AT. Finally, mice treated with STF exhibited significantly fewer metabolically active and M1-like macrophages in the AT compared to those under vehicle conditions. Overall, the authors conclude that targeting IRE1a has therapeutical potential for treating obesity and insulin resistance.

The study has some strengths, such as the detailed characterization of the effect of STF in different fat depots and a thorough analysis of macrophage populations. However, the lack of novelty in the findings somewhat limits the study´s impact on the field.

We thank the reviewer for the appreciation of our findings. We would use the opportunity to highlight several novelties. First, we characterized the relationship between the newly discovered CD9⁺ ATMs and the “M1-like” CD11c+ ATMs. Second, we demonstrated that M2 macrophage population was not reduced but instead increased in adipose tissue in obesity. Third, IRE1 inhibition does not improve thermogenesis by boosting M2 population, but instead, IRE1 inhibition suppresses pro-inflammatory macrophage populations including the M1-like ATMs.

Reviewer #3 (Public review):

Summary:

The manuscript by Wu D. et al. explores an innovative approach in immunometabolism and obesity by investigating the potential of targeting macrophage Inositol-requiring enzyme 1α (IRE1α) in cases of overnutrition. Their findings suggest that pharmacological inhibition of IRE1α could influence key aspects such as adipose tissue inflammation, insulin resistance, and thermogenesis. Notable discoveries include the identification of High-Fat Diet (HFD)-induced CD9⁺ Trem2+ macrophages and the reversal of metabolically active macrophages' activity with IRE1α inhibition using STF. These insights could significantly impact future obesity treatments.

Strengths:

The study's key strengths lie in its identification of specific macrophage subsets and the demonstration that inhibiting IRE1α can reverse the activity of these macrophages. This provides a potential new avenue for developing obesity treatments and contributes valuable knowledge to the field.

Weaknesses:

The research lacks an in-depth exploration of the broader metabolic mechanisms involved in controlling diet-induced obesity (DIO). Addressing this gap would strengthen the understanding of how targeting IRE1α might fit into the larger metabolic landscape.

We thank the reviewer for the appreciation of strengths in our manuscript. In particular, we appreciate the reviewer’s recommendation on the exploration of broader metabolic landscape, such as the effect of IRE1 inhibition on non-adipose tissue macrophages and metabolism. We agree that achieving these will certainly broaden the therapeutic potential of IRE1 inhibition to larger metabolic disorders and we will pursue these explorations in future studies.

Impact and Utility:

The findings have the potential to advance the field of obesity treatment by offering a novel target for intervention. However, further research is needed to fully elucidate the metabolic pathways involved and to confirm the long-term efficacy and safety of this approach. The methods and data presented are useful, but additional context and exploration are required for broader application and understanding.

Comments on revisions:

The author has revised the manuscript and addressed the most relevant comments raised by the reviewers. The paper is now significantly improved, though two minor issues remain.

(1) Studies were limited to male mice; this should be mentioned in the paper's Title.

Thanks for comment. We have modified the title to reflect the male mice only.

(2) Please include the sample size (n=) in all provided tables in the main manuscript and supplementary tables.

We have included the sample size in the main manuscript.

eLife Assessment

This manuscript presents important findings on a bacterial effector involved in plant symbiotic signaling. The effector proteolytically targets a key receptor while its activity is counteracted by host-mediated phosphorylation, revealing a dynamic interplay that fine-tunes symbiotic interactions. The evidence supporting these claims is solid, and the findings have potential signaling implications beyond bacterial interactions with plants.

Reviewer #1 (Public review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand, they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effectorthat cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants. Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo, and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al. found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

The presented data support the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions), since Agrobacterium as a closely rhizobia related bacterium might increase defense related proteolytic activity in the plant host cells, and these controls are provided.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells, the authors build largely on Western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). The authors discuss how the loss of NFR5 function (loss of cell death, impact on symbiosis) can be explained despite this vast excess of intact NFR5, but do not further explore the impact of this ratio on downstream signaling.

Reviewer #2 (Public review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

Comments on the revised version:

My concerns regarding the potential function of NopT during nodule symbiosis have been adequately addressed in the revised manuscript. Therefore, I have no further questions about this version, aside from a few minor suggestions:

(1) Please carefully check the text formatting throughout the manuscript to ensure consistency with scientific conventions and the journal's standards. For example, Line 105-117 and line119-131.<br /> (2) The term "detrimental" in line 624 may not accurately describe the function of NopT in rhizobial infection. Since the authors propose that NopT proteolytically cleaves NFR5 and suppresses NF signaling as a potential fine-tuning mechanism for legume symbiosis, a more precise term may be needed.<br /> (3) Lines 632-634 are somewhat unclear. If NopT serves as a strategy for rhizobia to evade detection by plant immunity, then knocking out NopT should, in theory, inhibit rhizobial infection. Clarification on this point would be beneficial.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effector that cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo. and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al., found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

The authors present evidence supporting the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions) that have been provided, since Agrobacterium as a closely rhizobia-related bacterium might increase defense related proteolytic activity in the plant host cells.

We appreciate your recognition of the importance of appropriate controls in our experimental design. In response to your comments, we revised our manuscript to ensure that the figures and legends provide a clear description of the controls used. We also included a more detailed description of our experimental design at several places. In particular, we have highlighted the use of the protease-dead version of NopT as a control (NopT^C93S). Therefore, NFR5-GFP cleavage in N. benthamiana clearly depended on protease activity of NopT and not on Agrobacterium (Fig. 3A). In the revised text, we carefully revied the conclusion and do not conclude at this stage that NopT proteolyzes NFR5. However, our subsequent experiments, including in vitro experiments, clearly show that NopT is able to proteolyze NFR5.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells the authors build largely on western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Thank you for your comments regarding the cleavage of NFR5 by NopT and its functional implications. We acknowledge that our immunoblots indicate only a relatively small proportion of the NFR5 cleavage product. Possible explanations could be as follows:

(1) The presence of full-length NFR5 does not preclude a significant impact of NopT on function of NFR5, as NopT is able to interact with NFR5. In other words, the NopT-NFR5 and NopT-NFR1 interactions at the plasma membrane might influence the function of the NFR1/NFR5 receptor without proteolytic cleavage of NFR5. In fact, protease-dead NopT^C93S expressed in NGR234ΔnopT showed certain effects in L. japonicus (less infection foci were formed compared to NGR234ΔnopT Fig. 5E). In this context, it is worth mentioning that the non-acylated NopT^C93S (Fig. 1B) and NopT_USDA257 (Fig. 6B) proteins were unable to suppress NFR1/NFR5-induced cell death in N. benthamina, but this could be explained by the lack of acylation and altered subcellular localization.

(2) In the cleavage assay, only small portion of NFR5 could be detected for cleavage by NopT. However, this cleavage might be sufficient to suppress signaling pathways, leading to the observed phenotypic changes (loss of cell death in N. benthamiana; altered infection in L. japonicus). We do believe this is a great point, therefore, we carefully revised the conclusion about this point. Throughout the paper, we stated that the cleavage of NFR5 suppresses symbiotic signaling but not disrupt the symbiotic signaling. We also removed the conclusion that cleavage of NFR5 by NopT results in the function loss of NFR5.

(3) N. benthamiana co-expressing NFR1/NFR5 leads to strong cell death, which suggest that the NFR1 kinase activity might be constitutively active even in the absence of Nod factors. But why co-expression of symbiotic receptor leads to cell death and how kinase activity is active in the absence of Nod factor are not clear, which is of great interest to be studied.

(4) The proteolytic activity of NopT may be reduced by the interaction of NopT with other proteins such as NFR1, which phosphorylates NopT and inactivates its protease activity.

In our revised manuscript version, we provide now quantitative data for the efficiency of NFR5 cleavage by NopT in different expression systems used (Figure 3 and Supplemental Fig. 16). We have also improved our Discussion in this context.  

Comments on latest version:

The presentation of the figures and the language has greatly improved and the specific mistakes pointed out in the last review have been corrected. I especially appreciate the new images used to illustrate the observed mutant phenotypes, which are much clearer and easier to understand. The pictures used to illustrate the mutant phenotypes seem to be of more comparable root regions than before. Overall, the requested changes have been implemented, with some exceptions described below.

• Figure 1: New representative images are shown for BAX1 and CERK1. These pictures are more consistent with the phenotype seen in other treatments, but since the data has not changed, I presume the data from leaf discs (where the leaf discs for these treatments looked very different) previously shown is still included. The criteria for what was considered cell death is in my opinion still not described in the legend. The cell death/total ratio has been added for all leaf discs, as requested.

Thank you so much for carefully pointing out this. Cell death in leaf disc results in the formation of necrotic plaques, which restrains pathogens within deceased cells. These plaques commonly manifest as leaf dehydration, frequently accompanied by a translucent appearance. Brown and shriveled leaf discs serve as indicators of cell death. We have added these descriptions in the figure legend of Figure 1.

• Figure 2: the discussion of the figure now emphasizes direct protein interaction. There is still no size marker in 2D or a description of size in the figure legend, making it difficult to compare the result to Figure 3. If I understand the rebuttal comments correctly, there are other bands on the blot, including non-specific bands. This does not negate the need to include the full blot as a supplemental figure to show cleaved NFR5 as well as other bands. I do not see any other clarifications on this subject in the manuscript.

Thank you for your suggestion. In the revised manuscript, we have included the kDa range for all proteins detected in Figure.2D. The full blot of Co-IP assay was shown in Fig S2 (a new supplemental data). Yes, we detected some smaller bands after immunoblot, but we cannot give clear conclusion of what these bands are based on the current study. Interestingly, these smaller bands were immunoprecipitated by anti-FLAG beads, suggesting that these bands are some truncated peptides from NFR5.

• Figure 5: From the pictures, it is now easier to understand what is meant by "infection foci". Although there is no description in the methods of how these were distinguished from infection threads, I believe the images are clear enough.

Thank you for your helpful comment. In the revised manuscript, we have added the descriptions about this experiment in the method section and in the legend in Figure 5A.

• Figure 6: The changes in the discussion are appreciated, but panel E still misrepresents the evidence in the paper, as from the drawing it still seems that the cleaved NFR5 is somehow directly responsible for suppressing infection when this was not shown.

Thank you for your thoughtful comments. We appreciate your suggestion to the schematic model to illustrate the cleavage of NFR5 to suppressing rhizobia infection. In the revised manuscript, we have changed the model in Figure 6E.

Reviewer #2 (Public review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

We appreciate your attention to these plant-specific differences. Previous studies showed that NopT expressed in tobacco (N. tabacum) or in specific Arabidopsis ecotypes (with PBS1/RPS5 genes) causes rapid cell death (Dai et al. 2008; Khan et al. 2022). Khan et al. 2022 reported recently that cell death does not occur in N. benthamiana unless the leaves were transformed with PBS1/RPS5 constructs. Our data shown in Fig. S17 confirm these findings. As cell death is usually associated with induction of plant protease activities, we considered N. tabacum and A. thaliana plants as not suitable for testing NFR5 cleavage by NopT. In fact, no NopT/NFR5 experiments were not performed with these plants in our study. In response to your comment, we now better describe the N. benthamiana expression system and cite the previous articles_. Furthermore, we have revised the Discussion section to better emphasize effector-induced immunity in non-host plants and the negative effect of rhizobial effectors during symbiosis. Our revisions certainly provide a clearer understanding of the advantages and limitations of the _N. benthamiana expression system.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

Thank you for this comment, which points out that we did not address this aspect precisely enough in the original manuscript version. We improved our manuscript and now write that nfr1 and nfr5 mutants do not produce nodules (Madsen et al., 2003; Radutoiu et al., 2003) and that over-expression of either NFR1 or NFR5 can activate NF signaling, resulting in formation of spontaneous nodules in the absence of rhizobia (Ried et al., 2014). In fact, compared to the nopT knockout mutant NGR234ΔnopT, wildtype NGR234 (with NopT) is less successful in inducing infection foci in root hairs of L. japonicus (Fig. 5). With respect to formation of nodule primordia, we repeated our inoculation experiments with NGR234ΔnopT and wildtype NGR234 and also included a nopT over-expressing NGR234 strain into the analysis. Our data clearly showed that nodule primordium formation was negatively affected by NopT. The new data are shown in Fig. 5 of our revised version. Our data show that NGR234 infection is not really successful, especially when NopT is over-expressed. This is consistent with our observations that NopT targets Nod factor receptors in L. japonicus and inhibits NF signaling (NIN promoter-GUS experiments). Our findings indicate that NopT might be an “Avr effector” for L. japonicus. However, in other host plants of NGR234, NopT possesses a symbiosis-promoting role (Dai et al. 2008; Kambara et al. 2009). Such differences could be explained by different NopT targets in different plants (in addition to Nod factor receptors), which may influence the outcome of the infection process. Indeed, our work shows that NopT can interact with various kinase-dead LysM domain receptors, suggesting a role of NopT in suppression or activation of plant immunity responses depending on the host plant. We discuss such alternative mechanisms in our revised manuscript version and emphasize the need for further investigation to elucidate the precise mechanisms underlying the observed infection phenotype and the role of NopT in modulating symbiotic signaling pathways. In this context, we would also like to mention the new figures of our manuscript which are showing (i) the efficiency of NFR5 cleavage by NopT in different expression systems (Figure 3), (ii) the interaction between NopT^C93S and His-SUMO-NFR5JM-GFP (Supplementary Fig. 5), and (iii) cleavage of His-SUMO-NFPJM-GFP by NopT (Supplementary Figs. S8 and S9).

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

Thank you for mentioning this point. We are aware of the possible paradox that the broad-host-range strain NGR234 produces an effector that appears to restrict its infection of host plants. As mentioned in our answer to the previous comment, NopT could have additional functions beyond the regulation of Nod factor signaling. In our revised manuscript version, we have modified our text as follows:

(1) We mention the potential evolutionary aspects of NopT-mediated regulation of rhizobial infection and discuss the possibility that interactions between NopT and Nod factor receptors may have evolved to fine-tune Nod factor signaling to avoid rhizobial hyperinfection in certain host legumes.

(2) We also emphasize that the presence of NopT may confer selective advantages in other host plants than L. japonicus due to interactions with proteins related to plant immunity. Like other effectors, NopT could suppress activation of immune responses (suppression of PTI) or cause effector-triggered immunity (ETI) responses, thereby modulating rhizobial infection and nodule formation. Interactions between NopT and proteins related to the plant immune system may represent an important evolutionary driving force for host-specific nodulation and explain why the presence of NopT in NGR234 has a negative effect on symbiosis with L. japonicus but a positive one with other legumes.

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

We also thank for this comment. We have revised the Discussion section of our manuscript and discuss now our failure to generate stable transgenic L. japonicus plants expressing NopT. We observed that the protease activity of NopT in aerial parts of L. japonicus had a negative effect on plant development, whereas NopT expression in hairy roots was possible. Such differences may be explained by different NopT substrates in roots and aerial parts of the plant. In this context, we also discuss our finding that NopT not only cleaves NFR5 but is also able to proteolyze other proteins of L. japonicus such as LjLYS11, suggesting that NopT not only suppresses Nod factor signaling, but may also interfere with signal transduction pathways related to plant immunity. We speculate that, depending on the host legume species, NopT could suppress PTI or induce ETI, thereby modulating rhizobial infection and nodule formation.

Comments on revised version:

This version has effectively addressed most of my concerns. However, one key issue remains unresolved regarding the mechanism of NopT in regulating nodule symbiosis. Specifically, the explanation of how NopT catabolizes NFR5 to regulate symbiosis is still not convincing within the current framework of plant-microbe interaction, where plants are understood to genetically control rhizobial colonization.

While alternative regulatory mechanisms in plant-microbe interactions are plausible, the notion that the NRG234-secreted effector NopT could reduce its own infection by either suppressing plant immunity or degrading the symbiosis receptor remains unsubstantiated. I believe further revisions are needed in the discussion section to more clearly address and clarify these findings and any lingering uncertainties.

We appreciate your positive comments on the reason why NopT catabolizes NFR5 to regulate symbiosis. NopT belongs to pathogen effecftors YopT family and also cleavage Arabidopsis AtLYK5 and L. japonicus LjLYS11 which trigger immunity responses in plants. NFR5, AtLYK5 and LjLYS11 has the conserved amino acid motif at the juxtamembrane domain, leading to cleaving NFR5 by NopT during symbiosis. Besides, in plant-microbe interaction, effector HopB1 cleaves immune co-receptor BAK1 at the kinase domain to inhibit plant defense. The effect on cleavage of receptor may be positive or negative. NopT suppressing symbiosis may avoid preventing hyperinfection in the specific interaction between rhizobia and legumes. In the revised manuscript, we have emphasized this point more clearly in why NopT could reduce its own infection by either suppressing plant immunity in discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Evaluation of the author's responses to the reviewer comments during the first review round

Reviewer's Comment:

Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with NopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Summary of response:

• NopT could be interfering with the NFR1/NFR5 complex without proteolytic cleavage

• The cleaved fraction may still be sufficient to disrupt signaling pathways

• Elevated abundance of NFR5 relative to WT levels

• Add quantitative data for efficiency of NFR5 cleavage in different systems

Evaluation of response:

• The quantification of NFR5 cleavage efficiency is welcome, and there is some discussion of the possible reasons for the large proportion of uncleaved NFR5. It is clear that there is a large difference in cleavage efficiency between L. japonicus roots and N. benthamiana.

• The data is shown as a bar plot. Given that only 3 biological replicates are used, the data points should be shown, and there is too little data to provide sensible error bars. It would be better to simply make a dot-plot and indicate the mean for each sample. However, the main aim of the comment is addressed.

Thank you for your constructive comments regarding Figure S16. In the revised manuscript, we have presented these data into dot-Plot format.

Reviewer's Comment:

It is also difficult to evaluate how the ratios of cleaved and full-length protein change when different versions of NopT are present without a quantification of band strengths normalized to loading controls (Figure 3C, 3D, 3F). The same is true for the blots supporting NFR1 phosphorylation of NopT (Figure 4A).

Summary of response:

• Quantified proportion of cleaved and full length NFR5 in different systems (S14)

• Band strengths of immunoblots quantified (4B)

Evaluation of response:

• The quantification has been performed as requested and the data is shown as bar plots. This type of data is frequently displayed as part of the blot figure itself, printed under each respective lane, making it easier for the reader to connect the ratios to the band sizes. If data is shown in a plot, the data points should be shown on the plot, as described above.

Thank you for your constructive comments regarding Figure 3. In the revised manuscript, we have added the cleavage efficiency in the 3A-3D.

Reviewer's Comment:

Nodule primordia and infection threads are still formed when L. japonicus plants are inoculated with ∆nopT mutant bacteria, but it is not clear if these primordia are infected or develop into fully functional nodules (Figure 5). A quantification of the ratio of infected and non-infected nodules and primordia would reveal whether NopT is only active at the transition from infection focus to thread or perhaps also later in the bacterial infection process of the developing root nodule.

Summary of response:

• Additional experiments with NGR234 or NGR234ΔnopT mutants find no non-infected nodules (fig. 5)

Evaluation of response:

• The requested quantification has been done, although the support for the findings would be stronger if also mature nodules per plant were quantified and plotted. If non-infected nodules were neither present in NGR234 or NGR234ΔnopT, it would still be advisable to include images of cross-sections of the fully-developed nodules.

We appreciate your positive comments on the cross-sections of the fully-developed nodules. In the revised manuscript, we have added the cross-section images of nodules in the Figure S12.

eLife Assessment

This study leverages an impressive and comprehensive longitudinal 16S rRNA gut microbiome dataset from baboons to provide important insight regarding the use of a microbiome-based clock to predict biological age. The evidence for age-associated microbiome features and environmental and social variables that impact microbiome aging is convincing. This study of microbiomes as markers of host age will fuel inquiries and studies and interest a broad range of researchers, especially those interested in alternatives to measuring biological aging.

Reviewer #1 (Public review):

Summary:

The authors used a subset of a very large, previously generated 16S dataset to: 1) assess age-associated features; and 2) develop a fecal microbiome clock, based on extensive longitudinal sampling of wild baboons for which near-exact chronological age is known. They further seek to understand deviation from age-expected patterns and uncover if and why some individuals have an older or younger microbiome than expected, and the health and longevity implications of such variation. Overall, the authors compellingly achieved their goals to discover age-associated microbiome features and develop a fecal microbiome clock. They also showed clear and exciting evidence for sex and rank-associated variation in the pace of gut microbiome aging and impacts of seasonality on microbiome age in females. These data add to a growing understanding of modifiers of the pace of age in primates, and links among different biological indicators of age, with implications for understanding and contextualizing human variation. However, in the current version there are gaps in the analyses with respect to the social environment, and in comparisons with other biological indicators of age. Despite this, I anticipate this work will be impactful, generate new areas of inquiry and fuel additional comparative studies.

Strengths:

The major strengths of the paper are the size and sampling depth of the study population, including ability to characterize of the social and physical environments, and the application of recent and exciting methods to characterize the microbiome clock. An additional strength was the ability of the authors to compare and contrast the relative age-predictive power of the fecal microbiome clock to other biological methods of age estimation available for the study population (dental wear, blood cell parameters, methylation data). Furthermore, the writing and support materials are clear and informative and visually appealing.

Revisions made following initial review have further improved the content and clarity.

Weaknesses:

Revisions to the manuscript clarified some of the analysis decisions and limitations regarding drawing comparisons between the microbiome clock and other metrics of biological age, and on the impact of sociality on microbiome metrics. Hopefully these interesting topics will be further addressed in forthcoming publications.

Reviewer #2 (Public review):

Summary:

Dasari et al present an interesting study investigating the use of 'microbiota age' as an alternative to other measures of 'biological age'. The study provides several curious insights into biological ageing. Although 'microbiota age' holds potential as a proxy of biological age, it comes with limitations considering the gut microbial community can be influenced various non-age related factors, and various age-related stressors may not manifest in changes in the gut microbiota.

Strengths:

The dataset this study is based on is impressive, and can reveal various insights into biological ageing and beyond. The analysis implemented is extensive and of high level.

Weaknesses:

The key weakness is the use of microbiota age instead of e.g., DNA-methylation based epigenetic age as a proxy of biological ageing, for reasons stated in the summary. DNA methylation levels can be measured from faecal samples, and as such epigenetic clocks too can be non-invasive.

In the first round of review, I provided authors a list of minor edits, which they have implemented in the revised version of the manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors used a subset of a very large, previously generated 16S dataset to:<br /> (1) Assess age-associated features; and (2) develop a fecal microbiome clock, based on an extensive longitudinal sampling of wild baboons for which near-exact chronological age is known. They further seek to understand deviation from age-expected patterns and uncover if and why some individuals have an older or younger microbiome than expected, and the health and longevity implications of such variation. Overall, the authors compellingly achieved their goals of discovering age-associated microbiome features and developing a fecal microbiome clock. They also showed clear and exciting evidence for sex and rank-associated variation in the pace of gut microbiome aging and impacts of seasonality on microbiome age in females. These data add to a growing understanding of modifiers of the pace of age in primates, and links among different biological indicators of age, with implications for understanding and contextualizing human variation. However, in the current version, there are gaps in the analyses with respect to the social environment, and in comparisons with other biological indicators of age. Despite this, I anticipate this work will be impactful, generate new areas of inquiry, and fuel additional comparative studies.

Thank you for the supportive comments and constructive reviews.

Strengths:

The major strengths of the paper are the size and sampling depth of the study population, including the ability to characterize the social and physical environments, and the application of recent and exciting methods to characterize the microbiome clock. An additional strength was the ability of the authors to compare and contrast the relative age-predictive power of the fecal microbiome clock to other biological methods of age estimation available for the study population (dental wear, blood cell parameters, methylation data). Furthermore, the writing and support materials are clear, informative and visually appealing.

Weaknesses:

It seems clear that more could be done in the area of drawing comparisons among the microbiome clock and other metrics of biological age, given the extensive data available for the study population. It was confusing to see this goal (i.e. "(i) to test whether microbiome age is correlated with other hallmarks of biological age in this population"), listed as a future direction, when the authors began this process here and have the data to do more; it would add to the impact of the paper to see this more extensively developed.

Comparing the microbiome clock to other metrics of biological age in our population is a high priority (these other metrics of biological age are in Table S5 and include epigenetic age measured in blood, the non-invasive physiology and behavior clock (NPB clock), dentine exposure, body mass index, and blood cell counts (Galbany et al. 2011; Altmann et al. 2010; Jayashankar et al. 2003; Weibel et al. 2024; Anderson et al. 2021)). However, we have opted to test these relationships in a separate manuscript. We made this decision because of the complexity of the analytical task: these metrics were not necessarily collected on the same subjects, and when they were, each metric was often measured at a different age for a given animal. Further, two of the metrics (microbiome clock and NPB clock) are measured longitudinally within subjects but on different time scales (the NPB clock is measured annually while microbiome age is measured in individual samples). The other metrics are cross-sectional. Testing the correlations between them will require exploration of how subject inclusion and time scale affect the relationships between metrics.

We now explain the complexity of this analysis in the discussion in lines 447-450. In addition, we have added the NPB clock (Weibel et al. 2024) to the text in lines 260-262 and to Table S5.

An additional weakness of the current set of analyses is that the authors did not explore the impact of current social network connectedness on microbiome parameters, despite the landmark finding from members of this authorship studying the same population that "Social networks predict gut microbiome composition in wild baboons" published here in eLife some years ago. While a mother's social connectedness is included as a parameter of early life adversity, overall the authors focus strongly on social dominance rank, without discussion of that parameter's impact on social network size or directly assessing it.

Thank you for raising this important point, which was not well explained in our manuscript. We find that the signatures of social group membership and social network proximity are only detectable our population for samples collected close in time. All of the samples analyzed in  Tung et al. 2015 (“Social networks predict gut microbiome composition in wild baboons”) were collected within six weeks of each other. By contrast, the data set analyzed here spans 14 years, with very few samples from close social partners collected close in time. Hence, the effects of social group membership and social proximity are weak or undetectable. We described these findings in Grieneisen et al. 2021 and Bjork et al. 2022, and we now explain this logic on line 530, which states, “We did not model individual social network position because prior analyses of this data set find no evidence that close social partners have more similar gut microbiomes, probably because we lack samples from close social partners sampled close in time (Grieneisen et al. 2021; Björk et al. 2022).”

We do find small effects of social group membership, which is included as a random effect in our models of how each microbiome feature is associated with host age (line 529) and our models predicting microbiome Dage (line 606; Table S6).

Reviewer #2 (Public review):

Summary:

Dasari et al present an interesting study investigating the use of 'microbiota age' as an alternative to other measures of 'biological age'. The study provides several curious insights into biological aging. Although 'microbiota age' holds potential as a proxy of biological age, it comes with limitations considering the gut microbial community can be influenced by various non-age related factors, and various age-related stressors may not manifest in changes in the gut microbiota. The work would benefit from a more comprehensive discussion, that includes the limitations of the study and what these mean to the interpretation of the results.

We agree and have text to the discussion that expands on the limitations of this study and what those limitations mean for the interpretation of the results. For instance, lines 395-400 read, “Despite the relative accuracy of the baboon microbiome clock compared to similar clocks in humans, our clock has several limitations. First, the clock’s ability to predict  individual age is lower than for age clocks based on patterns of DNA methylation—both for humans and baboons (Horvath 2013; Marioni et al. 2015; Chen et al. 2016; Binder et al. 2018; Anderson et al. 2021). One reason for this difference may be that gut microbiomes can be influenced by several non-age-related factors, including social group membership, seasonal changes in resource use, and fluctuations in microbial communities in the environment”

In addition, lines 405-411 now reads, “Third, the relationships between potential socio-environmental drivers of biological aging and the resulting biological age predictions were inconsistent. For instance, some sources of early life adversity were linked to old-for-age gut microbiomes (e.g., males born into large social groups), while others were linked to young-for-age microbiomes (e.g., males who experienced maternal social isolation or early life drought), or were unrelated to gut microbiome age (e.g., males who experienced maternal loss; any source of early life adversity in females).”

Strengths:

The dataset this study is based on is impressive, and can reveal various insights into biological ageing and beyond. The analysis implemented is extensive and high-level.

Weaknesses:

The key weakness is the use of microbiota age instead of e.g., DNA-methylation-based epigenetic age as a proxy of biological ageing, for reasons stated in the summary. DNA methylation levels can be measured from faecal samples, and as such epigenetic clocks too can be non-invasive. I will provide authors a list of minor edits to improve the read, to provide more details on Methods, and to make sure study limitations are discussed comprehensively.

Thank you for this point. In response, we have deleted the text from the discussion that stated that non-invasive sampling is an advantage of microbiome clocks. In addition, we now propose a non-invasive epigenetic clock from fecal samples as an important future direction for our population (see line 450).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Abstract - The opening 2 sentences are not especially original or reflective of the potential value/ premise of the study. Members of this team have themselves measured variation in biological age in many different ways, and the implication that measuring a microbiome clock is easy or straightforward is not compelling. This paper is very interesting and provides unique insight, but I think overall there is a missed opportunity in the abstract to emphasize this, given the innovative science presented here. Furthermore, the last 2 sentences of the abstract are especially interesting - but missing a final statement on the broader significance of research outside of baboons.

We appreciate these comments and have revised the Abstract accordingly. The introductory sentences now read, “Mammalian gut microbiomes are highly dynamic communities that shape and are shaped by host aging, including age-related changes to host immunity, metabolism, and behavior. As such, gut microbial composition may provide valuable information on host biological age.” (lines 31-34). The last two sentences of the abstract now read, “Hence, in our host population, gut microbiome age largely reflects current, as opposed to past, social and environmental conditions, and does not predict the pace of host development or host mortality risk. We add to a growing understanding of how age is reflected in different host phenotypes and what forces modify biological age in primates.” (lines 40-43).

If possible, it would be highly useful to present some comments on concordance in patterns at different levels. Are all ASVs assessed at both the family and genus levels? Do they follow similar patterns when assessed at different levels? What can we learn about the system by looking at different levels of taxonomic assignment?

The section on relationships between host age and individual microbiome features is already lengthy, so we have not added an analysis of concordance between different taxonomic levels. However, we added a justification for why we tested for age signatures in different levels of taxa to line 171, which reads, “We tested these different taxonomic levels in order to learn whether the degree to which coarse and fine-grained designations categories were associated with host age.”

To calculate the delta age - please clarify if this was done at the level of years, as suggested in Figure 3C, or at the level of months or portion months, etc?

Delta age is measured in years. This is now clarified in lines 294, 295, and 578.

Spelling mistake in table S12, cell B4 (Octovber)

Thank you. This typo has been corrected.

Given the start intro with vertebrates, the second paragraph needs some tweaking to be appropriate. Perhaps, "At least among mammals, one valuable marker of biological aging may lie in the composition and dynamics of the mammalian gut microbiome (7-10)." Or simply remove "mammalian".

We have updated this sentence based on your suggestions in line 54. It reads, “In mammals, one valuable marker of biological aging may lie in the composition and dynamics of the gut microbiome (Claesson et al. 2012; Heintz and Mair 2014; O’Toole and Jeffery 2015; Sadoughi et al. 2022).”

A rewrite at the end of the introduction is needed to avoid the almost direct repetition in lines 115-118 and 129-131 (including lit cited). One potentially effective way to approach this is to keep the predictions in the earlier paragraph and then more clearly center the approach and the overarching results statement in the latter paragraph. (I.e., "we find that season and social rank have stronger effects on microbiome age than early life events. Further, microbiome age does not predict host development or mortality.").

Thank you for pointing this out. We have re-organized the predictions in the introduction based on your suggestion. The alternative “recency effects” model now appears in the paragraph that starts in line 110. The final paragraph then centers on the overall approach and the results statement (lines 128-140)

Be clear in each case where taxon-level trends are discussed if it's at Family, Genus, or other level. It's there most, but not all, of the time.

We have gone through the text and clarified what taxa or microbiome feature was the subject of our analyses in any places where this was not clear.

In the legend for Figure 2, add clarification for how values to right versus left of the centered value should be interpreted with respect to age (e.g. "values to x of the center are more abundant in older individuals").

We now clarify in Figure 2C and 2D that “Positive values are more abundant in older hosts”.

Figure 3 - Are Panels A, B, and C all needed - can the value for all individuals not also be overlaid in the panel showing sex differences and the same point showing individuals with "old" and "young" microbiomes be added in the same plot if it was slightly larger?

We agree and have simplified Figure 3. We reduced the number of panels from three to two, and we added the information about how to calculate delta age to Panel A. We also moved the equation from the top of Panel C to the bottom right of Panel A.

Reviewer #2 (Recommendations for the authors):

Dasari et al present an interesting study investigating the use of 'microbiota age' as an alternative to other measures of 'biological age'. The study provides several curious insights which in principle warrant publication. However, I do think the manuscript should be carefully revised. Below I list some minor revisions that should be implemented. Importantly, the authors should discuss in the Discussion the pros and cons of using 'microbiota age' as a proxy of 'biological age'. Further, the authors should provide more information on Methods, to make sure the study can be replicated.

Thank you for these important points. Based on your comments and those of the first reviewer, we have expanded our discussion of the limitations of using microbiota age as a proxy for biological age (see edits to the paragraph starting in line 395).

We have also expanded our methods around sample collection, DNA extraction, and sequencing to describe our sampling methods, strategies to mitigate and address possible contamination, and batch effects. See lines 483-490 and our citations to the original papers where these methods are described in detail.

(1) Lines 85-99: I think this paragraph could be revisited to make the assumptions clearer. For instance, the last sentence is currently a little confusing: are authors expecting males to exhibit old-for-age microbiomes already during the juvenile period?

This prediction has been clarified. Line 96 now reads, “Hence, we predicted that adult male baboons would exhibit gut microbiomes that are old-for-age, compared to adult females (by contrast, we expected no sex effects on microbiome age in juvenile baboons).”

(2) Lines 118-121: Could the authors discuss this assumption in relation to what has been observed e.g., in humans in terms of delays in gut microbiome development? Delayed/accelerated gut microbiome development has been studied before, so this assumption would be stronger if related to what we know from previous studies.

This comment refers to the sentence which originally stated, “However, we also expected that some sources of early life adversity might be linked to young-for-age gut microbiota. For instance, maternal social isolation might delay gut microbiome development due to less frequent microbial exposures from conspecifics.” We have slightly expanded the text here (line 117) to explain our logic. We now include citations for our predictions. We did not include a detailed discussion of prior literature on microbiome development in the interest of keeping the same level of detail across all sections on our predictions.

(3) As the authors discuss, various adversities can lead to old-for-age but also young-for-age microbiome composition. This should be discussed in the limitations.

We agree. This is now discussed in the sentence starting at line 371, which reads, “…deviations from microbiome age predictions are explained by socio-environmental conditions experienced by individual hosts, especially recent conditions, although the effect sizes are small and are not always directionally consistent.” In addition, the text starting at line 405 now reads, “Third, the relationships between potential socio-environmental drivers of biological aging and the resulting biological age predictions were inconsistent. For instance, some sources of early life adversity were linked to old-for-age gut microbiomes (e.g., males born into large social groups), while others were linked to young-for-age microbiomes (e.g., males who experienced maternal social isolation or early life drought), or were unrelated to gut microbiome age (e.g., males who experienced maternal loss; any source of early life adversity in females).”

(4) In various places, e.g., lines 129-131, it is a little unclear at what chronological age authors are expecting microbiota to appear young/old-for-age.

This sentence was removed while responding to the comments from the first reviewer.

(5) Lines 132-133: this statement could be backed by stating that this is because the gut microbiota can change rapidly e.g., when diet changes (or whatever the authors think could be behind this).

We have added an expository sentence at line 123, including new citations. This sentence reads, “Indeed, gut microbiomes are highly dynamic and can change rapidly in response to host diet or other aspects of host physiology, behavior, or environments”.

We now cite:

· Hicks, A.L., et al. (2018). Gut microbiomes of wild great apes fluctuate seasonally in response to diet. Nature Communications 9, 1786.

· Kolodny, O., et al. (2019). Coordinated change at the colony level in fruit bat fur microbiomes through time. Nature Ecology & Evolution 3, 116-124.

· Risely, A., et al. (2021) Diurnal oscillations in gut bacterial load and composition eclipse seasonal and lifetime dynamics in wild meerkats. Nat Commun 12, 6017.

(6) Lines 135-137: current or past season and social rank? This paragraph introduces the idea that it could be past rather than current socio-environmental factors that might predict microbiota age, so the authors should clarify this sentence.

We have clarified the information in this sentence. line 135 now reads, “In general, our results support the idea that a baboon’s current socio-environmental conditions, especially their current social rank and the season of sampling, have stronger effects on microbiome age than early life events—many of which occurred many years prior to sampling.”

(7) Lines 136-137: this sentence could include some kind of a conclusion of this finding. What might this mean?

We have added a sentence at line 138, which speculates that, “…the dynamism of the gut microbiome may often overwhelm and erase early life effects on gut microbiome age.”

(8) Use 'microbiota' or 'microbiome' across the manuscript; currently, the terms are used interchangeably. I don't have a strong opinion on this, although typically 'microbiota' is used when data comes from 16S rRNA.

We have updated the text to replace any instance of “microbiota” with “microbiome”. We use the term microbiome in the sense of this definition from the National Human Genome Research Institute, which defines a microbiome as “the community of microorganisms (such as fungi, bacteria and viruses) that exists in a particular environment”.

(9) Figure 1 legend: make sure to unify formatting; e.g., present sample sizes as N= or n=, rather than both, and either include or do not include commas in 4-digit values (sample sizes).

We have checked the formatting related to sample sizes and the use of commas in 4-digits in the main text and supplement. The formats are now consistent.

(10) Line 166: relative abundances surely?

Following Gloor et al. (2017), our analyses use centered log-ratio (CLR) transformations of read counts, which is the recommended approach for compositional data such as 16S rRNA amplicon read counts. CLR transformations are scale-invariant, so the same ratio is obtained in a sample with few read versus many reads. We now cite Gloor et al. (2017) at line 169 and in the methods in line 517, which reads “centered log ratio (CLR) transformed abundances (i.e., read counts) of each microbial phyla (n=30), family (n=290), genus (n=747), and amplicon sequence variance (ASV) detected in >25% of samples (n=358). CLR transformations are a recommended approach for addressing the compositional nature of 16S rRNA amplicon read count data (Gloor et al. 2017).”  

(11) Lines 167-172: were technical factors, e.g., read depth or sequencing batch, included as random effects?

Thank you for catching this oversight in the text. We did model sequencing depth and batch effects. The sentence starting at line 173 now reads, “For each of these 1,440 features, we tested its association with host age by running linear mixed effects models that included linear and quadratic effects of host age and four other fixed effects: sequencing depth, the season of sample collection (wet or dry), the average maximum temperature for the month prior to sample collection, and the total rainfall in the month prior to sample collection (Grieneisen et al. 2021; Björk et al. 2022; Tung et al. 2015). Baboon identity, social group membership, hydrological year of sampling, and sequencing plate (as a batch effect) were modeled as random effects.”

(12) Lines 175-180: When discussing how these alpha diversity results relate to previous findings, the authors should be clear about whether they talk about weighted or non-weighted measures of alpha diversity. - also maybe this should be included in the discussion rather than the results? Please consider this when revisiting the manuscript (see how it reads after edits).

Richness is the only unweighted metric, which we now clarify in line 181. We opted to retain the interpretation in the text in its original location to maintain the emphasis in the discussion on the microbiome clock results.

(13) Table S1 is very hard to interpret in the provided PDF format as columns are not presented side-by-side. It is currently hard to check model output for e.g., specific families. This needs to be revisited.

We agree. We believe that eLife’s submission portal automatically generates a PDF for any supplementary item. However, we also include the supplementary tables as an Excel workbook which has the columns presented side-by-side.

(14) Line 184: taxa meaning what? Unclear what authors refer to with this sentence, taxa across taxonomic levels, or ASVs, or what does the 51.6% refer to?

We have edited line 191 to clarify that this sentence refers to taxa at all taxonomic levels (phyla to ASVs).

(15) Line 191: a punctuation mark missing after ref (81).

We have added the missing period at the end of this sentence.

(16) Lines 189-197: this should go into the discussion in my opinion.

We have opted to retain this interpretation, now at line 183.

(17) Lines 215-219: Not sure what this means; do the authors mean features were not restricted to age-associated taxa, ie also e.g., diversity and other taxa-independent patterns were included? If so, the rest of the highlighted lines should be revisited to make this clear, currently to me it is very unclear what 'These could include features that are not strongly age-correlated in isolation' means. Currently, that sounds like some features included were only age-associated in combination with other features, but unclear how this relates to taxa-dependency/taxa-independency.

We agree this was not clear. We have revised line 224 to read, “We included all 9,575 microbiome features in our age predictions, as opposed to just those that were statistically significantly associated with age because removing these non-significant features could exclude features that contribute to age prediction via interactions with other taxa.”

(18) Line 403-407: There is now a paper showing epigenetic clocks can be built with faecal samples, so this argument is not valid. Please revisit in light of this publication: https://onlinelibrary.wiley.com/doi/epdf/10.1111/mec.17330

Thank you for bringing this paper to our attention. We deleted the text that describes epigenetic clocks as invasive, and we now cite this paper in line 450, which reads, “We also hope to measure epigenetic age in fecal samples, leveraging methods developed in Hanski et al. 2024.”

(19) Line 427: a punctuation mark/semicolon missing before However.

We have corrected this typo.

(20) Lines 419-428: I don't quite understand this speculation. Why would the priority of access to food lead to an old-looking gut microbiome? This paragraph needs stronger arguments, currently unclear and also not super convincing.

We agree this was confusing. We have revised this text to clarify the explanation. The text starting at line 424 now reads, “This outcome points towards a shared driver of high social status in shaping gut microbiome age in both males and females. While it is difficult to identify a plausible shared driver, one benefit shared by both high-ranking males and females is priority of access to food. This access may result in fewer foraging disruptions and a higher quality, more stable diet. At the same time, prior research in Amboseli suggests that as animals age, their diets become more canalized and less variable (Grieneisen et al. 2021). Hence aging and priority of access to food might both be associated with dietary stability and old-for-age microbiomes. However, this explanation is speculative and more work is needed to understand the relationship between rank and microbiome age.”

(21) Line 434: remove 'be'.

We have corrected this typo.

(22) Line 478: add information on how samples were collected; e.g., were samples collected from the ground? How was cross-contamination with soil microbiota minimised? Were samples taken from the inner part of depositions? These factors can influence microbiota samples quite drastically so detailed info is needed. Also what does homogenisation mean in this context? How soon were samples freeze-dried after sample collection?

We have expanded our methods with respect to sample collection. This text starts in line 483 and reads, “Samples were collected from the ground within 15 minutes of defecation. For each sample, approximately 20 g of feces was collected into a paper cup, homogenized by stirring with a wooden tongue depressor, and a 5 g aliquot of the homogenized sample was transferred to a tube containing 95% ethanol. While a small amount of soil was typically present on the outside of the fecal sample, mammalian feces contains 1000 times the number of microbial cells in a typical soil sample (Sender, Fuchs, and Milo 2016; Raynaud and Nunan 2014), which overwhelms the signal of soil bacteria in our analyses (Grieneisen et al. 2021). Samples were transported from the field in Amboseli to a lab in Nairobi, freeze-dried, and then sifted to remove plant matter prior to long term storage at -80°C.”

(23) Line 480 onwards: were negative controls included in extraction batches? Were samples randomised into extraction batches?

Yes, we included extraction blanks. These are now described in lines 495-500. This text reads, “We included one extraction blank per batch, which had significantly lower DNA concentrations than sample wells (t-test; t=-50, p < 2.2x10-16; Grieneisen et al. 2021). We also included technical replicates, which were the same fecal sample sequenced across multiple extraction and library preparation batches. Technical replicates from different batches clustered with each other rather than with their batch, indicating that true biological differences between samples are larger than batch effects.”

(24) Were extraction, library prep, and sequencing negative controls included? Is data available?

We included extraction blanks (described above) and technical replicates, which were the same sample sequenced across multiple extraction and library preparation batches. Technical replicates from different batches clustered with each other rather than with their batch, indicating that true biological differences between samples are larger than batch effects.

We have updated the data availability statement to read, “All data for these analyses are available on Dryad at https://doi.org/10.5061/dryad.b2rbnzspv. The 16S rRNA gene sequencing data are deposited on EBI-ENA (project ERP119849) and Qiita (study 12949). Code is available at the following GitHub repository: https://github.com/maunadasari/Dasari_etal-GutMicrobiomeAge”.

(25) Line 562: how were corrected microbiome delta ages calculated? Currently, the authors state x, y and z factors were corrected for, but it is unclear how this was done.

The paragraph starting at line 577 describes how microbiome delta age was calculated. We have made only a few changes to this text because we were not sure which aspects of these methods confused the reviewer. However, briefly, we calculated sample-specific microbiome Dage in years as the difference between a sample’s microbial age estimate, age_m from the microbiome clock, and the host’s chronological age in years at the time of sample collection, age_c. Higher microbiome Dages indicate old-for-age microbiomes, as age_m > age_c, and lower values (which are often negative) indicate a young-for-age microbiome, where age_c > age_m (see Figure 3).

(26) Line 579: typo 'as'.

We have corrected this typo.

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eLife Assessment

This research is valuable as it investigates metabolic shuttling between photoreceptors and retinal pigment epithelium (RPE) using in vivo infusion techniques and mouse models. The authors find that the retina significantly relies on circulating glucose, with photoreceptors being the primary consumers of glucose, which is convincing. However, the study has incomplete evidence to support the claims that photoreceptors can use lactate as a fuel source, that lactate exported from photoreceptors is utilized by the RPE, and that lactate contributes to the TCA cycle in the RPE. These claims need substantial revision to include potential alternative explanations or perform key experiments.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors sought to build upon their prior work, which suggested the presence of an outer retinal metabolic microenvironment using ex vivo and in vitro systems, by using in vivo methods and a multitude of genetic models. The authors convincingly demonstrate that the retina prefers circulating glucose to some other circulating fuel sources and that photoreceptors are the main consumers of glucose in the retina. However, the claims regarding the ability of photoreceptors to utilize lactate as a fuel source, that lactate exported specifically from photoreceptors is taken up by RPE and further utilized to support the TCA cycle in the RPE are incomplete or inadequate and would benefit from further experimentation to convince the reader of such biological processes. Considering alternative explanations and performing key experiments to confirm or refute these claims would substantially improve the impact of this study.

Strengths:

The major strengths of this study are its in vivo infusion methodologies and utilization of mouse models that are devoid of photoreceptors or are photoreceptor-specific conditional knockouts to provide convincing evidence that the retina utilizes circulating glucose to a significant degree and photoreceptors are the main consumers of glucose in the retina. These in vivo studies are complemented by ex vivo experiments in retinal explants.

Weaknesses:

While the in vivo infusion methodologies are a clear strength, not utilizing these techniques or other in vivo methodologies with the genetic models that lack photoreceptors or photoreceptor-specific proteins and not providing in vivo metabolomics data from these infusions in the RPE is a major weakness. Also, some circulating fuel sources may not get into the retina in appreciable amounts, impacting some of the authors' claims. Another major weakness is that for many of the claims noted by the authors, alternative explanations have not been considered nor have the proper experiments been conducted to fully support or refute these claims. For example, the authors claim it is photoreceptors that utilize lactate upon knockout of Glut1. However, other cells in the retina, such as Muller glia, may be the ones actually catabolizing lactate based on prior studies and enzyme expression patterns and their kinetics to support photoreceptors via the production of other metabolites from lactate. This alternative has not been considered nor have experiments been conducted to refute this possibility. Additionally, the authors claim lactate exported from photoreceptors is being taken up by RPE. The models used to support this claim lack photoreceptors, or their ability to take up glucose. None of the models specifically address lactate export from photoreceptors. Finally, the authors claim lactate exported from photoreceptors can be oxidized to TCA cycle intermediates in the RPE in vivo. No experiments specifically addressed the downstream path of lactate exported by photoreceptors in RPE TCA cycle metabolism in vivo, so this conclusion is also not well supported. Hence, the claims need to be significantly amended with an acknowledgment of potential alternatives or with some key experiments performed.

Reviewer #2 (Public review):

Hass et al. use in vivo and ex vivo mouse models to explore and validate the use of glucose and lactate by the outer retina. While the authors' conclusions are not totally novel, their work uses powerful in vivo models to validate, strengthen, and support their conclusions. This data is an important step forward in the field's understanding of retinal metabolism.

They performed in vivo metabolite tracing with 5 different fuel sources and found that glucose was the primary fuel for TCA in the retina. While performing these experiments they measured the circulating levels of the tracer metabolites to ensure steady-state labeling which aids in the interpretation of the results. Showing the levels of the labeled tracer in the retina would be a nice addition to establishing if the tracer is getting into the target tissue.

To support their conclusions that the photoreceptors are the primary consumers of glucose in the retina, the authors used multiple mouse models either with photoreceptor degeneration or a retina lacking the primary glucose transporter. While the photoreceptor degeneration mouse model has some caveats that make interpreting the data challenging, the glucose transporter KO models are a powerful tool to show the changes in metabolite levels between the retina and RPE in a retina. These retinas are not degenerated and have more subtle metabolic rearrangements. Therefore decreases in glucose consumption and lactate export can confidently be attributed to the changes in the photoreceptor metabolism. This model also allowed the authors to show that when glucose uptake is limited the photoreceptors can use lactate.

The authors show in vivo data to support that the RPE uses lactate from the photoreceptors as a fuel source. They do very short-term tracing in vivo to show that the RPE has reduced lactate levels and TCA labeling in a mouse model lacking photoreceptors. There is no deficiency when the RPE is measured ex vivo. These data clearly show that the adjacent photoreceptor activity is impacting RPE metabolism.

The manuscript is well-written, and thorough and does a very good job detailing and explaining methods and concepts that are not straightforward. The authors address (and do not bury) confusing data that does not necessarily support their conclusions (for example glycolytic intermediates in Figure 3C being elevated. The authors even perform additional experiments to clarify artifacts they observed in the tracing of the degeneration model due to short-term ischemia.

Reviewer #3 (Public review):

This work addresses the metabolic interplay between photoreceptors and the adjacent supporting layer of the vertebrate retina, the retinal pigment epithelium (RPE). Prior work from the Hurley lab and others provided evidence, mainly in acutely dissected mouse retina and in cell culture, for the idea that although glucose enters the retina via the RPE, the photoreceptors use most of this glucose via glycolysis, producing lactate that is used by other cells such as Müller cells and RPE cells. In the current study, they build on this by showing that these same principles hold true in vivo, using organism-level stable isotope tracing, as well as in intact retina preparations. They also use several mutant mice that lack photoreceptors, or that lack glucose transporters in either rods or the whole retina, to examine the contribution of photoreceptors to retinal glucose uptake. While many of the concepts were introduced in earlier work, it is an important expansion of this work to show these same mechanisms function in vivo. The authors also use other labeled fuels, lactate, and palmitate, to characterize their use in the presence or absence of glucose transport.

The paper presents a nice combination of in vivo experiments (with a steady infusion of labeled metabolites into the circulation of a living mouse) with ex vivo experiments that allow the monitoring of lactate production and temporal control of labeling.

Overall, the work provides convincing evidence that in the eye of a living mouse, photoreceptors are the main consumers of glucose in the retina, and the main producers of lactate. It seems less clear that the incorporation of labeled glucose into TCA metabolites in the RPE is dependent on the photoreceptor processing of glucose to lactate. Figure 5D is cited as the evidence that "much less m+3 lactate reaches the RPE-choroid in AIPL-/- mice than in controls," and indeed there is much less labeled lactate; but the downstream labeling of citrate is not substantially affected. It is also hard to discern whether these in vivo experiments provide evidence that photoreceptor-derived lactate suppresses glucose oxidation in RPE cells (as shown in vitro in Kanow et al., 2017).

Author response:

We thank the reviewers for their thoughtful reading and review of our manuscript. These reviews make clear that, for this work to be complete, we must make progress on the following fronts:

(1) Expand the discussion to better incorporate alternate explanations of our data

(2) Improve data visualization and experimental support or an experimental refutation for the following concepts

a. Photoreceptor-derived lactate exported specifically from photoreceptors is utilized in the RPE TCA cycle

b. Photoreceptors can utilize lactate as a fuel source when starved of glucose

To address these concerns, we will focus our efforts on infusing ¹³C₆-glucose into rodΔglut1 mice. Lactate is not made without glucose, so this experiment should indicate whether glucose utilization in photoreceptors provides lactate to the RPE, and whether that lactate is used in the TCA cycle.

The reviewers also noted that changes in ¹³C labeling of RPE TCA cycle intermediates downstream of lactate is not obvious (between C57BL6J mice and AIPL1^-/-). We think that at least in part, this is a consequence of the way we presented the data. We will improve how we display our data so that the differences of incorporation of ¹³C in TCA cycle intermediates in control and AIPL1^-/- RPE is clearer.

eLife Assessment

This potentially valuable study presents claims of evidence for coordinated membrane potential oscillations in E. coli biofilms that can be linked to a putative K+ channel and that may serve to enhance photo-protection. The finding of waves of membrane potential would be of interest to a wide audience from molecular biology to microbiology and physical biology. Unfortunately, a major issue is that it is unclear whether the dye used can act as a Nernstian membrane potential dye in E. coli. The arguments of the authors, who largely ignore previously published contradictory evidence, are not adequate in that they do not engage with the fact that the dye behaves in their hands differently than in the hands of others. In addition, the lack of proper validation of the experimental method including key control experiments leaves the evidence incomplete.

Reviewer #1 (Public Review):

(1) Significance of the findings:

Cell-to-cell communication is essential for higher functions in bacterial biofilms. Electrical signals have proven effective in transmitting signals across biofilms. These signals are then used to coordinate cellular metabolisms or to increase antibiotic tolerance. Here, the authors have reported for the first time coordinated oscillation of membrane potential in E. coli biofilms that may have a functional role in photoprotection.

(2) Strengths of the manuscript:

- The authors report original data.<br /> - For the first time, they showed that coordinated oscillations in membrane potential occur in E. Coli biofilms.<br /> - The authors revealed a complex two-phase dynamic involving distinct molecular response mechanisms.<br /> - The authors developed two rigorous models inspired by 1) Hodgkin-Huxley model for the temporal dynamics of membrane potential and 2) Fire-Diffuse-Fire model for the propagation of the electric signal.<br /> - Since its discovery by comparative genomics, the Kch ion channel has not been associated with any specific phenotype in E. coli. Here, the authors proposed a functional role for the putative gated-voltage-gated K+ ion channel (Kch channel) : enhancing survival under photo-toxic conditions.

(3) Weakness:

- Contrarily to what is stated in the abstract, the group of B. Maier has already reported collective electrical oscillations in the Gram-negative bacterium Neisseria gonorrhoeae (Hennes et al., PLoS Biol, 2023).<br /> - The data presented in the manuscript are not sufficient to conclude on the photo-protective role of the Kch channel. The authors should perform the appropriate control experiments related to Fig4D,E, i.e. reproduce these experiments without ThT to rule out possible photo-conversion effects on ThT that would modify its toxicity. In addition, it looks like the data reported on Fig 4E are extracted from Fig 4D. If this is indeed the case, it would be more conclusive to report the percentage of PI-positive cells in the population for each condition. This percentage should be calculated independently for each replicate. The authors should then report the average value and standard deviation of the percentage of dead cells for each condition.<br /> - Although Fig 4A clearly shows that light stimulation has an influence on the dynamics of ThT signal in the biofilm, it is important to rule out possible contributions of other environmental variations that occur when the flow is stopped at the onset of light stimulation. I understand that for technical reasons, the flow of fresh medium must be stopped for the sake of imaging. Therefore, I suggest to perform control experiments consisting in stopping the flow at different time intervals before image acquisition (30min or 1h before). If there is no significant contribution from environmental variations due to medium perfusion arrest, the dynamics of ThT signal must be unchanged regardless of the delay between flow stop and the start of light stimulation.<br /> - To precise the role of K+ in the habituation response, I suggest using the ionophore valinomycin at sub-inhibitory concentrations (5 or 10µM). It should abolish the habituation response. In addition, the Kch complementation experiment exhibits a sharp drop after the first peak but on a single point. It would be more convincing to increase the temporal resolution (1min->10s) to show that there are indeed a first and a second peak. Finally, the high concentration (100µM) of CCCP used in this study completely inhibits cell activity. Therefore, it is not surprising that no ThT dynamics was observed upon light stimulation at such concentration of CCCP.<br /> - Since TMRM signal exhibits a linear increase after the first response peak (Supp Fig1D), I recommend to mitigate the statement at line 78.<br /> - Electrical signal propagation is an important aspect of the manuscript. However, a detailed quantitative analysis of the spatial dynamics within the biofilm is lacking. At minima, I recommend to plot the spatio-temporal diagram of ThT intensity profile averaged along the azimuthal direction in the biofilm. In addition, it is unclear if the electrical signal propagates within the biofilm during the second peak regime, which is mediated by the Kch channel: I have plotted the spatio-temporal diagram for Video S3 and no electrical propagation is evident at the second peak. In addition, the authors should provide technical details of how R^2(t) is measured in the first regime (Fig 7E).<br /> - In the series of images presented in supplementary Figure 4A, no wavefront is apparent. Although the microscopy technics used in this figure differs from other images (like in Fig2), the wavefront should be still present. In addition, there is no second peak in confocal images as well (Supp Fig4B) .<br /> - Many important technical details are missing (e.g. biofilm size, R^2, curvature and 445nm irradiance measurements). The description of how these quantitates are measured should be detailed in the Material & Methods section.<br /> - Fig 5C: The curve in Fig 5D seems to correspond to the biofilm case. Since the model is made for single cells, the curve obtained by the model should be compared with the average curve presented in Fig 1B (i.e. single cell experiments).<br /> - For clarity, I suggest to indicate on the panels if the experiments concern single cell or biofilm experiments. Finally, please provide bright-field images associated to ThT images to locate bacteria.<br /> - In Fig 7B, the plateau is higher in the simulations than in the biofilm experiments. The authors should add a comment in the paper to explain this discrepancy.

Reviewer #2 (Public Review):

The authors use ThT dye as a Nernstian potential dye in E. coli. Quantitative measurements of membrane potential using any cationic indicator dye are based on the equilibration of the dye across the membrane according to Boltzmann's law.

Ideally, the dye should have high membrane permeability to ensure rapid equilibration. Others have demonstrated that E.coli cells in the presence of ThT do not load unless there is blue light present, that the loading profile does not look like it is expected for a cationic Nernstian dye. They also show that the loading profile of the dye is different for E.coli cells deleted for the TolC pump. I, therefore, objected to interpreting the signal from the ThT as a Vm signal when used in E.coli. Nothing the authors have said has suggested that I should be changing this assessment.

Specifically, the authors responded to my concerns as follows:

(1) 'We are aware of this study, but believe it to be scientifically flawed. We do not cite the article because we do not think it is a particularly useful contribution to the literature.' This seems to go against ethical practices when it comes to scientific literature citations. If the authors identified work that handles the same topic they do, which they believe is scientifically flawed, the discussion to reflect that should be included.

(2)'The Pilizota group invokes some elaborate artefacts to explain the lack of agreement with a simple Nernstian battery model. The model is incorrect not the fluorophore.'<br /> It seems the authors object to the basic principle behind the usage of Nernstian dyes. If the authors wish to use ThT according to some other model, and not as a Nernstian indicator, they need to explain and develop that model. Instead, they state 'ThT is a Nernstian voltage indicator' in their manuscript and expect the dye to behave like a passive voltage indicator throughout it.

(3)'We think the proton effect is a million times weaker than that due to potassium i.e. 0.2 M K+<br /> versus 10-7 M H+. We can comfortably neglect the influx of H+ in our experiments.'<br /> I agree with this statement by the authors. At near-neutral extracellular pH, E.coli keeps near-neutral intracellular pH, and the contribution from the chemical concentration gradient to the electrochemical potential of protons is negligible. The main contribution is from the membrane potential. However, this has nothing to do with the criticism to which this is the response of the authors. The criticism is that ThT has been observed not to permeate the cell without blue light. The blue light has been observed to influence the electrochemical potential of protons (and given that at near-neutral intracellular and extracellular pH this is mostly the membrane potential, as authors note themselves, we are talking about Vm effectively). Thus, two things are happening when one is loading the ThT, not just expected equilibration but also lowering of membrane potential. The electrochemical potential of protons is coupled via the membrane potential to all the other electrochemical potentials of ions, including the mentioned K+.

(4) 'The vast majority of cells continue to be viable. We do not think membrane damage is dominating.' In response to the question on how the authors demonstrated TMRM loading and in which conditions (and while reminding them that TMRM loading profile in E.coli has been demonstrated in Potassium Phosphate buffer). The request was to demonstrate TMRM loading profile in their condition as well as to show that it does not depend on light. Cells could still be viable, as membrane permeabilisation with light is gradual, but the loading of ThT dye is no longer based on simple electrochemical potential (of the dye) equilibration.

(5) On the comment on the action of CCCP with references included, authors include a comment that consists of phrases like 'our understanding of the literature' with no citations of such literature. Difficult to comment further without references.

(6) 'Shielding would provide the reverse effect, since hyperpolarization begins in the dense centres of the biofilms. For the initial 2 hours the cells receive negligible blue light. Neither of the referee's comments thus seem tenable.'<br /> The authors have misunderstood my comment. I am not advocating shielding (I agree that this is not it) but stating that this is not the only other explanation for what they see (apart from electrical signaling). The other I proposed is that the membrane has changed in composition and/or the effective light power the cells can tolerate. The authors comment only on the light power (not convincingly though, giving the number for that power would be more appropriate), not on the possible changes in the membrane permeability.

(7) 'The work that TolC provides a possible passive pathway for ThT to leave cells seems slightly niche. It just demonstrates another mechanism for the cells to equilibrate the concentrations of ThT in a Nernstian manner i.e. driven by the membrane voltage.' I am not sure what the authors mean by another mechanism. The mechanism of action of a Nernstian dye is passive equilibration according to the electrochemical potential (i.e. until the electrochemical potential of the dye is 0).

(8) 'In the 70 years since Hodgkin and Huxley first presented their model, a huge number of similar models have been proposed to describe cellular electrophysiology. We are not being hyperbolic when we state that the HH models for excitable cells are like the Schrödinger<br /> equation for molecules. We carefully adapted our HH model to reflect the currently understood electrophysiology of E. coli.'

I gave a very concrete comment on the fact that in the HH model conductivity and leakage are as they are because this was explicitly measured. The authors state that they have carefully adopted their model based on what is currently understood for E.coli electrophysiology. It is not clear how. HH uses gKn^4 based on Figure2 here https://www.ncbi.nlm.nih.gov/pmc/articles/PMC1392413/pdf/jphysiol01442-0106.pdf, i.e. measured rise and fall of potassium conductance on msec time scales. I looked at the citation the authors have given and found a resistance of an entire biofilm of a given strain at 3 applied voltages. So why n^4 based on that? Why does unknown current have gqz^4 form? Sodium conductance in HH is described by m^3hgNa (again based on detailed conductance measurements), so why unknown current in E.coli by gQz^4? Why leakage is in the form that it is, based on what measurement?

Throughout their responses, the authors seem to think that collapsing the electrochemical gradient of protons is all about protons, and this is not the case. At near neutral inside and outside pH, the electrochemical potential of protons is simply membrane voltage. And membrane voltage acts on all ions in the cell.

Authors have started their response to concrete comments on the usage of ThT dye with comments on papers from my group that are not all directly relevant to this publication. I understand that their intention is to discredit a reviewer but given that my role here is to review this manuscript, I will only address their comments to the publications/part of publications that are relevant to this manuscript and mention what is not relevant.

Publications in the order these were commented on.

(1) In a comment on the paper that describes the usage of ThT dye as a Nernstian dye authors seem to talk about a model of an entire active cell.<br /> 'Huge oscillations occur in the membrane potentials of E. coli that cannot be described by the SNB model.' The two have nothing to do with each other. Nernstian dye equilibrates according to its electrochemical potential. Once that happens it can measure the potential (under the assumption that not too much dye has entered and thus lowered too much the membrane potential under measurement). The time scale of that is important, and the dye can only measure processes that are slower than that equilibration. If one wants to use a dye that acts under a different model, first that needs to be developed, and then coupled to any other active cell model.

(2) The part of this paper that is relevant is simply the usage of TMRM dye. It is used as Nernstian dye, so all the above said applies. The rest is a study of flagellar motor.

(3) The authors seem to not understand that the electrochemical potential of protons is coupled to the electrochemical potentials of all other ions, via the membrane potential. In the manuscript authors talk about, PMF~Vm, as DeltapH~0. Other than that this publication is not relevant to their current manuscript.

(4) The manuscript in fact states precisely that PMF cannot be generated by protons only and some other ions need to be moved out for the purpose. In near neutral environment it stated that these need to be cations (K+ e.g.). The model used in this manuscript is a pump-leak model. Neither is relevant for the usage of ThT dye.

Further comments include, along the lines of:

'The editors stress the main issue raised was a single referee questioning the use of ThT as an indicator of membrane potential. We are well aware of the articles by the Pilizota group and we believe them to be scientifically flawed. The authors assume there are no voltage-gated ion channels in E. coli and then attempt to explain motility data based on a simple Nernstian battery model (they assume E. coli are unexcitable<br /> matter). This in turn leads them to conclude the membrane dye ThT is faulty, when in fact it is a problem with their simple battery model.'

The only assumption made when using a cationic Nernstian dye is that it equilibrates passively across the membrane according to its electrochemical potential. As it does that, it does lower the membrane potential, which is why as little as possible is added so that this is negligible. The equilibration should be as fast as possible, but at the very least it should be known, as no change in membrane potential can be measured that is faster than that.

This behaviour should be orthogonal to what the cell is doing, it is a probe after all. If the cell is excitable, a Nernstian dye can be used, as long as it's still passively equilibrating and doing so faster than any changes in membrane potential due to excitations of the cells. There are absolutely no assumptions made on the active system that is about to be measured by this expected behaviour of a Nernstian dye. And there shouldn't be, it is a probe. If one wants to use a dye that is not purely Nernstian that behaviour needs to be described and a model proposed. As far as I can find, authors do no such thing.

There is a comment on the use of a flagellar motor as a readout of PMF, stating that the motor can be stopped by YcgR citing the work from 2023. Indeed, there is a range of references such as https://doi.org/10.1016/j.molcel.2010.03.001 that demonstrate this (from around 2000-2010 as far as I am aware). The timescale of such slowdown is hours (see here Figure 5 https://www.cell.com/cell/pdf/S0092-8674(10)00019-X.pdf). Needless to say, the flagellar motor when used as a probe, needs to stay that in the conditions used. Thus one should always be on the lookout at any other such proteins that could slow it down and we are not aware of yet or make the speed no longer proportional to the PMF. In the papers my group uses the motor the changes are fast, often reversible, and in the observation window of 30min. They are also the same with DeltaYcgR strain, which we have not included as it seemed given the time scales it's obvious, but certainly can in the future (as well as stay vigilant on any conditions that would render the motor a no longer suitable probe for PMF).

Reviewer #3 (Public Review):

This manuscript by Akabuogu et al. investigates membrane potential dynamics in E. coli. Membrane potential fluctuations have been observed in bacteria by several research groups in recent years, including in the context of bacterial biofilms where they have been proposed to play a role in cellular communication. Here, these authors investigate membrane potential in E. coli, in both single cells and biofilms. I have reviewed the revised manuscript provided by the authors, as well as their responses to the initial reviews; my opinion about the manuscript is largely unchanged. I have focused my public review on those issues that I believe to be most pressing, with additional comments included in the review to authors. Although these authors are working in an exciting research area, the evidence they provide for their claims is inadequate, and several key control experiments are still missing. In some cases, the authors allude to potentially relevant data in their responses to the initial reviews, but unfortunately these data are not shown. Furthermore, I cannot identify any traveling wavefronts in the data included in this manuscript. In addition to the challenges associated with the use of Thioflavin-T (ThT) raised by the second reviewer, these caveats make the work presented in this manuscript difficult to interpret.

First, some of the key experiments presented in the paper lack required controls:

(1) This paper asserts that the observed ThT fluorescence dynamics are induced by blue light. This is a fundamental claim in the paper, since the authors go on to argue that these dynamics are part of a blue light response. This claim must be supported by the appropriate negative control experiment measuring ThT fluorescence dynamics in the absence of blue light- if this idea is correct, these dynamics should not be observed in the absence of blue light exposure. If this experiment cannot be performed with ThT since blue light is used for its excitation, TMRM can be used instead.

In response to this, the authors wrote that "the fluorescent baseline is too weak to measure cleanly in this experiment." If they observe no ThT signal above noise in their time lapse data in the absence of blue light, this should be reported in the manuscript- this would be a satisfactory negative control. They then wrote that "It appears the collective response of all the bacteria hyperpolarization at the same time appears to dominate the signal." I am not sure what they mean by this- perhaps that ThT fluorescence changes strongly only in response to blue light? This is a fundamental control for this experiment that ought to be presented to the reader.

(2) The authors claim that a ∆kch mutant is more susceptible to blue light stress, as evidenced by PI staining. The premise that the cells are mounting a protective response to blue light via these channels rests on this claim. However, they do not perform the negative control experiment, conducting PI staining for WT the ∆kch mutant in the absence of blue light. In the absence of this control it is not possible to rule out effects of the ∆kch mutation on overall viability and/or PI uptake. The authors do include a growth curve for comparison, but planktonic growth is a very different context than surface-attached biofilm growth. Additionally, the ∆kch mutation may have impacts on PI permeability specifically that are not addressed by a growth curve. The negative control experiment is of key importance here.

Second, the ideas presented in this manuscript rely entirely on analysis of ThT fluorescence data, specifically a time course of cellular fluorescence following blue light treatment. However, alternate explanations for and potential confounders of the observed dynamics are not sufficiently addressed:

(1) Bacterial cells are autofluorescent, and this fluorescence can change significantly in response to stress (e.g. blue light exposure). To characterize and/or rule out autofluorescence contributions to the measurement, the authors should present time lapse fluorescence traces of unstained cells for comparison, acquired under the same imaging conditions in both wild type and ∆kch mutant cells. In their response to reviewers the authors suggested that they have conducted this experiment and found that the autofluorescence contribution is negligible, which is good, but these data should be included in the manuscript along with a description of how these controls were conducted.

(2) Similarly, in my initial review I raised a concern about the possible contributions of photobleaching to the observed fluorescence dynamics. This is particularly relevant for the interpretation of the experiment in which catalase appears to attenuate the decay of the ThT signal; this attenuation could alternatively be due to catalase decreasing ThT photobleaching. In their response, the authors indicated that photobleaching is negligible, which would be good, but they do not share any evidence to support this claim. Photobleaching can be assessed in this experiment by varying the light dosage (illumination power, frequency, and/or duration) and confirming that the observed fluorescence dynamics are unaffected.

Third, the paper claims in two instances that there are propagating waves of ThT fluorescence that move through biofilms, but I do not observe these waves in any case:

(1) The first wavefront claim relates to small cell clusters, in Fig. 2A and Video S2 and S3 (with Fig. 2A and Video S2 showing the same biofilm.) I simply do not see any evidence of propagation in either case- rather, all cells get brighter and dimmer in tandem. I downloaded and analyzed Video S3 in several ways (plotting intensity profiles for different regions at different distances from the cluster center, drawing a kymograph across the cluster, etc.) and in no case did I see any evidence of a propagating wavefront. (I attempted this same analysis on the biofilm shown in Fig. 2A and Video S2 with similar results, but the images shown in the figure panels and especially the video are still both so saturated that the quantification is difficult to interpret.) If there is evidence for wavefronts, it should be demonstrated explicitly by analysis of several clusters. For example, a figure of time-to-peak vs. position in the cluster demonstrating a propagating wave would satisfy this. Currently, I do not see any wavefronts in this data.

(2) The other wavefront claim relates to biofilms, and the relevant data is presented in Fig. S4 (and I believe also in what is now Video S8, but no supplemental video legends are provided, and this video is not cited in text.) As before, I cannot discern any wavefronts in the image and video provided; Reviewer 1 was also not able to detect wave propagation in this video by kymograph. Some mean squared displacements are shown in Fig. 7. As before, the methods for how these were obtained are not clearly documented either in this manuscript or in the BioRXiv preprint linked in the initial response to reviewers, and since wavefronts are not evident in the video it is hard to understand what is being measured here- radial distance from where? (The methods section mentions radial distance from the substrate, this should mean Z position above the imaging surface, and no wavefronts are evident in Z in the figure panels or movie.) Thus, clear demonstration of these wavefronts is still missing here as well.

Fourth, I have some specific questions about the study of blue light stress and the use of PI as a cell viability indicator:

(1) The logic of this paper includes the premise that blue light exposure is a stressor under the experimental conditions employed in the paper. Although it is of course generally true that blue light can be damaging to bacteria, this is dependent on light power and dosage. The control I recommended above, staining cells with PI in the presence and absence of blue light, will also allow the authors to confirm that this blue light treatment is indeed a stressor- the PI staining would be expected to increase in the presence of blue light if this is so.

(2) The presence of ThT may complicate the study of the blue light stress response, since ThT enhances the photodynamic effects of blue light in E. coli (Bondia et al. 2021 Chemical Communications). The authors could investigate ThT toxicity under these conditions by staining cells with PI after exposing them to blue light with or without ThT staining.

(3) In my initial review, I wrote the following: "In Figures 4D - E, the interpretation of this experiment can be confounded by the fact that PI uptake can sometimes be seen in bacterial cells with high membrane potential (Kirchhoff & Cypionka 2017 J Microbial Methods); the interpretation is that high membrane potential can lead to increased PI permeability. Because the membrane potential is largely higher throughout blue light treatment in the ∆kch mutant (Fig. 3[BC]), this complicates the interpretation of this experiment." In their response, the authors suggested that these results are not relevant in this case because "In our experiment methodology, cell death was not forced on the cells by introducing an extra burden or via anoxia." However, the logic of the paper is that the cells are in fact dying due to an imposed external stressor, which presumably also confers an increased burden as the cells try to deal with the stress. Instead, the authors should simply use a parallel method to confirm the results of PI staining. For example, the experiment could be repeated with other stains, or the viability of blue light-treated cells could be addressed more directly by outgrowth or colony-forming unit assays.

The CFU assay suggested above has the additional advantage that it can also be performed on planktonic cells in liquid culture that are exposed to blue light. If, as the paper suggests, a protective response to blue light is being coordinated at the biofilm level by these membrane potential fluctuations, the WT strain might be expected to lose its survival advantage vs. the ∆kch mutant in the absence of a biofilm.

Fifth, in several cases the data are presented in a way that are difficult to interpret, or the paper makes claims that are different to observe in the data:

(1) The authors suggest that the ThT and TMRM traces presented in Fig. S1D have similar shapes, but this is not obvious to me- the TMRM curve has very little decrease after the initial peak and only a modest, gradual rise thereafter. The authors suggest that this is due to increased TMRM photobleaching, but I would expect that photobleaching should exacerbate the signal decrease after the initial peak. Since this figure is used to support the use of ThT as a membrane potential indicator, and since this is the only alternative measurement of membrane potential presented in text, the authors should discuss this discrepancy in more detail.

(2) The comparison of single cells to microcolonies presented in figures 1B and D still needs revision:

First, both reviewer 1 and I commented in our initial reviews that the ThT traces, here and elsewhere, should not be normalized- this will help with the interpretation of some of the claims throughout the manuscript.

Second, the way these figures are shown with all traces overlaid at full opacity makes it very difficult to see what is being compared. Since the point of the comparison is the time to first peak (and the standard deviation thereof), histograms of the distributions of time to first peak in both cases should be plotted as a separate figure panel.<br /> Third, statistical significance tests ought to be used to evaluate the statistical strength of the comparisons between these curves. The authors compare both means and standard deviations of the time to first peak, and there are appropriate statistical tests for both types of comparisons.

(3) The authors claim that the curve shown in Fig. S4B is similar to the simulation result shown in Fig. 7B. I remain unconvinced that this is so, particularly with respect to the kinetics of the second peak- at least it seems to me that the differences should be acknowledged and discussed. In any case, the best thing to do would be to move Fig. S4B to the main text alongside Fig. 7B so that the readers can make the comparison more easily.

(4) As I wrote in my first review, in the discussion of voltage-gated calcium channels, the authors refer to "spiking events", but these are not obvious in Figure S3E. Although the fluorescence intensity changes over time, these fluctuations cannot be distinguished from measurement noise. A no-light control could help clarify this.

(5) In the lower irradiance conditions in Fig. 4A, the ThT dynamics are slower overall, and it looks like the ThT intensity is beginning to rise at the end of the measurement. The authors write that no second peak is observed below an irradiance threshold of 15.99 µW/mm2. However, could a more prominent second peak be observed in these cases if the measurement time was extended? Additionally, the end of these curves looks similar to the curve in Fig. S4B, in which the authors write that the slow rise is evidence of the presence of a second peak, in contrast to their interpretation here.

Additional considerations:

(1) The analysis and interpretation of the first peak, and particularly of the time-to-fire data is challenging throughout the manuscript the time resolution of the data set is quite limited. It seems that a large proportion of cells have already fired after a single acquisition frame. It would be ideal to increase the time resolution on this measurement to improve precision. This could be done by imaging more quickly, but that would perhaps necessitate more blue light exposure; an alternative is to do this experiment under lower blue light irradiance where the first spike time is increased (Figure 4A).

(2) The authors suggest in the manuscript that "E. coli biofilms use electrical signalling to coordinate long-range responses to light stress." In addition to the technical caveats discussed above, I am missing a discussion about what these responses might be. What constitutes a long-range response to light stress, and are there known examples of such responses in bacteria?

(3) The presence of long-range blue light responses can also be interrogated experimentally, for example, by repeating the Live/Dead experiment in planktonic culture or the single-cell condition. If the protection from blue light specifically emerges due to coordinated activity of the biofilm, the ∆kch mutant would not be expected to show a change in Live/Dead staining in non-biofilm conditions. The CFU experiment I mentioned above could also implicate coordinated long-range responses specifically, if biofilms and liquid culture experiments can be compared (although I know that recovering cells from biofilms is challenging.)

4. At the end of the results section, the authors suggest a critical biofilm size of only 4 μm for wavefront propagation (not much larger than a single cell!) The authors show responses for various biofilm sizes in Fig. 2C, but these are all substantially larger (and this figure also does not contain wavefront information.) Are there data for cell clusters above and below this size that could support this claim more directly?

(5) In Fig. 4C, the overall trajectories of extracellular potassium are indeed similar, but the kinetics of the second peak of potassium are different than those observed by ThT (it rises minutes earlier)- is this consistent with the idea that Kch is responsible for that peak? Additionally, the potassium dynamics also include the first ThT peak- is this surprising given that the Kch channel has no effect on this peak according to the model?

Detailed comments:

Why are Fig. 2A and Video S2 called a microcluster, whereas Video S3, which is smaller, is called a biofilm?

"We observed a spontaneous rapid rise in spikes within cells in the center of the biofilm" (Line 140): What does "spontaneous" mean here?

"This demonstrates that the ion-channel mediated membrane potential dynamics is a light stress relief process.", "E. coli cells employ ion-channel mediated dynamics to manage ROS-induced stress linked to light irradiation." (Line 268 and the second sentence of the Fig. 4F legend): This claim is not well-supported. There are several possible interpretations of the catalase experiment (which should be discussed); this experiment perhaps suggests that ROS impacts membrane potential but does not indicate that these membrane potential fluctuations help the cells respond to blue light stress. The loss of viability in the ∆kch mutant might indicate a link between these membrane potential experiments and viability, but it is hard to interpret without the no light controls I mention above.

"The model also predicts... the external light stress" (Lines 338-341): Please clarify this section. Where does this prediction arise from in the modeling work? Second, I am not sure what is meant by "modulates the light stress" or "keeps the cell dynamics robust to the intensity of external light stress" (especially since the dynamics clearly vary with irradiance, as seen in Figure 4A).

"We hypothesized that E. coli not only modulates the light-induced stress but also handles the increase of the ROS by adjusting the profile of the membrane potential dynamics" (Line 347): I am not sure what "handles the ROS by adjusting the profile of the membrane potential dynamics" means. What is meant by "handling" ROS? Is the hypothesis that membrane potential dynamics themselves are protective against ROS, or that they induce a ROS-protective response downstream, or something else? Later the authors write that changes in the response to ROS in the model agree with the hypothesis, but just showing that ROS impacts the membrane potential does not seem to demonstrate that this has a protective effect against ROS.

"Mechanosensitive ion channels (MS) are vital for the first hyperpolarization event in E. coli." (Line 391): This is misleading- mechanosensitive ion channels totally ablate membrane potential dynamics, they don't have a specific effect on the first hyperpolarization event. The claim that mechanonsensitive ion channels are specifically involved in the first event also appears in the abstract.

Also, the apparent membrane potential is much lower even at the start of the experiment in these mutants (Fig. 6C-D)- is this expected? This seems to imply that these ion channels also have a blue light-independent effect.

Throughout the paper, there are claims that the initial ThT spike is involved in "registering the presence of the light stress" and similar. What is the evidence for this claim?

"We have presented much better quantitative agreement of our model with the propagating wavefronts in E. coli biofilms..." (Line 619): It is not evident to me that the agreement between model and prediction is "much better" in this work than in the cited work (reference 57, Hennes et al. 2023). The model in Figure 4 of ref. 57 seems to capture the key features of their data.

In methods, "Only cells that are hyperpolarized were counted in the experiment as live" (Line 745): what percentage of cells did not hyperpolarize in these experiments?

Some indication of standard deviation (error bars or shading) should be added to all figures where mean traces are plotted.

Video S8 is very confusing- why does the video play first forwards and then backwards? It is easy to misinterpret this as a rise in the intensity at the end of the experiment.

Author response:

The issue of a control without blue light illumination was raised. Clearly without the light we will not obtain any signal in the fluorescence microscopy experiments, which would not be very informative. Instead, we changed the level of blue light illumination in the fluorescence microscopy experiments (figure 4A) and the response of the bacteria scales with dosage. It is very hard to find an alternative explanation, beyond that the blue light is stressing the bacteria and modulating their membrane potentials.

One of the referees refuses to see wavefronts in our microscopy data. We struggle to understand whether it is an issue with definitions (Waigh has published a tutorial on the subject in Chapter 5 of his book ‘The physics of bacteria: from cells to biofilms’, T.A.Waigh, CUP, 2024 – figure 5.1 shows a sketch) or something subtler on diffusion in excitable systems. We stand by our claim that we observe wavefronts, similar to those observed by Prindle et al¹ and Blee et al² for B. subtilis biofilms.

The referee is questioning our use of ThT to probe the membrane potential. We believe the Pilizota and Strahl groups are treating the E. coli as unexcitable cells, leading to their problems. Instead, we believe E. coli cells are excitable (containing the voltage-gated ion channel Kch) and we now clearly state this in the manuscript. Furthermore, we include a section here discussing some of the issues with ThT.

Use of ThT as a voltage sensor in cells

ThT is now used reasonably widely in the microbiology community as a voltage sensor in both bacterial [Prindle et al]1 and fungal cells [Pena et al]12. ThT is a small cationic fluorophore that loads into the cells in proportion to their membrane potential, thus allowing the membrane potential to be measured from fluorescence microscopy measurements.

Previously ThT was widely used to quantify the growth of amyloids in molecular biology experiments (standardized protocols exist and dedicated software has been created)13 and there is a long history of its use14. ThT fluorescence is bright, stable and slow to photobleach.

Author response figure 1 shows a schematic diagram of the ThT loading in E. coli in our experiments in response to illumination with blue light. Similar results were previously presented by Mancini et al15, but regimes 2 and 3 were mistakenly labelled as artefacts.

Author response figure 1. Schematic diagram of ThT loading during an experiment with E. coli cells under blue light illumination i.e. ThT fluorescence as a function of time. Three empirical regimes for the fluorescence are shown (1, 2 and 3).

The classic study of Prindle et al on bacterial biofilm electrophysiology established the use of ThT in B. subtilis biofilms by showing similar results occurred with DiSc3 which is widely used as a Nernstian voltage sensor in cellular biology1 e.g. with mitochondrial membrane potentials in eukaryotic organisms where there is a large literature. We repeated such a comparative calibration of ThT with DiSc3 in a previous publication with both B. subtilis and P. aeruginosa cells2. ThT thus functioned well in our previous publications with Gram positive and Gram negative cells.

However, to our knowledge, there are now two groups questioning the use of ThT and DiSc3 as voltage sensors with E. coli cells15-16. The first by the Pilizota group claims ThT only works as a voltage sensor in regime 1 of Author response figure 1 using a method based on the rate of rotation of flagellar motors. Another slightly contradictory study by the Strahl group claims DiSc316 only acts as a voltage sensor with the addition of an ionophore for potassium which allows free movement of potassium through the E. coli membranes.

Our resolution to this contradiction is that ThT does indeed work reasonably well with E. coli. The Pilizota group’s model for rotating flagellar motors assumes the membrane voltage is not varying due to excitability of the membrane voltage (otherwise a non-linear Hodgkin Huxley type model would be needed to quantify their results) i.e. E. coli cells are unexcitable. We show clearly in our study that ThT loading in E. coli is a function of irradiation with blue light and is a stress response of the excitable cells. This is in contradiction to the Pilizota group’s model. The Pilizota group’s model also requires the awkward fiction of why cells decide to unload and then reload ThT in regimes 2 and 3 of Author response figure 1 due to variable membrane partitioning of the ThT. Our simple explanation is that it is just due to the membrane voltage changing and no membrane permeability switch needs to be invoked. The Strahl group’s16 results with DiSc3 are also explained by a neglect of the excitable nature of E. coli cells that are reacting to blue light irradiation. Adding ionophores to the E. coli membranes makes the cells unexcitable, reduces their response to blue light and thus leads to simple loading of DiSc3 (the physiological control of K+ in the cells by voltage-gated ion channels has been short circuited by the addition of the ionophore).

Further evidence of our model that ThT functions as a voltage sensor with E. coli include:

1) The 3 regimes in Author response figure 1 from ThT correlate well with measurements of extracellular potassium ion concentration using TMRM i.e. all 3 regimes in Author response figure 1 are visible with this separate dye (figure 1d).

2) We are able to switch regime 3 in Author response figure 1, off and then on again by using knock downs of the potassium ion channel Kch in the membranes of the E. coli and then reinserting the gene back into the knock downs. This cannot be explained by the Pilizota model.

We conclude that ThT works reasonably well as a sensor of membrane voltage in E. coli and the previous contradictory studies15-16 are because they neglect the excitable nature of the membrane voltage of E. coli cells in response to the light used to make the ThT fluoresce.

Three further criticisms of the Mancini et al method15 for calibrating membrane voltages include:

1) E. coli cells have clutches that are not included in their models. Otherwise the rotation of the flagella would be entirely enslaved to the membrane voltage allowing the bacteria no freedom to modulate their speed of motility.

2) Ripping off the flagella may perturb the integrity of the cell membrane and lead to different loading of the ThT in the E. coli cells.

3) Most seriously, the method ignores the activity of many other ion channels (beyond H+) on the membrane voltage that are known to exist with E. coli cells e.g. Kch for K+ ions. The Pilizota groups uses a simple Nernstian battery model developed for mitochondria in the 1960s. It is not adequate to explain our results.

An additional criticism of the Winkel et al study17 from the Strahl group is that it indiscriminately switches between discussion of mitochondria and bacteria e.g. on page 8 ‘As a consequence the membrane potential is dominated by H+’. Mitochondria are slightly alkaline intracellular organelles with external ion concentrations in the cytoplasm that are carefully controlled by the eukaryotic cells. E. coli are not i.e. they have neutral internal pHs, with widely varying extracellular ionic concentrations and have reinforced outer membranes to resist osmotic shocks (in contrast mitochondria can easily swell in response to moderate changes in osmotic pressure).

A quick calculation of the equilibrium membrane voltage of E. coli can be easily done using the Nernst equation dependent on the extracellular ion concentrations defined by the growth media (the intracellular ion concentrations in E. coli are 0.2 M K+ and 10-7 M H+ i.e. there is a factor of a million fewer H+ ions). Thus in contradiction to the claims of the groups of Pilizota15 and Strahl17, H+ is a minority determinant to the membrane voltage of E. coli. The main determinant is K+. For a textbook version of this point the authors can refer to Chapter 4 of D. White, et al’s ‘The physiology and biochemistry of prokaryotes’, OUP, 2012, 4th edition.

Even in mitochondria the assumption that H+ dominates the membrane potential and the cells are unexcitable can be questioned e.g. people have observed pulsatile depolarization phenomena with mitochondria18-19. A large number of K+ channels are now known to occur in mitochondrial membranes (not to mention Ca2+ channels; mitochondria have extensive stores of Ca2+) and they are implicated in mitochondrial membrane potentials. In this respect the seminal Nobel prize winning research of Peter Mitchell (1961) on mitochondria needs to be amended20. Furthermore, the mitochondrial work is clearly inapplicable to bacteria (the proton motive force, PMF, will instead subtly depend on non-linear Hodgkin-Huxley equations for the excitable membrane potential, similar to those presented in the current article). A much more sophisticated framework has been developed to describe electrophysiology by the mathematical biology community to describe the activity of electrically excitable cells (e.g. with neurons, sensory cells and cardiac cells), beyond Mitchell’s use of the simple stationary equilibrium thermodynamics to define the Proton Motive Force via the electrochemical potential of a proton (the use of the word ‘force’ is unfortunate, since it is a potential). The tools developed in the field of mathematical electrophysiology8 should be more extensively applied to bacteria, fungi, mitochondria and chloroplasts if real progress is to be made.

Related to the previous point, we now cite articles from the Pilizota and Strahl groups in the main text (one from each group). Unfortunately, the space constraints of eLife mean we cannot make a more detailed discussion in the main article.

In terms of modelling the ion channels, the Hodgkin-Huxley type model proposes that the Kch ion channel can be modelled as a typical voltage-gated potassium ion channel i.e. with a 𝑛⁴ term in its conductivity. The literature agrees that Kch is a voltage-gated potassium ion channel based on its primary sequence³. The protein has the typical 6 transmembrane helix motif for a voltage-gated ion channel. The agent-based model assumes little about the structure of ion channels in E. coli, other than they release potassium in response to a threshold potassium concentration in their environment. The agent based model is thus robust to the exact molecular details chosen and predicts the anomalous transport of the potassium wavefronts reasonably well (the modelling was extended in a recent Physical Review E article(⁴). Such a description of reaction-anomalous diffusion phenomena has not to our knowledge been previously achieved in the literature⁵ and in general could be used to describe other signaling molecules.

1. Prindle, A.; Liu, J.; Asally, M.; Ly, S.; Garcia-Ojalvo, J.; Sudel, G. M., Ion channels enable electrical communication in bacterial communities. Nature 2015, 527, 59.

2. Blee, J. A.; Roberts, I. S.; Waigh, T. A., Membrane potentials, oxidative stress and the dispersal response of bacterial biofilms to 405 nm light. Physical Biology 2020, 17, 036001.

3. Milkman, R., An E. col_i homologue of eukaryotic potassium channel proteins. _PNAS 1994, 91, 3510-3514.

4. Martorelli, V.; Akabuogu, E. U.; Krasovec, R.; Roberts, I. S.; Waigh, T. A., Electrical signaling in three-dimensional bacterial biofilms using an agent-based fire-diffuse-fire model. Physical Review E 2024, 109, 054402.

5. Waigh, T. A.; Korabel, N., Heterogeneous anomalous transport in cellular and molecular biology. Reports on Progress in Physics 2023, 86, 126601.

6. Hodgkin, A. L.; Huxley, A. F., A quantitative description of membrane current and its application to conduction and excitation in nerve. Journal of Physiology 1952, 117, 500.

7. Dawson, S. P.; Keizer, J.; Pearson, J. E., Fire-diffuse-fire model of dynamics of intracellular calcium waves. PNAS 1999, 96, 606.

8. Keener, J.; Sneyd, J., Mathematical Physiology. Springer: 2009.

9. Coombes, S., The effect of ion pumps on the speed of travelling waves in the fire-diffuse-fire model of Ca2+ release. Bulletin of Mathematical Biology 2001, 63, 1.

10. Blee, J. A.; Roberts, I. S.; Waigh, T. A., Spatial propagation of electrical signals in circular biofilms. Physical Review E 2019, 100, 052401.

11. Gorochowski, T. E.; Matyjaszkiewicz, A.; Todd, T.; Oak, N.; Kowalska, K., BSim: an agent-based tool for modelling bacterial populations in systems and synthetic biology. PloS One 2012, 7, 1.

12. Pena, A.; Sanchez, N. S.; Padilla-Garfias, F.; Ramiro-Cortes, Y.; Araiza-Villaneuva, M.; Calahorra, M., The use of thioflavin T for the estimation and measurement of the plasma membrane electric potential difference in different yeast strains. Journal of Fungi 2023, 9 (9), 948.

13. Xue, C.; Lin, T. Y.; Chang, D.; Guo, Z., Thioflavin T as an amyloid dye: fibril quantification, optimal concentration and effect on aggregation. Royal Society Open Science 2017, 4, 160696.

14. Meisl, G.; Kirkegaard, J. B.; Arosio, P.; Michaels, T. C. T.; Vendruscolo, M.; Dobson, C. M.; Linse, S.; Knowles, T. P. J., Molecular mechanisms of protein aggregation from global fitting of kinetic models. Nature Protocols 2016, 11 (2), 252-272.

15. Mancini, L.; Tian, T.; Guillaume, T.; Pu, Y.; Li, Y.; Lo, C. J.; Bai, F.; Pilizota, T., A general workflow for characterization of Nernstian dyes and their effects on bacterial physiology. Biophysical Journal 2020, 118 (1), 4-14.

16. Buttress, J. A.; Halte, M.; Winkel, J. D. t.; Erhardt, M.; Popp, P. F.; Strahl, H., A guide for membrane potential measurements in Gram-negative bacteria using voltage-sensitive dyes. Microbiology 2022, 168, 001227.

17. Derk te Winkel, J.; Gray, D. A.; Seistrup, K. H.; Hamoen, L. W.; Strahl, H., Analysis of antimicrobial-triggered membrane depolarization using voltage sensitive dyes. Frontiers in Cell and Developmental Biology 2016, 4, 29.

18. Schawarzlander, M.; Logan, D. C.; Johnston, I. G.; Jones, N. S.; Meyer, A. J.; Fricker, M. D.; Sweetlove, L. J., Pulsing of membrane potential in individual mitochondria. The Plant Cell 2012, 24, 1188-1201.

19. Huser, J.; Blatter, L. A., Fluctuations in mitochondrial membrane potential caused by repetitive gating of the permeability transition pore. Biochemistry Journal 1999, 343, 311-317.

20. Mitchell, P., Coupling of phosphorylation to electron and hydrogen transfer by a chemi-osmotic type of mechanism. Nature 1961, 191 (4784), 144-148.

21. Baba, T.; Ara, M.; Hasegawa, Y.; Takai, Y.; Okumura, Y.; Baba, M.; Datsenko, K. A.; Tomita, M.; Wanner, B. L.; Mori, H., Construction of Escherichia Coli K-12 in-frame, single-gene knockout mutants: the Keio collection. Molecular Systems Biology 2006, 2, 1.

22. Schinedlin, J.; al, e., Fiji: an open-source platform for biological-image analysis. Nature Methods 2012, 9, 676.

23. Hartmann, R.; al, e., Quantitative image analysis of microbial communities with BiofilmQ. Nature Microbiology 2021, 6 (2), 151.

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

Critical synopsis of the articles cited by referee 2:

(1) ‘Generalized workflow for characterization of Nernstian dyes and their effects on bacterial physiology’, L.Mancini et al, Biophysical Journal, 2020, 118, 1, 4-14.

This is the central article used by referee 2 to argue that there are issues with the calibration of ThT for the measurement of membrane potentials. The authors use a simple Nernstian battery (SNB) model and unfortunately it is wrong when voltage-gated ion channels occur. Huge oscillations occur in the membrane potentials of E. coli that cannot be described by the SNB model. Instead a Hodgkin Huxley model is needed, as shown in our eLife manuscript and multiple other studies (see above). Arrhenius kinetics are assumed in the SNB model for pumping with no real evidence and the generalized workflow involves ripping the flagella off the bacteria! The authors construct an elaborate ‘work flow’ to insure their ThT results can be interpreted using their erroneous SNB model over a limited range of parameters.

(2) ‘Non-equivalence of membrane voltage and ion-gradient as driving forces for the bacterial flagellar motor at low load’, C.J.Lo, et al, Biophysical Journal, 2007, 93, 1, 294.

An odd de novo chimeric species is developed using an E. coli  chassis which uses Na+ instead of H+ for the motility of its flagellar motor. It is not clear the relevance to wild type E. coli, due to the massive physiological perturbations involved. A SNB model is using to fit the data over a very limited parameter range with all the concomitant errors.

(3) Single-cell bacterial electrophysiology reveals mechanisms of stress-induced damage’, E.Krasnopeeva, et al, Biophysical Journal, 2019, 116, 2390.

The abstract says ‘PMF defines the physiological state of the cell’. This statement is hyperbolic. An extremely wide range of molecules contribute to the physiological state of a cell. PMF does not even define the electrophysiology of the cell e.g. via the membrane potential. There are 0.2 M of K+ compared with 0.0000001 M of H+ in E. coli, so K+ is arguably a million times more important for the membrane potential than H+ and thus the electrophysiology!

Equation (1) in the manuscript assumes no other ions are exchanged during the experiments other than H+. This is a very bad approximation when voltage-gated potassium ion channels move the majority ion (K+) around!

In our model Figure 4A is better explained by depolarisation due to K+ channels closing than direct irreversible photodamage. Why does the THT fluorescence increase again for the second hyperpolarization event if the THT is supposed to be damaged? It does not make sense.

(4) ‘The proton motive force determines E. coli robustness to extracellular pH’, G.Terradot et al, 2024, preprint.

This article expounds the SNB model once more. It still ignores the voltage-gated ion channels. Furthermore, it ignores the effect of the dominant ion in E. coli, K+. The manuscript is incorrect as a result and I would not recommend publication.

In general, an important problem is being researched i.e. how the membrane potential of E. coli is related to motility, but there are serious flaws in the SNB approach and the experimental methodology appears tenuous.

Answers to specific questions raised by the referees

Reviewer #1 (Public Review):

Summary:

Cell-to-cell communication is essential for higher functions in bacterial biofilms. Electrical signals have proven effective in transmitting signals across biofilms. These signals are then used to coordinate cellular metabolisms or to increase antibiotic tolerance. Here, the authors have reported for the first time coordinated oscillation of membrane potential in E. coli biofilms that may have a functional role in photoprotection.

Strengths:

- The authors report original data.

- For the first time, they showed that coordinated oscillations in membrane potential occur in E. Coli biofilms.

- The authors revealed a complex two-phase dynamic involving distinct molecular response mechanisms.

- The authors developed two rigorous models inspired by 1) Hodgkin-Huxley model for the temporal dynamics of membrane potential and 2) Fire-Diffuse-Fire model for the propagation of the electric signal.

- Since its discovery by comparative genomics, the Kch ion channel has not been associated with any specific phenotype in E. coli. Here, the authors proposed a functional role for the putative K+ Kch channel : enhancing survival under photo-toxic conditions.